I find this statement to be incredibly useful in understanding problems in our perception and approach to solving them. I think most of us were raised with one-dimensional notions of good and bad, right and wrong. We conflate the problems with the concept of something 'bad' which therefore suggests that there is a 'good' or a right to be made. If we apply the reasoning presented in this question, problems will never actually be solved in the greater context. A situation or instance that may present as a problem to one subject or subjects at a single point in time may not be problematic at all in a different context. Having such a fixed and rigid perspective of problems and their solutions can limit our ability to innovate and develop because such a perspective does not acknowledge or consider the alternative contexts that a 'problem' might exist in.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

This study asks whether the phenomenon of crossmodal temporal recalibration, i.e. the adjustment of time perception by consistent temporal mismatches across the senses, can be explained by the concept of multisensory causal inference. In particular, they ask whether the explanation offered by causal inference better explains temporal recalibration better than a model assuming that crossmodal stimuli are always integrated, regardless of how discrepant they are.

The study is motivated by previous work in the spatial domain, where it has been shown consistently across studies that the use of crossmodal spatial information is explained by the concept of multisensory causal inference. It is also motivated by the observation that the behavioral data showcasing temporal recalibration feature nonlinearities that, by their nature, cannot be explained by a fixed integration model (sometimes also called mandatory fusion).

To probe this the authors implemented a sophisticated experiment that probed temporal recalibration in several sessions. They then fit the data using the two classes of candidate models and rely on model criteria to provide evidence for their conclusion. The study is sophisticated, conceptually and technically state-of-the-art, and theoretically grounded. The data clearly support the authors’ conclusions.

I find the conceptual advance somewhat limited. First, by design, the fixed integration model cannot explain data with a nonlinear dependency on multisensory discrepancy, as already explained in many studies on spatial multisensory perception. Hence, it is not surprising that the causal inference model better fits the data.

We have addressed this comment by including an asynchrony-contingent model, which is capable of predicting the nonlinearity of recalibration effects by employing a heuristic approximation of the causal-inference process (Fig. 3). We also updated the previous competitor model with a more reasonable asynchrony-correction model as the baseline of model comparison, which assumes recalibration aims to restore synchrony whenever the sensory measurement of SOA indicates an asynchrony. The causal-inference model outperformed both models, as indicated by model evidence (Fig. 4A). Furthermore, model predictions show that the causal-inference model more accurately captures recalibration at large SOAs at both the group (Fig. 4B) and the individual levels (Fig. S4).

Second, and again similar to studies on spatial paradigms, the causal inference model fails to predict the behavioral data for large discrepancies. The model predictions in Figure 5 show the (expected) vanishing recalibration for large delta, while the behavioral data don’t decay to zero. Either the range of tested SOAs is too small to show that both the model and data converge to the same vanishing effect at large SOAs, or the model's formula is not the best for explaining the data. Again, the studies using spatial paradigms have the same problem, but in my view, this poses the most interesting question here.

We included an additional simulation (Fig. 5B) to show that the causal-inference model can predict non-zero recalibration for long adapter SOAs, especially in observers with a high common-cause prior and low sensory precision. This ability to predict a non-zero recalibration effect even at large SOA, such as 0.7 s, is one key feature of the causal-inference model that distinguishes it from the asynchrony-contingent model.

In my view there is nothing generally wrong with the study, it does extend the 'known' to another type of paradigm. However, it covers little new ground on the conceptual side.

On that note, the small sample size of n=10 is likely not an issue, but still, it is on the very low end for this type of study.

This study used a within-subject design, which included 3 phases each repeated in 9 sessions, totaling 13.5 hours per participant. This extensive data collection allows us to better constrain the model for each participant. Our conclusions are based on the different models’ ability to fit individual data.

Reviewer #2 (Public Review):

Summary:

Li et al.’s goal is to understand the mechanisms of audiovisual temporal recalibration. This is an interesting challenge that the brain readily solves in order to compensate for real-world latency differences in the time of arrival of audio/visual signals. To do this they perform a 3-phase recalibration experiment on 9 observers that involves a temporal order judgment (TOJ) pretest and posttest (in which observers are required to judge whether an auditory and visual stimulus were coincident, auditory leading or visual leading) and a conditioning phase in which participants are exposed to a sequence of AV stimuli with a particular temporal disparity. Participants are required to monitor both streams of information for infrequent oddballs, before being tested again in the TOJ, although this time there are 3 conditioning trials for every 1 TOJ trial. Like many previous studies, they demonstrate that conditioning stimuli shift the point of subjective simultaneity (pss) in the direction of the exposure sequence.

These shifts are modest - maxing out at around -50 ms for auditory leading sequences and slightly less than that for visual leading sequences. Similar effects are observed even for the longest offsets where it seems unlikely listeners would perceive the stimuli as synchronous (and therefore under a causal inference model you might intuitively expect no recalibration, and indeed simulations in Figure 5 seem to predict exactly that which isn't what most of their human observers did). Overall I think their data contribute evidence that a causal inference step is likely included within the process of recalibration.

Strengths:

The manuscript performs comprehensive testing over 9 days and 100s of trials and accompanies this with mathematical models to explain the data. The paper is reasonably clearly written and the data appear to support the conclusions.

Weaknesses:

While I believe the data contribute evidence that a causal inference step is likely included within the process of recalibration, this to my mind is not a mechanism but might be seen more as a logical checkpoint to determine whether whatever underlying neuronal mechanism actually instantiates the recalibration should be triggered.

We have addressed this comment by replacing the fixed-update model with an asynchrony-correction model, which assumes that the system first evaluates whether the measurement of SOA is asynchronous, thus indicating a need for recalibration (Fig. 3). If it does, it shifts the audiovisual bias by a proportion of the measured SOA. We additionally included an asynchrony-contingent model, which is capable of replicating the nonlinearity of recalibration effects by a heuristic approximation of the causal-inference process.

Model comparisons indicate that the causal-inference model of temporal recalibration outperforms both alternative models (Fig. 4A). Furthermore, the model predictions demonstrate that the causal-inference model more accurately captures recalibration at large SOAs at both the group level (Fig. 4B) and individual level (Fig. S4).

The authors’ causal inference model strongly predicts that there should be no recalibration for stimuli at 0.7 ms offset, yet only 3/9 participants appear to show this effect. They note that a significant difference in their design and that of others is the inclusion of longer lags, which are unlikely to originate from the same source, but don’t offer any explanation for this key difference between their data and the predictions of a causal inference model.

We added further simulations to show that the causal-inference model can predict non-zero recalibration also for longer adapter SOAs, especially in observers with a large common-cause prior (Fig. 5A) and low sensory precision (Fig. 5B). This ability to predict a non-zero recalibration effect even at longer adapter SOAs, such as 0.7 s, is a key feature of the causal-inference model that distinguishes it from the asynchrony-contingent model.

I’m also not completely convinced that the causal inference model isn’t ‘best’ simply because it has sufficient free parameters to capture the noise in the data. The tested models do not (I think) have equivalent complexity - the causal inference model fits best, but has more parameters with which to fit the data. Moreover, while it fits ‘best’, is it a good model? Figure S6 is useful in this regard but is not completely clear - are the red dots the actual data or the causal inference prediction? This suggests that it does fit the data very well, but is this based on predicting held-out data, or is it just that by having more parameters it can better capture the noise? Similarly, S7 is a potentially useful figure but it's not clear what is data and what are model predictions (what are the differences between each row for each participant; are they two different models or pre-test post-test or data and model prediction?!).

I'm not an expert on the implementation of such models but my reading of the supplemental methods is that the model is fit using all the data rather than fit and tested on held-out data. This seems problematic.

We recognize the risk of overfitting with the causal-inference model. We now rely on Bayesian model comparisons, which use model evidence for model selection. This method automatically incorporates a penalty for model complexity through the marginalization over the parameter space (MacKay, 2003).

Our design is not suitable for cross-validation because the model-fitting process is computationally intensive and time-consuming. Each fit of the causal-inference model takes approximately 30 hours, and multiple fits with different initial starting points are required to rule out that the parameter estimates correspond to local minima.

I would have liked to have seen more individual participant data (which is currently in the supplemental materials, albeit in a not very clear manner as discussed above).

We have revised Supplementary Figures S4-S6 to show additional model predictions of the recalibration effect for individual participants, and participants’ temporal-order judgments are now shown in Supplement Figure S7. These figures confirm the better performance of the causal-inference model.

The way that S3 is described in the text (line 141) makes it sound like everyone was in the same direction, however, it is clear that 2 /9 listeners show the opposite pattern, and 2 have confidence intervals close to zero (albeit on the -ve side).

We have revised the text to clarify that the asymmetry occurs in both directions and is idiosyncratic (lines 168-171). We summarized the distribution of the individual asymmetries of the recalibration effect across visual-leading and auditory-leading adapter SOAs in Supplementary Figure S2.

Reviewer #3 (Public Review):

Summary:

Li et al. describe an audiovisual temporal recalibration experiment in which participants perform baseline sessions of ternary order judgments about audiovisual stimulus pairs with various stimulus-onset asynchronies (SOAs). These are followed by adaptation at several adapting SOAs (each on a different day), followed by post-adaptation sessions to assess changes in psychometric functions. The key novelty is the formal specification and application/fit of a causal-inference model for the perception of relative timing, providing simulated predictions for the complete set of psychometric functions both pre and post-adaptation.

Strengths:

(1) Formal models are preferable to vague theoretical statements about a process, and prior to this work, certain accounts of temporal recalibration (specifically those that do not rely on a population code) had only qualitative theoretical statements to explain how/why the magnitude of recalibration changes non-linearly with the stimulus-onset asynchrony of the adapter.

(2) The experiment is appropriate, the methods are well described, and the average model prediction is a fairly good match to the average data (Figure 4). Conclusions may be overstated slightly, but seem to be essentially supported by the data and modelling.

(3) The work should be impactful. There seems a good chance that this will become the go-to modelling framework for those exploring non-population-code accounts of temporal recalibration (or comparing them with population-code accounts).

(4) A key issue for the generality of the model, specifically in terms of recalibration asymmetries reported by other authors that are inconsistent with those reported here, is properly acknowledged in the discussion.

Weaknesses:

(1) The evidence for the model comes in two forms. First, two trends in the data (non-linearity and asymmetry) are illustrated, and the model is shown to be capable of delivering patterns like these. Second, the model is compared, via AIC, to three other models. However, the main comparison models are clearly not going to fit the data very well, so the fact that the new model fits better does not seem all that compelling. I would suggest that the authors consider a comparison with the atheoretical model they use to first illustrate the data (in Figure 2). This model fits all sessions but with complete freedom to move the bias around (whereas the new model constrains the way bias changes via a principled account). The atheoretical model will obviously fit better, but will have many more free parameters, so a comparison via AIC/BIC or similar should be informative

In the revised manuscript, we switched from AIC to Bayesian model selection, which approximates and compares model evidence. This method incorporates a strong penalty for model complexity through marginalization over the parameter space (MacKay, 2003).

We have addressed this comment by updating the former competitor model into a more reasonable version that induces recalibration only for some measured SOAs and by including another (asynchrony-contingent) model that is capable of predicting the nonlinearity and asymmetry of recalibration (Fig. 3) while heuristically approximating the causal inference computations. The causal-inference model outperformed the asynchrony-contingent model, as indicated by model evidence (Fig. 4A). Furthermore, model predictions show that the causal-inference model more accurately captures recalibration at large SOAs at both the group (Fig. 4B) and the individual level (Fig. S4).

(2) It does not appear that some key comparisons have been subjected to appropriate inferential statistical tests. Specifically, lines 196-207 - presumably this is the mean (and SD or SE) change in AIC between models across the group of 9 observers. So are these differences actually significant, for example via t-test?

We statistically compared the models using Bayes factors (Fig. 4A). The model evidence for each model was approximated using Variational Bayesian Monte Carlo. Bayes factors provided strong evidence in support of the causal-inference model relative to the other models.

(3) The manuscript tends to gloss over the population-code account of temporal recalibration, which can already provide a quantitative account of how the magnitude of recalibration varies with adapter SOA. This could be better acknowledged, and the features a population code may struggle with (asymmetry?) are considered.

We simulated a population-code model to examine its prediction of the recalibration effect for different adapter SOAs (lines 380–388, Supplement Section 8). The population-code model can predict the nonlinearity of recalibration, i.e., a decreasing recalibration effect as the adapter SOA increases. However, to capture the asymmetry of recalibration effects across auditory-leading and visual-leading adapter stimuli, we would need to assume that the auditory-leading and visual-leading SOAs are represented by neural populations with unequal tuning curves.

(4) The engagement with relevant past literature seems a little thin. Firstly, papers that have applied causal inference modeling to judgments of relative timing are overlooked (see references below). There should be greater clarity regarding how the modelling here builds on or differs from these previous papers (most obviously in terms of additionally modelling the recalibration process, but other details may vary too). Secondly, there is no discussion of previous findings like that in Fujisaki et al.’s seminal work on recalibration, where the spatial overlap of the audio and visual events didn’t seem to matter (although admittedly this was an N = 2 control experiment). This kind of finding would seem relevant to a causal inference account.

References:

Magnotti JF, Ma WJ and Beauchamp MS (2013) Causal inference of asynchronous audiovisual speech. Front. Psychol. 4:798. doi: 10.3389/fpsyg.2013.00798

Sato, Y. (2021). Comparing Bayesian models for simultaneity judgement with different causal assumptions. J. Math. Psychol., 102, 102521.

We have revised the Introduction and Discussion to better situate our study within the existing literature. Specifically, we have incorporated the suggested references (lines 66–69) and provided clearer distinctions on how our modeling approach builds on or differs from previous work on causal-inference models, particularly in terms of modeling the recalibration process (lines 75–79). Additionally, we have discussed findings that might contradict the assumptions of the causal-inference model (lines 405–424).

(5) As a minor point, the model relies on simulation, which may limit its take-up/application by others in the field.

Upon acceptance, we will publicly share the code for all models (simulation and parameter fitting) to enable researchers to adapt and apply these models to their own data.

(6) There is little in the way of reassurance regarding the model’s identifiability and recoverability. The authors might for example consider some parameter recovery simulations or similar.

We conducted a model recovery for each of the six models described in the main text and confirmed that the asynchrony-contingent and causal-inference models are identifiable (Supplement Section 11). Simulations of the asynchrony-correction model were sometimes best fit by causal-inference models, because the latter behaves similarly when the prior of a common cause is set to one.

We also conducted a parameter recovery for the winning model, the causal-inference model with modality-specific precision (Supplement Section 13).

Key parameters, including audiovisual bias  , amount of auditory latency noise  , amount of visual latency noise  , criterion, lapse rate  showed satisfactory recovery performance. The less accurate recovery of  is likely due to a tradeoff with learning rate  .

(7) I don't recall any statements about open science and the availability of code and data.

Upon acceptance of the manuscript, all code (simulation and parameter fitting) and data will be made available on OSF and publicly available.

Recommendations for the authors:

Reviewing Editor (Recommendations For The Authors):

In addition to the comments below, we would like to offer the following summary based on the discussion between reviewers:

The major shortcoming of the work is that there should ideally be a bit more evidence to support the model, over and above a demonstration that it captures important trends and beats an account that was already known to be wrong. We suggest you:

(1) Revise the figure legends (Figure 5 and Figure 6E).

We revised all figures and figure legends.

(2) Additionally report model differences in terms of BIC (which will favour the preferred model less under the current analysis);

We now base the model comparison on Bayesian model selection, which approximates and compares model evidence. This method incorporates a strong penalty for model complexity through marginalization over the parameter space (MacKay, 2003).

(3) Move to instead fitting the models multiple times in order to get leave-one-out estimates of best-fitting loglikelihood for each left-out data point (and then sum those for the comparison metric).

Unfortunately, our design is not suitable for cross-validation methods because the model-fitting process is computationally intensive and time-consuming. Each fit of the causal-inference model takes approximately 30 hours, and multiple fits with different initial starting points are required to rule out local minima.

(4) Offering a comparison with a more convincing model (for example an atheoretical fit with free parameters for all adapters, e.g. as suggested by Reviewer 3.

We updated the previous competitor model and included an asynchrony-contingent model, which is capable of predicting the nonlinearity of recalibration (Fig. 3). The causal-inference model still outperformed the asynchrony-contingent model (Fig. 4A). Furthermore, model predictions show that only the causal-inference model captures non-zero recalibration effects for long adapter SOAs at both the group level (Fig. 4B) and individual level (Figure S4).

Reviewer #1 (Recommendations For The Authors):

A larger sample size would be better.

This study used a within-subject design, which included 9 sessions, totaling 13.5 hours per participant. This extensive data collection allows us to better constrain the model for each participant. Our conclusions are based on the different models’ ability to fit individual data rather than on group statistics.

It would be good to better put the study in the context of spatial ventriloquism, where similar model comparisons have been done over the last ten years and there is a large body of work to connect to.

We now discuss our model in relation to models of cross-modal spatial recalibration in the Introduction (lines 70–78) and Discussion (lines 324–330).

Reviewer #2 (Recommendations For The Authors):

Previous authors (e.g. Yarrow et al.,) have described latency shift and criterion change models as providing a good fit of experimental data. Did the authors attempt a criterion shift model in addition to a shift model?

We have considered criterion-shift variants of our atheoretical recalibration models in Supplement Section 1. To summarize the results, we varied two model assumptions: 1) the use of either a Gaussian or an exponential measurement distribution, and 2) recalibration being implemented either as a shift of bias or a criterion. We fit each model variant separately to the ternary TOJ responses of all sessions. Bayesian model comparisons indicated that the bias-shift model with exponential measurement distributions best captured the data of most participants.

Figure 4B - I'm not convinced that the modality-independent uncertainty is anything but a straw man. Models not allowed to be asymmetric do not show asymmetry? (the asymmetry index is irrelevant in the fixed update model as I understand it so it is not surprising the model is identical?).

We included the assumption that temporal uncertainty might be modality-independent for several reasons. First, there is evidence suggesting that a central mechanism governs the precision of temporal-order judgments (Hirsh & Sherrick, 1961), indicating that precision is primarily limited by a central mechanism rather than the sensory channels themselves. Second, from a modeling perspective, it was necessary to test whether an audio-visual temporal bias alone, i.e., assuming modality-independent uncertainty, could introduce asymmetry across adapter SOAs. Additionally, most previous studies implicitly assumed symmetric likelihoods, i.e., modality-independent latency noise, by fitting cumulative Gaussians to the psychometric curves derived from 2AFC-TOJ tasks (Di Luca et al., 2009; Fujisaki et al., 2004; Harrar & Harris, 2005; Keetels & Vroomen, 2007; Navarra et al., 2005; Tanaka et al., 2011; Vatakis et al., 2007, 2008; Vroomen et al., 2004).

Why does a zero SOA adapter shift the pss towards auditory leading? Is this a consequence of the previous day’s conditioning - it’s not clear from the methods whether all listeners had the same SOA conditioning sequence across days.

The auditory-leading recalibration effect for an adapter SOA of zero has been consistently reported in previous studies (e.g., Fujisaki et al., 2004; Vroomen et al., 2004). This effect symbolizes the asymmetry in recalibration. This asymmetry can be explained by differences across modalities in the noisiness of the latencies (Figure 5C) in combination with audiovisual temporal bias (Figure S8).

We added details about the order of testing to the Methods section (lines 456–457).

Reviewer #3 (Recommendations For The Authors):

Abstract

“Our results indicate that human observers employ causal-inference-based percepts to recalibrate cross-modal temporal perception” Your results indicate this is plausible. However, this statement (basically repeated at the end of the intro and again in the discussion) is - in my opinion - too strong.

We have revised the statement as suggested.

Intro and later

Within the wider literature on relative timing perception, the temporal order judgement (TOJ) task refers to a task with just two response options. Tasks with three response options, as employed here, are typically referred to as ternary judgments. I would suggest language consistent with the existing literature (or if not, the contrast to standard usage could be clarified).

Ref: Ulrich, R. (1987). Threshold models of temporal-order judgments evaluated by a ternary response task. Percept. Psychophys., 42, 224-239.

We revised the term for the task as suggested throughout the manuscript.

Results, 2.2.2

“However, temporal precision might not be due to the variability of arrival latency.” Indeed, although there is some recent evidence that it might be.

Ref: Yarrow, K., Kohl, C, Segasby, T., Kaur Bansal, R., Rowe, P., & Arnold, D.H. Neural-latency noise places limits on human sensitivity to the timing of events. Cognition, 222, 105012 (2022).

We included the reference as suggested (lines 245–248).

Methods, 4.3.

Should there be some information here about the order of adaptation sessions (e.g. random for each observer)?

We added details about the order of testing to the Methods section (lines 456–457).

Supplemental material section 1.

Here, you test whether the changes resulting from recalibration look more like a shift of the entire psychometric function or an expansion of the psychometric function on one side (most straightforwardly compatible with a change of one decision criterion). Fine, but the way you have done this is odd, because you have introduced a further difference in the models (Gaussian vs. exponential latency noise) so that you cannot actually conclude that the trend towards a win for the bias-shift model is simply down to the bias vs. criterion difference. It could just as easily be down to the different shapes of psychometric functions that the two models can predict (with the exponential noise model permitting asymmetry in slopes). There seems to be no reason that this comparison cannot be made entirely within the exponential noise framework (by a very simple reparameterization that focuses on the two boundaries rather than the midpoint and extent of the decision window). Then, you would be focusing entirely on the question of interest. It would also equate model parameters, removing any reliance on asymptotic assumptions being met for AIC.

We revised our exploration of atheoretical recalibration models. To summarize the results, we varied two model assumptions: 1) the use of either a Gaussian or an exponential measurement distribution, and 2) recalibration being implemented either as a shift of the cross-modal temporal bias or as a shift of the criterion. We fit each model separately to the ternary TOJ responses of all sessions. Bayesian model comparisons indicated that the bias-shift model with exponential measurement distributions best described the data of most participants.

References

Di Luca, M., Machulla, T.-K., & Ernst, M. O. (2009). Recalibration of multisensory simultaneity:

cross-modal transfer coincides with a change in perceptual latency. Journal of Vision, 9(12), Article 7.

Fujisaki, W., Shimojo, S., Kashino, M., & Nishida, S. ’ya. (2004). Recalibration of audiovisual simultaneity. Nature Neuroscience, 7(7), 773–778.

Harrar, V., & Harris, L. R. (2005). Simultaneity constancy: detecting events with touch and vision. Experimental Brain Research. Experimentelle Hirnforschung. Experimentation Cerebrale, 166(3-4), 465–473.

Hirsh, I. J., & Sherrick, C. E., Jr. (1961). Perceived order in different sense modalities. Journal of Experimental Psychology, 62(5), 423–432.

Keetels, M., & Vroomen, J. (2007). No effect of auditory-visual spatial disparity on temporal recalibration. Experimental Brain Research. Experimentelle Hirnforschung. Experimentation Cerebrale, 182(4), 559–565.

MacKay, D. J. (2003). Information theory, inference and learning algorithms.https://citeseerx.ist.psu.edu/document?repid=rep1&type=pdf&doi=201b835c3f3a3626ca07b e68cc28cf7d286bf8d5

Navarra, J., Vatakis, A., Zampini, M., Soto-Faraco, S., Humphreys, W., & Spence, C. (2005). Exposure to asynchronous audiovisual speech extends the temporal window for audiovisual integration. Brain Research. Cognitive Brain Research, 25(2), 499–507.

Tanaka, A., Asakawa, K., & Imai, H. (2011). The change in perceptual synchrony between auditory and visual speech after exposure to asynchronous speech. Neuroreport, 22(14), 684–688.

Vatakis, A., Navarra, J., Soto-Faraco, S., & Spence, C. (2007). Temporal recalibration during asynchronous audiovisual speech perception. Experimental Brain Research. Experimentelle Hirnforschung. Experimentation Cerebrale, 181(1), 173–181.

Vatakis, A., Navarra, J., Soto-Faraco, S., & Spence, C. (2008). Audiovisual temporal adaptation of speech: temporal order versus simultaneity judgments. Experimental Brain Research. Experimentelle Hirnforschung. Experimentation Cerebrale, 185(3), 521–529.

Vroomen, J., Keetels, M., de Gelder, B., & Bertelson, P. (2004). Recalibration of temporal order perception by exposure to audio-visual asynchrony. Brain Research. Cognitive Brain Research, 22(1), 32–35.

Author response:

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

Reviewer 1 (Public Review):

Summary:

In this manuscript by Bimbard et al., a new method to perform stable recordings over long periods of time with neuropixels, as well as the technical details on how the electrodes can be explanted for follow-up reuse, is provided. I think the description of all parts of the method is very clear, and the validation analyses (n of units per day over time, RMS over recording days...) are very convincing. I however missed a stronger emphasis on why this could provide a big impact on the ephys community, by enabling new analyses, new behavior correlation studies, or neurophysiological mechanisms across temporal scales.

Strengths:

Open source method. Validation across laboratories. Across species (mice and rats) demonstration of its use and in different behavioral conditions (head-fixed and freely moving).

Weaknesses:

Weak emphasis on what can be enabled with this new method that didn't exist before.

We thank the reviewer for highlighting the limited discussion around scientific impact. Our implant has several advantages which combine to make it much more accessible than previous solutions. This enables a variety of recording configurations that would not have been possible with previous designs, facilitating recordings from a wider range of brain regions, animals, and experimental setups. In short, there are three key advances which we now emphasise in the manuscript:

Adaptability: The CAD files can be readily adapted to a wide range of configurations (implantation depth, angle, position of headstage, etc.). Labs have already modified the design for their needs, and re-shared with the community (Discussion, Para 5).

Weight: Because of the lightweight design, experimenters can i) perform complex and demanding freely moving tasks as we exemplify in the manuscript, and ii) implant female and water restricted mice while respecting animal welfare weight limitations (Flexible design, Para 1).

Cost: At ~$10, our implant is significantly cheaper than published alternatives, which makes it affordable to more labs and means that testing modifications is cost-effective (Discussion, Para 4).

Reviewer 1 (Recommendations For The Authors):

- Differences between mice and rats seem very significant. Although this is probably not surprising, I suggest that the authors comment on this to make it clear to anyone trying to use in different species that are not quantified in the main figures.

The reviewer is correct—there are qualitative differences between mice and rats, particularly with respect to the unit median amplitude. We have added a comment in the discussion to highlight these inter-species variations (Discussion, Para 7)

- Another comment that would be useful to have would be how to tackle the problem of tracking the same neuron across days. Even if currently impossible, it could be useful to provide discussion along those lines as to where future improvements (either in hardware or software) can be made.

We thank the reviewer for highlighting this. Figure. 5 does show data from tracking the same neuron across days (and even months). We have modified the language to make this clear.

Reviewer 2 (Public Review):  

Summary:

This work by Bimbard et al., introduces a new implant for Neuropixels probes. While Neuropixels probes have critically improved and extended our ability to record the activity of a large number of neurons with high temporal resolution, the use of these expensive devices in chronic experiments has so far been hampered by the difficulty of safely implanting them and, importantly, to explant and reuse them after conclusion of the experiment. The authors present a newly designed two-part implant, consisting of a docking and a payload module, that allows for secure implantation and straightforward recovery of the probes. The implant is lightweight, making it amenable for use in mice and rats, and customizable. The authors provide schematics and files for printing of the implants, which can be easily modified and adapted to custom experiments by researchers with little to no design experience. Importantly, the authors demonstrate the successful use of this implant across multiple use cases, in head-fixed and freely moving experiments, in mice and rats, with different versions of Neuropixels probes, and across 8 different labs. Taken together, the presented implants promise to make chronic Neuropixel recordings and long-term studies of neuronal activity significantly easier and attainable for both current and future Neuropixels users.

Strengths:

The implants have been successfully tested across 8 different laboratories, in mice and rats, in headfixed and freely moving conditions, and have been adapted in multiple ways for a number of distinct experiments.

Implants are easily customizable and the authors provide a straightforward approach for customization across multiple design dimensions even for researchers not experienced in design.

The authors provide clear and straightforward descriptions of the construction, implantation, and explant of the described implants.

The split of the implant into a docking and payload module makes reuse even in different experiments (using different docking modules) easy.

The authors demonstrate that implants can be re-used multiple times and still allow for high-quality recordings.

The authors show that the chronic implantations allow for the tracking of individual neurons across days and weeks (using additional software tracking solutions), which is critical for a large number of experiments requiring the description of neuronal activity, e.g. throughout learning processes.

The authors show that implanted animals can even perform complex behavioral tasks, with no apparent reduction in their performance.

Weaknesses:

While implanted animals can still perform complex behavioral tasks, the authors describe that the implants may reduce the animals' mobility, as measured by prolonged reaction times. However, the presented data does not allow us to judge whether this effect is specifically due to the presented implant or whether any implant or just tethering of the animals per se would have the same effects.

The reviewer is correct: some of the differences in mouse reaction time could be due to the tether rather than the implant. As these experiments were also performed in water-restricted female mice with the heavier Neuropixels 1.0 implant, our data represent the maximal impact of the implant, and we have highlighted this point in the revision (Freely behaving animals, Para 2).  

While the authors make certain comparisons to other, previously published approaches for chronic implantation and re-use of Neuropixels probes, it is hard to make conclusive comparisons and judge the advantages of the current implant. For example, while the authors emphasize that the lower weight of their implant allows them to perform recordings in mice (and is surely advantageous), the previously described, heavier implants they mention (Steinmetz et al., 2021; van Daal et al., 2021), have also been used in mice. Whether the weight difference makes a difference in practice therefore remains somewhat unclear.

The reviewer is correct: without a direct comparison, we cannot be certain that our smaller, lighter implant improves behavioural results (although this is supported by the literature, e.g. Newman et al, 2023). However, the reduced weight of our implant is critical for several laboratories represented in this manuscript due to animal welfare requirements. Indeed, in van Daal et al the authors “recommend a [mouse] weight of >25 g for implanting Neuropixels 1.0 probes.” This limit precludes using (the vast majority of) female mice, or water-restricted animals. Conversely, our implant can be routinely used with lighter, water-restricted male and female mice. We emphasised this point in the revision (Discussion, Para 2).

The non-permanent integration of the headstages into the implant, while allowing for the use of the same headstage for multiple animals in parallel, requires repeated connections and does not provide strong protection for the implant. This may especially be an issue for the use in rats, requiring additional protective components as in the presented rat experiments.

We apologise for not clarifying the various headstage holder options in the manuscript and we have now addressed this in the revision (Freely behaving animals, Para 1&2). Our repository has headstage holder designs (in the XtraModifications/Mouse_FreelyMoving folder). This allows leaving the headstage on the implant, and thus minimize the number of connections (albeit increasing the weight for the mouse). Indeed, mice recorded while performing the task described in our manuscript had the head-stage semi-permanently integrated to the implant, and we now highlight this in the revision (Freely behaving animals, Para 1).

Reviewer 2 (Recommendations For The Authors): 

The description of the different versions of the head-stage holders should be more clear, listing also advantages/disadvantages of the different solutions. It would be also useful if the authors could comment on the use of these head-stage holders in rats, since they do not seem to offer much protection.

We thank the reviewer for this point, and we have added notes to the manuscript to clarify the various advantages of the different headstage-holders, and that the headstage can be permanently attached to the implant (Freely behaving animals, Para 1&2). This is the primary advantage of these solutions compared with the minimal implant—at the expense of increasing the implant weight.  

The reviewer’s concerns regarding the lack of protection for implants in rats is well-placed, and we now emphasise that these experiments benefited from the additional protection of an external 3D casing, which is likely critical for use in larger animals (Freely behaving animals, Para 1).

While re-used probes seem to show similar yields across multiple uses (Figure 4C), it seems as if there is a much higher variability of the yield for probes that are used for the first (maybe also second) time. There are probes with much higher than average yields, but it seems none of the re-used probes show such high yields. Is this a real effect? Is this because the high-yield probes happened to have not been used multiple times? Is there an analysis the authors could provide to reduce the concern that yields may generally be lower for re-used probes/that there are no very high yields for re-used probes?

We understand the reviewer’s concern with respect to Figure 4C, however, the re-use of any given probe was determined only by the experimental needs of the project. It is therefore not possible that there is a relationship between probes selected for re-use and unit-yield. We now specify this in the revised legend of Figure 4C. This variability (and the consistency in yield across uses) likely stems from differences between labs, brain region, and implantation protocol.

The authors claim that a 'large fraction' of units could be tracked for the entire duration of the experiment (Figure 5A,B). They mention in the discussion that quantification can be found in a different manuscript (van Beest et al., 2023), but this should also be quantified here in at least some more detail, also for other animals in addition to the one mouse which was recorded for ~100 days. What fraction can be held for different durations? What is the average holding time, etc.?

We agree with the reviewer, and have now added new panels quantifying the probability and reliability of tracking a neuron across days (Figure 5E-F). We also comment on the change in tracking probability across time, and its variability across recordings (Stability, Para 4).

Reviewer 3 (Public Reviews):

Summary:

In this manuscript, Bimbard and colleagues describe a new implant apparatus called "Apollo Implant", which should facilitate recording in freely moving rodents (mice and rats) using Neuropixels probes. The authors collected data from both mice and rats, they used 3 different versions of Neuropixels, multiple labs have already adopted this method, which is impressive. They openly share their CAD designs and surgery protocol to further facilitate the adaptation of their method.

Strengths:

Overall, the "Apollo Implant" is easy to use and adapt, as it has been used in other laboratories successfully and custom modifications are already available. The device is reproducible using common 3D printing services and can be easily modified thanks to its CAD design (the video explaining this is extremely helpful). The weight and price are amazing compared to other systems for rigid silicon probes allowing a wide range of use of the "Apollo Implant".

Weaknesses:

The "Apollo Implant" can only handle Neuropixels probes. It cannot hold other widely used and commercially available silicon probes. Certain angles and distances are not possible in their current form (distance between probes 1.8 to 4mm, implantation depth 2-6.5 mm, or angle of insertion up to 20 degrees).

As we now discuss in the manuscript (Discussion, Para 4), one implant accommodating the diversity of the existing probes is beyond the scope of this project. However, because the design is adaptable, groups should be able to modify the current version of the implant to adapt to their electrodes’ size and format (and can highlight any issues in the Github “Discussions” area).

With Neuropixels, the current range of depths covers practically all trajectories in the mouse brain. In rats, where deeper penetrations may be useful, the experimenter can attach the probe at a lower point in the payload module to expose more of the shank. We now specify this in the Github repository.  

We have now extended the range of inter-probe distances from a maximum of 4 mm to 6.5 mm. Distances beyond this may be better served by 2 implants, and smaller distances could be achieved by attaching two probes on the same side of the docking module. These points are now specified in the revised manuscript (Flexible design, Para 2).

Reviewer 3 (Recommendations For The Authors):

I have only a few questions and suggestions:

Is it possible to create step-by-step instructions for explantation (similar to Figure-1 with CAD schematics)? You mention that payload holder is attached to a micromanipulator, but it is unclear how this is achieved. How was the payload secured with a screw (which screw)? My understanding is that as you turn the screw in the payload holder, it will grab onto the payload module from both sides, but the screw is not in contact with the payload module, correct? I found the screw type on your GitHub, but it would be great if you could add a bill of materials in a table format, so readers don't have to jump between GitHub and article.

We have now added a bill of materials to the revised manuscript (Implant design and materials, Para 2), although up-to-date links are still provided on the Github repository due to changing availability.

What happens if you do a dual probe implant and cannot avoid blood vessels in one or both of the craniotomies due to the pre-defined geometry? Is this a frequent issue? How can you overcome this during the surgery?

Blood vessels can be difficult to avoid in some cases, but we are typically able to rotate/reposition the probes to solve this issue. In some cases, with 4-shank probes, the blood vessel can be positioned between individual probe shanks. We now detail this in the revised manuscript (Assembly and implantation, Para 3).

I assume if the head is not aligned (line-332) the probe can break during recovery. Have you experienced this during explanation?

As we now specify in the manuscript (Explantation, Para 2), we are careful when explanting the probe to avoid this issue, and due to the flexibility of the shanks, it does not appear to be a major concern.

Why did you remove the UV glue (line 435)? How can you level the skull? I assume you have covered bregma and lambda in the first surgery which can create an uneven surface to measure even after you remove the UV glue.

We thank the reviewer for highlighting this omission from the methods. We now explain (Implantation, Carandini-Harris laboratory) that the UV-glue is completely removed during the second surgery, and the skull is cleaned and scored. This improves the adhesion of the dental cement, and allows for reliable levelling of the skull.

In line 112 you mentioned that the number of recorded neurons was stable; however, you found a 3% mean decrease in unit count per day (line 120). Stability is great until day 10 (in Figure 4A), but it deteriorates quickly after that. I think it would help readers if you could add the mean{plus minus}SEM of recorded units in the text for days 1-10, days 11-50, and days 51-100 (using the data from Figure 4A).

We have now added Supplementary Figure 4 to show unit count across bins of days, and a corresponding comment in the text (Stability, Para 2).

A full survey of the probe (Figure 4B) means that you recorded neuronal activity across 4-5000 channels (depending on how many channels were in the brain). While it is clear that a full probe survey can reduce the number of animals needed for a study, it is also clear in this figure that by day 25 you can record ~300 neurons on 4000 channels. It would be great to discuss this in the discussion and give a balanced view of the long-term stability of these recordings.

Overall, keeping a large number of units for a long time still remains a challenge. Here, we could record on average 85 neurons per bank during the first 10 days, and then only 45 after 50 days. It is important to note that our quantification averages across all banks recorded, including those in a ventricle or partly outside of the brain. Thus, our results represent a lower estimate of the total neurons recorded. Our new Supplementary Figure 4 helps to highlight the diversity of neuron number recorded per animal. Further improvements in surgical techniques and spike sorting will likely improve stability further and we have now added this comment in the manuscript (Stability, Para 2). For example, we observed excellent stability in a mouse where the craniotomy was stabilized with KwikSil (Supplementary Figure 5).

The RMS value was around 20 uV in some of the recordings, and according to Figure 4G it is around 16 uV on average. Is it safe to accept putative single units with 20 uV amplitudes, when the baseline noise level is this close to the spike peak-to-peak amplitude?

On average, less than 1% of the units selected using all the other metrics except the amplitude had an amplitude below 30 µV, and 2.6% below 50 µV. Increasing the threshold to 30 µV, or even 50 µV, did not affect the results. We have now added this comment in the Methods (Data processing, Para 3).

Can you add the waveform and ISIH of the example unit from day 106 to Figure 5?

We have now added 4 units tracked up to day 106 in Figure 5.  

Could you move Supplementary Figure 3A to Figure 4? The number of units is more valuable information than the RMS noise level. I understand that you don't have such a nice coverage of all the days as in Figure 3 and 4, but you might be able to group for the first 3 days and the last 3 days (and if data is available, the middle 3 days) as a boxplot. The goal would be for the reader to be able to see whether there is any change in the number of single units over time.

We agree with the reviewer, the number of units is more valuable. We had included this information in Figure 4A-F, but we have made edits to the text to make it clearer that this is what is being shown. The data from Figure 3A is already contained within Figure 4, but in 3A the data is separated by individual labs.

Product numbers are missing in multiple places: line-285 (screw), line-288 (screw), line-290 (screw), line-309 (manipulator), line-374 (gold pin and silver wire), line-384 (Mill-Max), line-394 (silver wire), and many more. It would be great if you could add all these details, so people can replicate your protocol.

We thank the reviewer for highlighting this, and we have added details of screw thread-size and length to relevant parts of the manuscript, although any type of screw can be used. Similarly, other components are non-specific (e.g. multiple silver-wire diameters were used across labs), so we have not included specific product numbers for general consumer items (like screws and silver wires) to avoid indicating that a specific part must be purchased.

While it is great to see lab-specific methods, I am not sure in their current form it helps to understand the protocol better. The information is conveyed in different ways (I assume these were written by different people), in different orders, and in different depths (some mention probe implant location relative to bregma and midline, some don't). There are many different glues, epoxies, cement, wires, and pins. I would recommend rewriting these methods sections under a unified template, so it is easier to follow.

We thank the reviewer for this suggestion and we have rewritten this section of the methods accordingly. We now use a template structure to simplify the comparisons between labs: the same template is used for each lab in each section (payload module assembly, implantation, and data acquisition).

Line-307: why is a skull screw optional for grounding? What did you use for ground and reference if not a ground screw?

We now specify in the manuscript that during head-fixed experiments, the animal’s headplate can be used for grounding, and combined with internal referencing provided by the Neuropixels, yielded lownoise recordings (Implantation protocol, Methods).

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

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Reply to the reviewers

Reviewer 1

Comment 1: A gallery of different cell cycle stages should be included to define KDM4A centrosomal localization at G1, S and G2 phases and whether it is localized to duplicating centrosomes.

Response: We thank the reviewer for this excellent suggestion. We have now included Fig S1H demonstrating the persistence/retention of KDM4A at the centrosome through the cell cycle. The text in the Results section has been updated to reflect this addition.

Comment 2: The immunoprecipitations in Fig. 1 and Supp. Fig. 1 must include appropriate controls. There is no positive control in Fig. 1E and the negative controls for the tagged pulldowns are not appropriate in that there is no other HA-tagged protein in cells. Antibody controls and the reciprocal immunoprecipitations should also be included in the same figure (with controls).

Response: To address the first point, we have included Histone H3 as a positive control for the KDM4A antibody in Figures 1E and 1F. As for the second point raised by the reviewer, the empty vector is an HA-tagged empty vector and so the antibody controls are already included in the Figure as the ‘empty vector’. We have now included detailed information in the Figure legend to clarify the same. In addition, as suggested by the reviewer we have moved the reverse IPs to the main Figure 1 (Figures 1G and 1I).

Comment 3: Fig. 1H: The use of overexpressed GFP-centrin for immunoprecipitations is questionable; centrin overexpression can cause centrosome amplification, so the level of centrin relative to the endogenous level should be demonstrated.

Response: This is with regards to the renumbered Fig. 1J. We have generated hTERT RPE-1 GFP-Centrin expressing stable cell lines that were used for our studies. This is a commonly used cell line in the field and although transient over-expression of GFP-centrin does cause centrosome defects, stable cells are less likely to have elevated centrosome defects. Importantly, the concern of overamplification of centrosomes in these cells is less of a concern given that we have only used these cells to validate the localization of KDM4A to centrosomes using centrin as a centrosome marker. Nonetheless, to ensure that we do not have an aberrant increase in centrosome defects in these cells we have included IF images of our cells (green channel in low-mag and high-mag images below) and are happy to report that we did not observe significantly elevated incidence of centrosome amplification in these stable cell lines.

Comment 4: The precise localization of KDM4A should be determined more clearly with respect to known centrosomal structures/ regions. One would speculate a PCM localization from the data presented here, but the use of centrobin as a marker does not allow the mother centriole's location to be determined with great clarity. It is unclear why the authors chose centrobin as a marker; further explanation of this might be helpful to the reader. Centrobin is usually cited as a daughter centriole marker (PMID: 16275750, but see 29440264). Supp. Fig. 3J appears to shows 2centrioles labelled with centrobin but the paper does not specify whether centrobin is chosen as a daughter marker or otherwise.

Response: We thank the reviewer for this astute observation. Our initial rationale for choosing centrobin was simply to use a centrosome marker that worked robustly and reliably with minimal background staining, essential for the single-molecule super-resolution imaging. The question we wanted to address was generating a geographic region in the cell showing nano-scale localization of KDM4A. The 2D images shown in Fig. 2 can be understandably static and hard to visualize the 3D distribution of KDM4A which is not exclusive to centrioles (centrobin although more daughter centriole, does show weaker signal at the mother centriole as well). We have now extensively re-worked Figure 2, including the inclusion of a video in Supplemental Information. We have now included new nano-scale imaging of KDM4A with g-tubulin (a more traditional centrosome marker), which shows a similar distribution of KDM4A across the centrosome and have also included distribution measurements along the x- and y-axis showing both KDM4A and centrobin/g-tubulin. We have modified the text to refer to centrobin as a centrosome marker (centrobin as the reviewer rightly noted can localize to both centrioles although predominantly at the daughter centriole).

Comment 5: Related to this localization issue, Fig. 2D is unclear to this reviewer. What is this normalized to- a marker or just a set of coordinates? This is an unusual means of representing a localization that does not help the reader understand the (sub-) centrosomal location of KDM4A. The analysis in Supp. Fig. 4 is of somewhat limited value and might be omitted.

__Response: __We apologize for the confusion with the Figure and have simplified the graphs to indicate the single-molecule distribution plotted along the x- and y-axis showing both KDM4A and the centrosome markers i.e. centrobin and g-tubulin.

Comment 6: Fig. 3 shows the amplification of gamma-tubulin signals, but there is no control for cell cycle stage. The Kdm4a knockout cells appear to be twice the size of the controls, suggesting a G2 phase arrest, which can potentiate centrosome overduplication, or cytokinetic failure in a previous cell cycle (this may also be the case in Figs. 6C and 7B). Therefore, these cells should be phenotyped more robustly with respect to their proliferative characteristics and cell cycle phase distribution. Cell cycle phenotypes should also be checked in the rescue experiments.

Response: We thank the reviewer for the comments above. The cells shown in Fig. 3 are interphase cells evaluated for centrosome numbers in Kdm4a-deficient cells, independent of mitosis. We apologize for the lack of clarity and the confusion generated by our erroneous statement at the beginning of the paragraph “we next investigated a functional role for KDM4A at mitotic centrosomes”. In fact, we started by first evaluating interphase cells to interrogate consequences of losing Kdm4a, followed by evaluations of the mitotic phenotypes once we observed increased centrosome numbers. This error has now been corrected in the Results.

As for the reviewer’s comment on phenotyping the cells further, we have now performed these evaluations and have included them in Figure 3 (as new panels Figures 3D, 3E, 3F). Our MTT proliferation assays showed the Kdm4a-null cells proliferated slower than control non-targeted MEFs, although this did not result in any significant issues with cell cycle progression with both cell lines progressing without any arrests and importantly without accumulating increased DNA content/aneuploidy. The rescue cell lines were also phenotyped (new Figures 7C, 7D and 7E) and similarly did not show any altered cell cycle progression.

Comment 7: Related to the previous point, in the DAPI staining in Figure 5A, 'pseudo-bipolar' cells #1 and #3 (from the top) seem to have greatly increased levels of DNA, suggesting failed cytokinesis as a mechanism of centrosome abnormality. This is a very different process to a centrosome overduplication within a single cell cycle; given that these are knockouts, it is not clear what conclusions should be drawn from the current analysis.

Response: The reviewer makes an excellent point, about the increased centrosome numbers arising from failure to complete cytokinesis. We have performed further phenotyping of the Kdm4a-null cells, included as new Figures 3D, 3E and 3F. Although the Kdm4a-deficient cells grew slower than their Kdm4a-proficient counterparts, there were no significant issues with cell cycle progression and importantly no evidence of increased aneuploidy. We have also now performed further analysis using centrin as a centriole marker to quantify centrosome numbers (new Figures 4C, 4D and 4E) and have found that there is a significant increase in disjointed centrioles (Figure 4E) suggesting that in addition to any potential amplification there also appears to be an increased loss of cohesion in cells deficient for KDM4A. We have also further confirmed presence of single/disjointed centrioles using TEM analysis (new Figure 4F)

Comment 8: The JIB-04 result may suggest that KDM4A inhibition causes fragmentation of spindle poles, given that it is a relatively short treatment that would probably not be long enough for centrosome overduplication. Whether this arises during M phase, distinct from the over duplication phenotype seen where there are >4 centrioles, should be posed as a separate question- these may be distinct outcomes from KMD4A inhibition at different cell cycle times.

Response: We completely agree with the reviewer that the JIB-04 treatment is relatively short and does in fact suggest that this is independent of any over duplication phenotype observed in the Kdm4a-CRISPR knockouts. We thank the reviewer for the suggestion of posing two separate questions to address this point and have made the changes in the manuscript (see Results). In addition, our new data discussed in Comment 7 above, corroborates this hypothesis.

Comment 9: It is unclear why the authors call the cell shown in Fig. 4B 'pseudo-bipolar'- there are clearly four poles here (as in the multipolar example shown in Fig 5A). This makes the data in Fig. 5 difficult to interpret. The authors should review their classification.

Response: We thank the reviewer for catching this error. We apologize for the misrepresentation of the representative image and have now included the correct image that shows pseudo-bipolar spindles (new Figure 5D) replacing the multipolar spindle. In addition, we have reviewed our data and the quantitation remains unchanged.

Comment 10: Expression of the vector control in the Kdm4a nulls in Fig. 7A appears to show a decline in the H3K36me3 levels, confusing the outcome of this experiment. Quantitation should be provided for these blots.

Response: We have now included the requested quantitation (new Figure 7B) for Figure 7A.

Comment 11: A rescue experiment should be included for the siRNA knockdown of KDM4A.

Response: A rescue experiment with the siRNA experiments is challenging as we use a pooled siRNA (4 siRNAs) targeting KDM4A. Rescue with a KDM4A construct would result in the knockdown of the exogenously expressed KDM4A as well. The rescue experiments have been therefore performed with the CRISPR knockout cell lines.

Comment 12: Size markers should be shown in all immunoblots.

Response: We have now included size markers as requested by the reviewer for all Figures showing immunoblots (Figures 1, 5, 7 and Supplementary Figures 1, 5).

Comment 13: p.6, 11 'the resulting payment' and 'caustic chromosome environment' are strange usages and should be rephrased.

Response: The text has been rephrased.

Comment 14: Are all panels shown at the same magnification in Fig. 1B? (The telophase DAPI appears different to the anaphase)

Response: We have confirmed that the magnification is the consistent across the entire panel of images in Figure 1.

Comment 15: Blow-up panels should be shown so that the centrosomes can be visualised more clearly (Fig. 1 and Supp. Fig. 1).

Response: We have now included blow-up panels for all centrosome images in Figure 1 and Supplemental Figure 1.

Comment 16: The MT labelling in Fig. 1D is not of good quality; this imaging should be improved.

Response: We believe that microtubule densities are impacted by modulating KDM4A in cells likely arising from alternate mechanisms that we are currently investigating. However, to the reviewer’s point we have placed the transient overexpression images in Supplementary information (Supplemental Figure 1I) and have replaced with new Figure 1D, using our stable clones expressing RFP-vector or RFP-KDM4A.

Reviewer 2

Comment 1: Coimmunoprecipitation and GFP-trap analyses demonstrated interactions between KDM4A and centrobin, CP110, and centrin-2 (Fig. 1). While the authors suggest a functional a functional association with the centrosome, it is noteworthy that no known centriole protein has been identified to interact simultaneously with centrobin, CP110, and centrin-2, located in distinct sub-centriolar regions. Additionally, 3D super-resolution microscopy indicates that KDM4A is not restrained to a particular region of the centrosome, surely not at the centriole (Fig. 4D). These results hint that centrobin, CP110 and centrin-2 may be potential substrates of KDM4A. Therefore, it is worth to conduct immunostaining and coimmunoprecipitation analyses with the JIB-04-treated cells.

Response: The reviewer makes an excellent point. The co-immunoprecipitation studies were not conducted to show a direct interaction between the centrosome proteins and KDM4A, but more as a proof-of principle that KDM4A is interacting with centrosome proteins (we do not know if this is direct or indirect, although the data would likely suggest an indirect mechanism). Given that we had used centrobin, centrin and CP110 in our immunofluorescence analysis we also used them for our co-IP studies to provide further evidence of a centrosome localization for KDM4A. It is intriguing that any one of these proteins could in fact be substrates for KDM4A, although an in-depth study would be required to prove this since the super-resolution localization would suggest that KDM4A is not at the centrioles per se and is in fact more of a pericentriolar protein. We have clarified this point in the Discussion. Although the experiments suggested with the JIB treatment would be intriguing, identifying a bone fide centrosome substrate for KDM4A’s demethylase activity is not trivial and would require identification of methylation on a substrate followed by then determining if KDM4A can demethylate the target. Methylation on non-chromatin substrates such as centrosome proteins is not currently well characterized.

Comment 2: The generation supernumerary centrioles in Kdm4a KO MEFs is intriguing yet warrants careful description (Fig. 3). First, supernumerary centrioles should be coimmunostained with multiple centriole markers, such as centrin-2, CP110 and centrobin antibodies at synchronized populations such as G1, S and M phases. Second, the number of centrioles per cells may be counted and statistically analyzed.

Response: We thank the reviewer for making this suggestion. We have now included new Figures 4C, 4D, 4E and 4F where we show immunofluorescence with Centrin 2 in Kdm4a-deficient cells. Having found an increased incidence of unpaired centrioles in cells deficient for Kdm4a we have further performed TEM to show the presence of these unpaired/disjoint centrioles.

Comment 3: The high proportion of pseudo-bipolar cells in the NT group requires attention (Fig. 5).

Response: We thank the reviewer for this astute observation. To obtain enough mitotic cells for analysis we synchronized the MEFs, which appeared to increase the baseline of pseudo-bipolar spindles reflected in the quants. Despite this increase the differential between the controls and Kdm4a-null cells is significant, as indicated, and we have now made this evident in the text for clarity.

Comment 4: The KO-rescue cells should be valuable tools to confirm specific roles of KDM4A at the centrosome (Fig. 7). The authors may generate stable cell lines in which wild type and H188A mutant KDM4A are expressed in the KO cells, and use them for centrosome localization of the ectopic proteins, spindle formation and supernumerary centriole generation.

Response: The reviewer makes an excellent point and in fact we generated the stables (Figure 7) with this idea in mind. Unfortunately (but not completely surprising as this is frequently observed in comparable settings) we observed decreased mitotic abnormalities and genomic instability in the Kdm4a-null cells over time in culture. This is likely arising from a compensatory mechanism/redundancy that perhaps kicks in to enable survival of these cells. The process of generating the stables was therefore tricky with us only being able to reliably analyze genomic stability as a downstream readout of mitotic abnormalities that might have occurred in these cells (early passages analyzed for genomic stability).

Reviewer 3

Comment 1: Figure 1D: the RFP vector alone localizes to the centrosome. How was the signal across the cells? Can the authors provide a fluorescence intensity measurement comparing the negative control RFP and RFP-KDM4A to demonstrate the localization at centrosomes of the enzyme? While I found the endogenous staining convincing, the fusion protein is less.

Response: The MEFs were transiently transfected with the RFP-vector/KDM4A for the images shown. In our experience it is not uncommon for the RFP/mCherry/GFP tags to be prominent at the spindle and often tagged vector controls are omitted from many prominent publications. However, in our case there is a significant increase in RFP-KDM4A signal observed at the spindle poles and we have now included the quantification of signal from the two poles in Supplemental Figure 1J where the signal is 3 times higher in the RFP-KDM4A expressing cells compared to vector. We have also included new Figure 1D demonstrating the RFP-KDM4A localization to spindle poles in our stable cell lines where the signal for the control RFP-vector is negligible. The transient transfection data has been moved to Supplemental Figure 1 (1I).

Comment 2: Figure 1E-F: How specific do the authors think the interactions with CP110 and centrobin are? Do they IP the entire centrosome proteome or do they think that they reveal some specific interactions within the centrosome? Can the authors comment on this? What is the significance of these interactions? Do the authors think that KDM4A is a centriolar component? Or a PCM component? This is only briefly mentioned in the discussion, it should be extended. Did they try to IP PCM components as well?

Response: The reviewer brings up an excellent point. The purpose of the immunoprecipitation was to demonstrate the ability of KDM4A to pull down centrosome associated proteins and vice versa. We are unable to comment on the interactions being direct or indirect, although we suspect that most of the interactions are likely indirect, given that KDM4A is not specifically localized to the centrioles. As per the reviewer’s suggestion, we have now expanded the Discussion to speculate on the potential significance of these interactions and how they might enable identification of novel KDM4A interactors and potential substrates.

Comment 3: Fig.S3: the signal of KDM4A seems broader than that of centrobin, with an average diameter of 749 nm. What is the diameter of centrobin for comparison using this method? The interpretation of the authors concerning this localization is not clear to me: "The quantification data of the diameter of the KDM4A distribution, independently in the different axes (x, y, z), revealed a relatively uniform/circular distribution (Fig. 2D) suggesting that KDM4A was not restrained to a particular region of the centrosome". Is KDM4A at centriole or at centrosomes? PCM or centriole component? From the interpretation stated above, it seems that KDM4A is everywhere from the proximal to the distal axis of the centriole, is it correct? But isn't more PCM?

Response: We would like to apologize for the lack of clarity with respect to the centrobin measurements compared to those of KDM4A. We have attempted to clarify the distributions measurements by showing the distributions for both the centrobin and KDM4A signals. In addition, we have anow included new data with g-tubulin to show co-localization of KDM4A signal with g-tubulin and to also demonstrate that the signal for KDM4A is not centriole specific but is essentially more uniformly distributed throughout the centrosome. We have also included a video (Video 1) as Supplemental data to clarify this point.

Comment 4: Fig.4B: The authors established that there is an increase in centrosome number upon short inactivation of KDM4A by JIB-04, which affects its enzymatic activity and not the scaffolding function. In addition, the loss of KDM4A phenocopies the effect of the drug: this means that the enzymatic activity is required to control the centrosome number. This is also re-enforced by the rescue with WT enzyme and not the enzymatically dead mutant of KDM4A (looking at micronuclei formation-Fig.7). Could the author speculate on this? The fast action of the inhibitor would exclude a block in S phase as stated in the discussion. The authors mention centrosome fragmentation but there is no evidence that this is happening here. The authors mentioned several possible mechanisms in the discussion without really exploring them. The authors also mention here that the chronic loss of KDM4A could arise through a distinct mechanism than that of the inhibitor, this statement was surprising. Could the authors check if they have a cell cycle delay or block in their KO cells? While it seems that the authors would like to address these points in the future, I think that the mechanistic aspect is lacking in this study or at least some hints of it.

Response: We agree with all the points brought up by the reviewer. We have elaborated the discussion as recommended, however the challenge with a demethylase is identifying a potential methyltransferase that can lay a methyl mark on a potential substrate followed by then establishing KDM4A as an eraser for the same substrate. To address, the comment about a cell cycle delay as also brought up by Reviewer 1 (Comment 6), we have performed additional phenotyping of the cells and these data are now included in Figure 3 (as new panels Figures 3D, 3E, 3F) and new Figures 7C, 7D and 7E (for the rescue cell lines) which did not show any altered cell cycle progression.

Comment 5: In general, the figures are organized in an unconventional manner with the panels from one figure distributed on several pages. Could the authors group the panels of each figure in one page to ease the understanding and the reading?

Response: Although we do understand how having multiple panels on several pages makes its difficult to read, the immunofluorescence images would be extremely difficult to observe clearly. Also, this comment will be resolved once the manuscript is accepted for publication as we will re-format per journal guidelines.

Comment 6: Figure S1F-G: the authors provide a large field of view showing a dozen of nuclei. While I acknowledge that this is to show the overall staining, itis difficult to really see the foci of KDM4A or g-Tubulin or centrin. The quality of the images looks really pixelated; this might be due to the PDF compression, but I cannot see any red signal on the panels. Could the authors enhance the B/C of the images so that one can see the signal corresponding to the centrosomes? Is it also possible to have a zoom on the centrosome itself with split channels to illustrate the co-localization? As it is, it is not clearly shown. In the panel G, there are many foci of KDM4A in the nucleus and 2 associated with a centrin staining, which correspond to the centrosomes. However, the signals do not seem to fully colocalize. What do the authors think about this?

Response: We have provided larger zoomed in view of the cells in Figure S1 as requested.

Comment 7: Figure 1A: same comment as above concerning the quality of the image. I am also concerned by the g-Tubulin staining as it looks not on focus and I do not see any foci that would correspond to the centrosome position, while the merge image clearly shows yellow signal, proof of co-localisation. Could the author correct this? In the inset, can the authors zoom on the centrosomes and display the split channels so that one can appreciate the co-localization of the 2 signals?The quality and display of Fig.1B is much better. Could we have the same rendering for the interphase cells of 1A?

Response: The picture in Figure 1A is a raw image. This image has not undergone the same post-image deconvolution applied to the other images in the manuscript. The deconvolved images reduce the KDM4A signal in the nucleus and only demonstrate the highly intense signal at the centrosomes especially in mitotic cells. If we show the deconvolved image here it would lead to the erroneous perception that there is no KDM4A signal in the nucleus and the rest of the cell. To clarify this point we have modified the figure legends to state that this is a raw image. In addition, we have also provided blow-ups of the centrosomes specifically.

Comment 8: Fig.3D: the nucleus of the cell is really affected with many blobs or micronuclei. Is this cell dying? The authors count the number of g-tubulin foci in interphase (Fig. 3C). Could they do it in mitosis and use centrin? In mitosis, there should be 4

Response: The cell in question is not dying and is micronucleated. The question of genomic instability is addressed later in the manuscript and hence the point was not made in this figure. We thank the reviewer for suggesting use of centrin. We have now included these data as new Figures 4C, 4D and 4E.

Authors’ Response (31 December 2024)

GENERAL ASSESSMENT

In this article, Kay refutes a major claim made by Watson et al., 2023. In the original publication, Watson et al. argue that macromolecular condensation acts as a cellular buffering mechanism to compensate for the effects of osmotic shock. In particular, they claim that, when water is drawn into or out of the cell due to hypo- or hyper-osmotic shock, respectively, macromolecular condensates rapidly capture (during hypo-osmotic shock) or release (during hyper-osmotic shock) free water to maintain a constant water potential (presumably in addition to a constant solute concentration and osmolality) within the cell. While Watson et al. find that macromolecular condensation in cells is responsive to osmotic shock, they do not measure intracellular water potential, osmolality, or macromolecular density in intact cells, and therefore do not directly demonstrate that biocondensation buffers any of these properties in living cells. In response, Kay argues that, while such a water buffer could temporarily maintain an osmolality differential across the membrane, this osmolality differential will necessarily drive water across the membrane until the osmolality within the cell equals the osmolality outside of the cell. Therefore, the steady-state behaviour is expected to be identical with and without the water buffer. Using the well-established pump-leak model for osmotic water transport, Kay further shows that the timescale at which a water buffer can maintain even a 10% osmolality differential across the membrane is at most a minute for a typical animal cell.

Overall, Kay 2024 provides a compelling rebuttal to a strong claim made by Watson et al. However, there is an opportunity for Kay to acknowledge nuanced situations where such a water buffering mechanism as that posited by Watson may be useful to cells. It’s also unclear if Kay has described a major inconsistency with Watson et al., particularly since the water release rate from condensates is not well quantified.<br />

I thank the reviewers and curating editor for taking the time to work through our paper and providing guidance for improving it.

In what follows we have responded to all the points raised during the review in blue and have attached a revised version of the manuscript with all changes marked up. I should note that I have included my collaborator Zahra Aminzare as an author on the paper, since she did significant work in overcoming some difficulties with the simulations.

RECOMMENDATIONS

Essential revisions:

1. The author could acknowledge nuanced situations in which the water buffering mechanism described by Watson et al. may be useful to cells. For example, by slowing the rate of change of intracellular osmolarity due to osmotic shock and thus giving the cell time for more active feedback mechanisms to engage, or in buffering rapid fluctuations in extracellular osmolality

The only situation that we could think of where the change in osmolarity was transient and fast, is blood cells moving through the vasa recta in kidney (L 143) , where the interstitial osmolarity gets as high as 1,200 mOsm. The cells are exposed to this change for a few seconds, approximately every 5 min. However, no one seems to have measured how much the plasma changes as blood transits through the vasa recta. we have elaborated a bit more on this in the revised version of the manuscript.

1. The flux of water across lipid membranes depends on the pressure difference across the membrane. The author simulated the situation with a 30 mOsm (~75 kPa) osmotic pressure difference. Considering that physiologically relevant pressure fluctuations can be much lower (a few kPa), is it possible that a water buffer would be more effective when there are small pressure differences across the cell membrane? The author should discuss this.

We have repeated the simulations now using smaller osmotic gradient (15 mOsm). With these it can buy a little more time since that rate of water influx is slower. This has been included in the revised paper (L 76-78).

1. The author should cite the work from which they obtained the water buffer release rate.

To the best of our knowledge there is no information on this point. When I first presented Watson et al. with my counter argument, I assumed that the release of water was instantaneous. They countered that it is likely to be more gradual, therefore I simulated a slower release process. In the revised version of the paper, we now included both slow and quick release to show that it makes little difference. We have now noted that for the WB to counteract the change in extracellular osmolarity, the rate of water release must match very closely that of the water influx or efflux, which seems implausible (see L 81-86).

1. It would be helpful to measure the dynamics of intracellular volume concurrently with biocondensate formation under cells exposed to osmotic shock (ideally under experimental conditions where cells either do or do not form condensates). If Watson et al.’s hypothesis is correct, the volume should not change (this seems unlikely). If your hypothesis is correct that buffering could only ever be temporary, one could then experimentally determine the buffering timescale by measuring the stall time between the shock and when the volume begins to change. The stall should also disappear in conditions where condensate formation is inhibited.

We have added this suggestion to the revised paper (L 152-154).

1. There are two inaccuracies in the discussion of membrane tension caused by osmotic pressure that would benefit from being corrected. First, when using Laplace’s Law to calculate membrane tension induced by 30 mOsm pressure, the author used a cell radius of 10 um and calculated a large (180 mN/m) membrane tension. This is significantly overestimated because the cell membrane can form local deformations via attachment to the cytoskeleton. These local deformations are typically around 10 - 100 nm, thus reducing the calculated membrane tension by 2-3 orders of magnitude, below the lysis tension of the membrane (1 - 10 mN/m). Second, the author is correct that measured resting membrane tension is low (< 0.3 mN/m). However, recent evidence suggests that tension on the cell membrane can locally or transiently reach much higher levels (to > 1mN/m). This is supported by activation of mechanosensitive ion channels such as Piezo1, which require an activation membrane tension ~ 1mN/m.

We have now included a discussion of the first point (see L 127-130). On the second point, if the reviewers could please provide us with a reference to this we would be grateful and will include it in the revised version of the paper.

1. The discussion on non-equilibrium states is not very clear. Is the author suggesting that a water buffer can work more efficiently in an equilibrium system such as a giant vesicle?

The reviewers raise an interesting point. In a closed system like a test tube a WB could act without opposition, but as soon as one introduces a membrane that is permeable to water it will be overwhelmed, no matter if the system is an energetically driven one like the PLM or a passive one like a giant vesicle. There is no difference between a passive and active system. To show this we set up a cell without a sodium pump and used a high concentration of impermeant extracellular molecules to stabilize the volume. (see L 102-107, and Fig. 1)

1. Because the pump-leak model is generic, some contextual discussion of condensates would be helpful. For example, the dynamic formation of hydrogen bonds, van der Waals interactions, and possible charges resulting from hyperosmotic or low osmotic conditions that may indirectly participate in the hypothesis.

Our argument does not depend on the mechanism of water release or binding. There may indeed be many ways of changing the water bound to a macromolecule, but we will leave it to proponents of the WB hypothesis to explore this.

1. Has the author considered whether the thermodynamic driving forces associated with phase separation and condensate formation might affect the ability of condensates to buffer intracellular osmolality?

This is beyond the scope of our paper, so again we will leave it to others to address this. Rather than discuss all the different scenarios we have chosen to quote the papers of (Guttman et al., 1995; Parsegian et al., 2000), which Watson et al. do not refer to.

Optional suggestions:

1. The language of the article focuses on the role of membrane permeability, which is of course key. However, it might be helpful to explicitly state that an osmolality differential will always drive water across the membrane, so even if a water buffer could temporarily maintain such an osmolality differential, water will continue to flow across the membrane until the buffer is saturated and this differential is equalized.

This is indeed what will happen. We have tried to clarify this in the revised version (see L 208-210).

(This is a response to peer review conducted by Biophysics Colab on version 1 of this preprint.)

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

The manuscript by Oleh et al. uses in vitro electrophysiology and compartmental modeling (via NEURON) to investigate the expression and function of HCN channels in mouse L2/3 pyramidal neurons. The authors conclude that L2/3 neurons have developmentally regulated HCN channels, the activation of which can be observed when subjected to large hyperpolarizations. They further conclude via blockade experiments that HCN channels in L2/3 neurons influence cellular excitability and pathway-specific EPSP kinetics, which can be neuromodulated. While the authors perform a wide range of slice physiology experiments, concrete evidence that L2/3 cells express functionally relevant HCN channels is limited. There are serious experimental design caveats and confounds that make drawing strong conclusions from the data difficult. Furthermore, the significance of the findings is generally unclear, given modest effect sizes and a lack of any functional relevance, either directly via in vivo experiments or indirectly via strong HCN-mediated changes in known operations/computations/functions of L2/3 neurons.

Specific points:

(1) The interpretability and impact of this manuscript are limited due to numerous methodological issues in experimental design, data collection, and analysis. The authors have not followed best practices in the field, and as such, much of the data is ambiguous and/or weak and does not support their interpretations (detailed below). Additionally, the authors fail to appropriately explain their rationale for many of their choices, making it difficult to understand why they did what they did. Furthermore, many important references appear to be missing, both in terms of contextualizing the work and in terms of approach/method. For example, the authors do not cite Kalmbach et al 2018, which performed a directly comparable set of experiments on HCN channels in L2/3 neurons of both humans and mice. This is an unacceptable omission. Additionally, the authors fail to cite prior literature regarding the specificity or lack thereof of Cs+ in blocking HCN. In describing a result, the authors state "In line with previous reports, we found that L2/3 PCs exhibited an unremarkable amount of sag at 'typical' current commands" but they then fail to cite the previous reports.

We thank the reviewer for the thorough examination of our manuscript; however, we disagree with many of the raised concerns for several reasons, as detailed here:

To address the lack of certain citations, we would like to emphasize that in the introduction section, we did initially focus on the several decades-long line of investigation into the HCN channel content of layer 2/3 pyramidal cells (L2/3 PCs), where there has undoubtedly been some controversy as to their functional contribution. We did not explicitly cite papers that claimed to find no/little HCN channels/sag- although this would be a significant list of publications from some excellent investigators, as methods used may have differed from ours leading to different interpretations. Simply stated, unless one was explicitly looking for HCN in L2/3 PCs, it might go unobserved. However, we now addressed this more clearly in the revision:

Just to take one example: in the publication mentioned by the reviewer (Kalmbach et al 2018), the investigators did not carry out voltage clamp or dynamic clamp recordings, as we did in our work here. Furthermore, the reported input resistance values in the aforementioned paper were far above other reports in mice (Routh et al. 2022, Brandalise et al 2022, Hedrick et al 2012; which were similar to our findings here), suggesting that recordings in Kalmbach were carried out at membrane potentials where HCN activation may be less available (Routh, Brager and Johnston 2022).

Another reason for some mixed findings in the field is undoubtedly due to the small/nonexistent sag in L2/3 current clamp recordings (in mice). We also observed a very small sag, which can be explained by the following:  The ‘sag’ potential is a biphasic voltage response emerging from a relatively fast passive membrane response and a slower Ih activation. In L2/3 PCs, hyperpolarization-activated currents are apparently faster than previously described, and are located proximally (Figure 2 & Figure 5). Therefore, their recruitment in mouse L2/3 PCs is on a similar timescale to the passive membrane response, resulting in a more monophasic response. We now include a more full set of citations in the updated introduction section, to highlight the importance of HCN channels in L2/3 PCs in mice (and other species).

The justification for using cesium (i.e., ‘best practices’) is detailed below.

(2) A critical experimental concern in the manuscript is the reliance on cesium, a nonspecific blocker, to evaluate HCN channel function. Cesium blocks HCN channels but also acts at potassium channels (and possibly other channels as well). The authors do not acknowledge this or attempt to justify their use of Cs+ and do not cite prior work on this subject. They do not show control experiments demonstrating that the application of Cs+ in their preparation only affects Ih. Additionally, the authors write 1 mM cesium in the text but appear to use 2 mM in the figures. In later experiments, the authors switch to ZD7288, a more commonly used and generally accepted more specific blocker of HCN channels. However, they use a very high concentration, which is also known to produce off-target effects (see Chevaleyre and Castillo, 2002). To make robust conclusions, the authors should have used both blockers (at accepted/conservative concentrations) for all (or at least most) experiments. Using one blocker for some experiments and then another for different experiments is fraught with potential confounds.

To address the concerns regarding the usage of cesium to block HCN channels, we would like to state that neither cesium nor ZD-7288 are without off-target effects, however in our case the potential off-target effects of external cesium were deemed less impactful, especially concerning AP firing output experiments. Extracellular cesium has been widely accepted as a blocker of HCN channels (Lau et al. 2010, Wickenden et al. 2009, Rateau and Ropert 2005, Hemond et al. 2009, Yang et al. 2015, Matt et al. 2010). However, it is well known to act on potassium channels as well at higher concentrations, which has been demonstrated with intracellular and extracellular application (Puil et al. 1981, Fleidervish et al. 2008, Williams et al. 1991, 2008).

Although we initially performed ‘internal’ control experiments to ensure the cesium concentration was unlikely to greatly block voltage gated K+ channels during our recordings, we recognize these were not included in the original manuscript. These are detailed as follows: during our recordings cesium had no significant effect on action potential halfwidth, ruling out substantial blocking of potassium channels, nor did it affect any other aspects of suprathreshold activity (now reported in results, page 4 - line 113). Furthermore, we observed similar effects on passive properties (resting membrane potential, input resistance) following ZD-7288 as with cesium, which we now also updated in our figures (Supplementary Figure 1). We did acknowledge that ZD-7288 is a widely accepted blocker of HCN, and for this reason we carried out some of our experiments using this pharmacological agent instead of cesium.

On the other hand, ZD-7288 suffers from its own side effects, such as potential effects on sodium channels (Wu et al. 2012) and calcium channels (Sánchez-Alonso et al. 2008, Felix et al. 2003). As our aim was to provide functional evidence for the importance of HCN channels, we initially deemed these potential effects unacceptable in experiments where AP firing output (e.g., in cell-attached experiments) was measured. Nonetheless, in new experiments now included here, we found the effects of ZD and cesium on AP output were similar as shown in new Supplemental Figure 1.

Many experiments were supported by complementary findings using external cesium and ZD-7288. For example, the effect of ZD-7288 on EPSPs was confirmed by similar synaptic stimulation experiments using cesium. This is important, as synaptic inputs of L2/3 PCs are modulated by both dendritic sodium (Ferrarese et al. 2018) and calcium channels (Landau 2022), therefore the application of ZD-7288 alone may have been difficult to interpret in isolation. We thank the reviewer for bringing up this important point.

(3) A stronger case could be made that HCN is expressed in the somatic compartment of L2/3 cells if the authors had directly measured HCN-isolated currents with outside-out or nucleated patch recording (with appropriate leak subtraction and pharmacology). Whole-cell voltage-clamp in neurons with axons and/or dendrites does not work. It has been shown to produce erroneous results over and over again in the field due to well-known space clamp problems (see Rall, Spruston, Williams, etc.). The authors could have also included negative controls, such as recordings in neurons that do not express HCN or in HCN-knockout animals. Without these experiments, the authors draw a false equivalency between the effects of cesium and HCN channels, when the outcomes they describe could be driven simply by multiple other cesium-sensitive currents. Distortions are common in these preparations when attempting to study channels (see Williams and Womzy, J Neuro, 2011). In Fig 2h, cesium-sensitive currents look too large and fast to be from HCN currents alone given what the authors have shown in their earlier current clamp data. Furthermore, serious errors in leak subtraction appear to be visible in Supplementary Figure 1c. To claim that these conductances are solely from HCN may be misleading.

We disagree with the argument that “Whole-cell voltage-clamp in neurons with axons and/or dendrites does not work”. Although this method is not without its confounds (i.e. space clamp), it is still a useful initial measure as demonstrated countless times in the literature. However, the reviewer is correct that the best approach to establish the somatodendritic distribution of ion channels is by direct somatic and dendritic outside-out patches. Due to the small diameter of L2/3 PC dendrites, these experiments haven’t been carried out yet in the literature for any other ion channel either to our knowledge. Mapping this distribution electrophysiologically may be outside the scope of the current manuscript, but it was hard for us to ignore the sheer size of the Cs⁺ sensitive hyperpolarizing currents in whole cell. Thus, we will opt to report this data.

Also, we should point out that space clamp-related errors manifest in the overestimation of frequency-dependent features, such as activation kinetics, and underestimation of steady-state current amplitudes. The activation time constant of our measured currents are somewhat faster than previously reported; reducing major concerns regarding space clamp errors. Furthermore, we simply do not understand what “too large… to be from HCN currents” means. Our voltage-clamp measured currents are similar to previously reported HCN currents (Meng et al. 2011, Li 2011, Zhao et al. 2019, Yu et al. 2004, Zhang et al. 2008, Spinelli et al. 2018, Craven et al. 2006, Ying et al. 2012, Biel et al. 2009).

Furthermore, we should point out that our measured currents activated at hyperpolarized voltages, had the same voltage dependence as HCN currents, did not show inactivation, influenced both input resistance and resting membrane potential, and are blocked by low concentration extracellular cesium. Each of these features would point to HCN.

(4) The authors present current-clamp traces with some sag, a primary indicator of HCN conductance, in Figure 2. However, they do not show example traces with cesium or ZD7288 blockade. Additionally, the normalization of current injected by cellular capacitance and the lack of reporting of input resistance or estimated cellular size makes it difficult to determine how much current is actually needed to observe the sag, which is important for assessing the functional relevance of these channels. The sag ratio in controls also varies significantly without explanation (Figure 6 vs Figure 7). Could this variability be a result of genetically defined subgroups within L2/3? For example, in humans, HCN expression in L2/3 varies from superficial and deep neurons. The authors do not make an effort to investigate this. Regardless of inconsistencies in either current injection or cell type, the sag ratio appears to be rather modest and similar to what has already been reported previously in other papers.

We thank the reviewer for pointing out that our explanation for the modest sag ratio might have not been sufficient to properly understand why this measurement cannot be applied to layer 2/3 pyramidal cells. Briefly: sag potential emerges from a relatively (compared to I_h) fast passive membrane response and a slower HCN recruitment. The opposing polarity and different timescales of these two mechanisms results in a biphasic response called “sag” potential. However, if the timescale of these two mechanisms is similar, the voltage response is not predicted to be biphasic. We have shown that hyperpolarization activated currents in our preparations are fast and proximal, therefore they are recruited during the passive response (see Figure 2g.). This means that although a substantial amount of HCN currents are activated during hyperpolarization, their activation will not result in substantial sag. Therefore, sag ratio measurement is not necessarily applicable to approximate the HCN content of mouse L2/3 PCs. We would like to emphasize that sag ratio measurements are correct in case of other cell types (i.e. L5 and CA1 PCs_,_ and our aim is not to discredit the method, but rather to show that it cannot be applied similarly in the case of mouse L2/3 PCs.

Our own measurements, similar to others in the literature show that L2/3 PCs exhibit modest sag ratios, however, this does not mean that HCN is not relevant. I_h activation in L2/3 PCs does not manifest in large sag potential but rather in a continuous distortion of steady-state responses (Figure 2b.). The reviewer is correct that L2/3 PCs are non-homogenous, therefore we sampled along the entire L2/3 axis. This yielded some potential variability in our results (i.e., passive properties); yet we did not observe any cells where hyperpolarizing-activated/Cs⁺-sensitive currents could not be resolved. As structural variability of L2/3 cells does result in variability in cellular capacitance, we compensated for this variability by injecting cellular capacitance-normalized currents. Our measured cellular capacitances were in accordance with previously published values, in the range of 50-120 pF. Therefore, the injected currents were not outside frequently used values. Together, we would like to state that whether substantial sag potential is present or not, initial estimates of the HCN content for each L2/3 PC should be treated with caution.

(5) In the later experiments with ZD7288, the authors measured EPSP half-width at greater distances from the soma. However, they use minimal stimulation to evoke EPSPs at increasingly far distances from the soma. Without controlling for amplitude, the authors cannot easily distinguish between attenuation and spread from dendritic filtering and additional activation and spread from HCN blockade. At a minimum, the authors should share the variability of EPSP amplitude versus the change in EPSP half-width and/or stimulation amplitudes by distance. In general, this kind of experiment yields much clearer results if a more precise local activation of synapses is used, such as dendritic current injection, glutamate uncaging, sucrose puff, or glutamate iontophoresis. There are recording quality concerns here as well: the cell pictured in Figure 3a does not have visible dendritic spines, and a substantial amount of membrane is visible in the recording pipette. These concerns also apply to the similar developmental experiment in 6f-h, where EPSP amplitude is not controlled, and therefore, attenuation and spread by distance cannot be effectively measured. The outcome, that L2/3 cells have dendritic properties that violate cable theory, seems implausible and is more likely a result of variable amplitude by proximity.

To resolve this issue, we made a supplementary figure showing elicited amplitudes, which showed no significant distance dependence and minimal variability (new Supplementary Figure 6). We thank the reviewer for suggesting an amplitude-halfwidth comparison control (now included as new Supplementary Figure 6).). To address the issue of the non-visible spines, we would like to note that these images are of lower magnification and power to resolve them. The presence of dendritic spines was confirmed in every recorded pyramidal cell observed using 2P microscopy at higher magnification.

We would like to emphasize that although our recordings “seemingly” violated the cable theory, this is only true if we assume a completely passive condition. As shown in our manuscript, cable theory was not violated, as the presence of NMDA receptor boosting explained the observed ‘non-Rallian’ phenomenon.

(6) Minimal stimulation used for experiments in Figures 3d-i and Figures 4g-h does not resolve the half-width measurement's sensitivity to dendritic filtering, nor does cesium blockade preclude only HCN channel involvement. Example traces should be shown for all conditions in 3h; the example traces shown here do not appear to even be from the same cell. These experiments should be paired (with and without cesium/ZD). The same problem appears in Figure 4, where it is not clear that the authors performed controls and drug conditions on the same cells. 4g also lacks a scale bar, so readers cannot determine how much these measurements are affected by filtering and evoked amplitude variability. Finally, if we are to believe that minimal stimulation is used to evoke responses of single axons with 50% fail rates, NMDA receptor activation should be minimal to begin with. If the authors wish to make this claim, they need to do more precise activation of NMDA-mediated EPSPs and examine the effects of ZD7288 on these responses in the same cell. As the data is presented, it is not possible to draw the conclusion that HCN boosts NMDA-mediated responses in L2/3 neurons.

As stated in the figure legends, the control and drug application traces are from the same cell, both in figure 3 and figure 4, and the scalebar is not included as the amplitudes were normalized for clarity. We have address the effects of dendritic filtering above in answer (5), and cesium blockade above in answer (2). To reiterate, dendritic filtering alone cannot explain our observations, and cesium is often a better choice for blocking HCN channels compared to ZD-7288, which blocks sodium channels as well.

When an excitatory synaptic signal arrives onto a pyramidal cell in typical conditions, neurotransmitter sensitive receptors transmit a synaptic current to the dendritic spine. This dendritic spine is electrically isolated by the high resistance of the spine neck and due to the small membrane surface of the spine, the synaptic current can elicit remarkably large voltage changes. These voltage changes can be large enough to depolarize the spine close to zero millivolts upon even single small inputs (Jayant et al. 2016). Therefore, to state that single inputs arriving to dendritic spines cannot be large enough to recruit NMDA receptor activation is incorrect. This is further exemplified by the substantial literature showing ‘miniature’ NMDA recruitment via stochastic vesicle release alone.

(7) The quality of recordings included in the dataset has concerning variability: for example, resting membrane potentials vary by >15-20 mV and the AP threshold varies by 20 mV in controls. This is indicative of either a very wide range of genetically distinct cell types that the authors are ignoring or the inclusion of cells that are either unhealthy or have bad seals.

Although we are aware of the diversity of L2/3 PCs, resolving further layer depth differences is outside the scope of our current manuscript. However, as shown in Kalmbech et al, resting membrane potential can greatly vary (>15-20 mV) in L2/3 PCs depending on distance from pia. We acknowledge that the variance in AP threshold is large and could be due to genetically distinct cell types.

(8) The authors make no mention of blocking GABAergic signaling, so it must be assumed that it is intact for all experiments. Electrical stimulation can therefore evoke a mixture of excitatory and inhibitory responses, which may well synapse at very different locations, adding to interpretability and variability concerns.

We thank the reviewer for pointing out our lack of detail regarding the GABAergic signaling blocker SR 95531. We did include this drug in our recordings of (50Hz stim.) signal summation, so GABAergic responses did not contaminate our recordings. We now included this information in the results section (page 5) and the methods section (page 15)

(9) The investigation of serotonergic interaction with HCN channels produces modest effect sizes and suffers the same problems as described above.

We do not agree with the reviewer that 50% drop in neuronal AP firing responses (Figure 7b) was a modest effect size. Thus, we opted to keep this data in the manuscript.

(10) The computational modeling is not well described and is not biologically plausible. Persistent and transient K channels are missing. Values for other parameters are not listed. The model does not seem to follow cable theory, which, as described above, is not only implausible but is also not supported by the experimental findings.

The model was downloaded from the Cell Type Database from the Allen Institute, with only minor modifications including the addition of dendritic HCN channels and NDMA receptors- which were varied along a wide parameter space to find a ‘best fit’ to our observations. These additions were necessary to recapitulate our experimental findings. We agree the model likely does not fully recapitulate all aspects of the dendrites, which as we hope to convey in this manuscript, are not fully resolved in mouse L2/3 PCs. This is a previously published neuronal model, and despite its potential shortcomings, is one among a handful of open-source neuronal models of a fully reconstructed L2/3 PC.

Reviewer #2 (Public Review):

Summary:

This paper by Olah et al. uncovers a previously unknown role of HCN channels in shaping synaptic inputs to L2/3 cortical neurons. The authors demonstrate using slice electrophysiology and computational modeling that, unlike layer 5 pyramidal neurons, L2/3 neurons have an enrichment of HCN channels in the proximal dendrites. This location provides a locus of neuromodulation for inputs onto the proximal dendrites from L4 without an influence on distal inputs from L1. The authors use pharmacology to demonstrate the effect of HCN channels on NMDA-mediated synaptic inputs from L4. The authors further demonstrate the developmental time course of HCN function in L2/3 pyramidal neurons. Taken together, this a well-constructed investigation of HCN channel function and the consequences of these channels on synaptic integration in L2/3 pyramidal neurons.

Strengths:

The authors use careful, well-constrained experiments using multiple pharmacological agents to asses HCN channel contributions to synaptic integrations. The authors also use a voltage clamp to directly measure the current through HCN channels across developmental ages. The authors also provide supplemental data showing that their observation is consistent across multiple areas of the cerebral cortex.

Weaknesses:

The gradient of the HCN channel function is based almost exclusively on changes in EPSP width measured at the soma. While providing strong evidence for the presence of HCN current in L2/3 neurons, there are space clamp issues related to the use of somatic whole-cell voltage clamps that should be considered in the discussion.

We thank the reviewer for pointing out our careful and well-constrained experiments and for making suggestions. The potential effects of space clamp errors are detailed in the extended explanations under Reviewer 1, Specific points (3).

Reviewer #3 (Public Review):

Summary:

The authors study the function of HCN channels in L2/3 pyramidal neurons, employing somatic whole-cell recordings in acute slices of visual cortex in adult mice and a bevy of technically challenging techniques. Their primary claim is a non-uniform HCN distribution across the dendritic arbor with a greater density closer to the soma (roughly opposite of the gradient found in L5 PT-type neurons). The second major claim is that multiple sources of long-range excitatory input (cortical and thalamic) are differentially affected by the HCN distribution. They further describe an interesting interplay of NMDAR and HCN, serotonergic modulation of HCN, and compare HCN-related properties at 1, 2 and 6 weeks of age. Several results are supported by biophysical simulations.

Strengths:

The authors collected data from both male and female mice, at an age (6-10 weeks) that permits comparison with in vivo studies, in sufficient numbers for each condition, and they collected a good number of data points for almost all figure panels. This is all the more positive, considering the demanding nature of multi-electrode recording configurations and pipette-perfusion. The main strength of the study is the question and focus.

Weaknesses:

Unfortunately, in its present form, the main claims are not adequately supported by the experimental evidence: primarily because the evidence is indirect and circumstantial, but also because multiple unusual experimental choices (along with poor presentation of results) undermine the reader's confidence. Additionally, the authors overstate the novelty of certain results and fail to cite important related publications. Some of these weaknesses can be addressed by improved analysis and statistics, resolving inconsistent data across figures, reorganizing/improving figure panels, more complete methods, improved citations, and proofreading. In particular, given the emphasis on EPSPs, the primary data (for example EPSPs, overlaid conditions) should be shown much more.

However, on the experimental side, addressing the reviewer's concerns would require a very substantial additional effort: direct measurement of HCN density at different points in the dendritic arbor and soma; the internal solution chosen here (K-gluconate) is reported to inhibit HCN; bath-applied cesium at the concentrations used blocks multiple potassium channels, i.e. is not selective for HCN (the fact that the more selective blocker ZD7288 was used in a subset of experiments makes the choice of Cs+ as the primary blocker all the more curious); pathway-specific synaptic stimulation, for example via optogenetic activation of specific long-range inputs, to complement / support / verify the layer-specific electrical stimulation.

We thank the reviewer for their very careful examination of our manuscript and helpful suggestions. We addressed the concerns raised in the review and presented more raw traces in our figures. Although direct dendritic HCN mapping measurements are outside the scope of the current manuscript due to the morphological constraints presented by L2/3 PCs (which explains why no other full dendritic nonlinearity distribution has been described in L2/3 PCs with this method), we nonetheless supplemented our manuscript with additional suggested experiments as suggested. For example, we included the excellent suggestion of pathway-specific optogenetic stimulation to further validate the disparate effect of HCN channels for distal and proximal inputs. We agree that ZD-7288 is a widely accepted blocker of HCN channels. However, the off-target effects on sodium channels may have significantly confounded our measurements of AP output using extracellular stimulation. Therefore, we chose low concentration cesium as the primary blocker for those experiments, but now validated several other Cs⁺-based results with ZD-7288 as well.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

I have some issues that need clarification or correction.

(1) On page 3, line 90, the authors state "We found that bath application of Cs+ (1mM)..." but the methods and Figure 1 state "2mM Cs+". Please check and correct.

Correct, typo corrected.

(2) Related to Cs+ application, the methods state that "CsMeSO4 (2mM) was bath applied..." Is this correct? CsMeSO4 is typically used intracellularly while CsCl is used extracellularly. If so, please justify. If not, please correct.

It is correct. The justification for not using CsCl selectively extracellularly is that introducing intracellular chloride ions can significantly alter basic biophysical properties, unrelated to the cesium effect. However, no similar distinction has been made for CsMeSO4, which would exclude the use of this drug extracellularly.

(3) The authors normalize the current injections by cell capacitance (pA/pF). Was this done because there is a significant variance in cell morphology? A bit of justification for why the authors chose to normalize the current injection this way would help. If there is significant variation in cell capacitance across cells (or developmental ages), the authors could also include these data.

Indeed, we choose to normalize current injection to cellular capacitance due to the markedly different morphology of deep and superficial L2/3 PCs. Deeper L2/3 PCs have a pronounced apical branch, closely resembling other pyramidal cell types such as L5 PCs, while superficial L2/3 PC lack a thick main apical branch and instead are equipped with multiple, thinner apical dendrites. This morphological variation would yield an inherent bias in several of the reported measurements, therefore we corrected for it by normalizing current injection to cellular capacitance, similar to our previous recent publications (Olah, Goettemoeller et al., 2022, Goettemoeller et al. 2024, Kumar et al. 2024).

(4) On page 15, line 445, the section heading is "PV cell NEURON modeling". Is this a typo? The models are of L2/3 pyramidal neurons, correct?  

Correct, typo corrected.

(5) Figures 3F and 3I are plots of the voltage integral for different inputs before and after Cs+. The y-axis label units are "pA*ms". This should be "mV*ms" for a voltage integral.  

Correct, typo corrected.

(6) On page 9, line 273, the text reads "Voltage clamp experiments revealed that the rectification of steady-state voltage responses to hyperpolarizing current injection was amplified with 5-CT (Fig. 7c)". Both the text and Figure 7C describe current clamp, not voltage clamp, recordings. Please check and correct.

Correct, typo corrected.

(7) Figure 2i looks to be a normalized conductance vs voltage (i.e. activation) plot. The y-axis shows 0-1 but the units are in nS. Is that a coincidence or an error?

Correct, typo corrected.

Reviewer #3 (Recommendations For The Authors):

This is your paper. My comments are my own opinion, I don't expect you to agree or to respond. But I hope that what I wrote below will help you to understand my perspective.

Please pardon my directness (and sheer volume) in this section - I have a lot of notes/thoughts and hope you may find some of them helpful. My high-level comments are unfortunately rather critical, and in (small) part that is because I encountered too many errors/typos/ambiguities in figures, legend, and text. I expect many would be caught with good proofreading, but uncorrected caused confusion on my part, or an inability to interpret your figures with confidence, given some ambiguity.

The paper reads a bit like patchwork - likely a result of many "helpful" reviewers who came before me. Consider starting with and focusing on the synaptic findings, expanding the number of figures and panels dedicated to that, showing example traces for all conditions, and giving yourself the space to portray these complex experiments and results. While I'm not a fan of a large number of supplemental figures, I feel you could move the "extra" results to the supplementals to improve the focus and get right to the meat of it.

For me, the main concern is that the evidence you present for the non-uniform HCN distribution is rather indirect. Ideally, I'd like to see patch recordings from various dendritic locations (as others have done in rats, at least; I'm not sure if L2/3 mice have had such conductance density measurements made in basal and apical dendrites). Otherwise, perhaps optical mapping, either functional or via staining. I also mention some concerns about the choice of internal and cesium. More generally, I want to see more primary data (traces), in particular for the big synaptic findings (non-uniform, L1-vs-L4 differences, NMDAR).

We thank the reviewer for the helpful suggestions. Indeed, direct patch clamp recording is widely considered to be the best method to identify dendritic ion channel distribution, however, we choose an in silico approach instead, for several reasons. Undoubtedly, one of the main reasons to omit direct dendritic recordings was that due to the uniquely narrow apical dendrites this method is extremely challenging, with no previous examples in the literature where isolated dendritic outside-out patch recordings were achieved from this cell type. However, there are theoretical considerations as well. In primates, it has been demonstrated that HCN1 channels are concentrated on dendritic spines (Datta et al., 2023) therefore direct outside-out recordings are not adequate in these circumstances. In future experiments we could directly target L2/3 PC dendrites for outside out recordings in order to resolve dendritic nonlinearity distribution, although a cell-attached methodology may be better suited due to the HCN biophysical properties being closely regulated by intracellular signaling pathways.

The introduction and Figures 1 and 2 are not so interesting and not entirely accurate: L2/3 do not have "abundant" HCN, nor is there an actual controversy about whether they have HCN. It's been clear (published) for years that they have about the same as all other non-PT neocortical pyramidal neurons (see e.g. Larkum 2007; Sheets 2011). Your own Figure 1A has a logarithmic scale and shows L2/3 as having the lowest expression (?) of all pyramidals and roughly 10x lower than L5 PT, but the text says "comparable", which is misleading.

We thank the reviewer for this comment. Although there are sporadic reports in the literature about the HCN content of L2/3 PCs, most of these publications arrive to the same conclusion from the negligible sag potential (as the mentioned Larkum et al., 2007 publication); namely that L2/3 PCs do not contain significant amount of HCN channels. We have shown with voltage and current clamp recordings that this assumption is false, as sag potential is not a reliable indicator of HCN content in L2/3 PCs. With the term “controversial” we aimed to highlight the different conclusions of functional investigations (e.g. Sheets et al., 2011) and sag potential recordings (e.g. Larkum et al., 2007), regarding the importance of HCN channels in L2/3 PCs.

Non-uniform HCN with distal lower density has already been published for a (rare) pyramidal neuron in CA1 (Bullis 2007), similar to what you found in L2/3, and different from the main CA1 population.

We thank the reviewer for this suggestion. We have now included the mentioned citation in the introduction section (page 3).

Express sag as a ratio or percentage, consistently. Figure out why in Figure 7 the average sag ratio is 0.02 while in Fig. S1 it is 0.07 (for V1) - that is a massive difference.

The calculation of sag ratio is consistent across the manuscript (at -6pA.pF), except for experiments depicted in Fig. 7 where sag ratio was calculated from -2pA/pF steps. Explanation below:

Sag should be measured at a common membrane potential, with each neuron receiving a current pulse appropriate to reach that potential. Your approach of capacitance-based may allow for the same, but it is not clear which responses are used to calculate a single sag value per cell (as in Figure 2d).

Thank you, we now included this info in the methods section. Sag potential was measured at the -6 pA/pF step peak voltage, except for Fig. 7 as noted above. We have now included this discrepancy detail in the methods section (page 14 ). These recordings in Fig. 7 took significantly longer than any other recording in the manuscript, as it took a considerable time to reach steady-state response from 5-CT application. -6pA/pF is a current injection in the range of 400-800 pA, which was proven to be too severe for continued application in cells after more than an hour of recording. Accordingly, we decided to lower the hyperpolarizing current step in these recordings. The absolute value of sag is thus different in Fig. 7, but nonetheless the 5-CT effect was still significant. Notably, we probably wouldn’t have noticed the small sag in L2/3 here (and thus the entire study), save for the fact that we looked at -6pA/pF to begin.

In a paper focused on HCN, I would have liked to see resonance curves in the passive characterization.

We thank the reviewer for the suggestion. Resonance curves can indeed provide useful insights into the impact of HCN on a cell’s physiological behavior, however, these experiments are outside the scope of our current manuscript as without in vivo recordings, resonance curves do not contribute to the manuscript in our opinion.

How did you identify L2/3? Did you target cells in L2 or L3 or in the middle, or did you sample across the full layer width for each condition? A quantitative diagram showing where you patched (soma) and where you stimulated (L1, L4) with actual measurements, would be helpful (supplemental perhaps). You mention in the text that some L2/3 don't have a tuft, suggesting some variability in morphology - some info on this would be useful, i.e. since you did fill at least some of the neurons (eg 3A), how similar/different are the dendritic arbors?

We sampled the entire L2/3 region during our recordings. It has been published that deep and superficial L2/3  PCs are markedly different in their morphology, and a recent publication (Brandelise et al. 2023) has even separated these two subpopulations to broad-tufted and slender tufted pyramidal cells, which receive distinct subcortical inputs. Although this differentiation opens exciting avenues for future research, examining potential layer gradients in our dataset would warrant significantly higher sample numbers and is currently out of the scope of our manuscript.

Distal vs proximal: this could use more clarification, considering how central it is to your results. What about a synapse on a basal dendrite, but 150 or 200 um from the soma, is that considered proximal? Is the distance to the soma you report measured along the 3D dendrite, along the 2D dendrite, as a straight line to the soma, or just relative to some layers or cortical markers? (I apologize if I missed this).

We thank the reviewer for pointing out the missing description in the results section. We have amended this oversight (p15).  Furthermore, although deeper L3 PCs have characteristic apical and basal dendritic branches, when recordings were made from more superficial L2 cells, a large portion of their dendrites extended radially, which made their classification ambiguous. Therefore, we did not use “apical” and “basal” terminology in the paper to avoid confusion. Distances were measured along the 3D reconstructed surface of the recovered pyramidal cells. This information is now included in the methods.

Line 445, "PV cell NEURON modeling" ... hmm. Everyone re-uses methods sections to some degree, but this is not confidence-inspiring, and also not from a proofreading perspective.

We have corrected the typo.

It seems that you constructed a new HCN NEURON mechanism when several have been published/reviewed already. Please explain your reasons or at least comment on the differences.

There are slight differences in our model compared to previously published models. Nevertheless, we took a previously published HCN model as a base (Gasparini et al, 2004), and created our own model to fit our whole-cell voltage clamp recordings.

Bath-applied Cs+ can change synaptic transmission (in the hippocampus; Chevaleyre 2002). But also ZD7288 has some such effects. Also, see (Harris 1995) for a Cs+ and ZD7288 comparison. As well as (Harris 1994) for more Cs+ side-effects (it broadens APs, etc). Bath-applied blockers may affect both long-range and local synapses in your recordings, via K-channels or perhaps presynaptic HCN (though I am aware of your Fig. 1e). Since you can do intracellular perfusion, you could apply ZD7288 postsynaptically (Sheets 2011), an elegant solution.

We thank the reviewer for the suggestion. We were aware of the potential presynaptic effects of cesium (i.e., presynaptic Kv or other channel effects) and did measure PPR after cesium application (Fig. 1h), noting no effect. At Cs⁺ concentrations used here, we now also include new data in the results showing no effect on somatically recorded AP waveform (i.e., representative of a Kv channel effect). As stated earlier for reviewer 1, we now performed additional experiments using either cesium or ZD-7288 for comparison (e.g., see updated Fig. 1; Supplementary Figure 1; Fig. 3b-e). Intracellular ZD re-perfusion is an elegant solution which we will absolutely consider in future experiments.

K-Gluconate is reported to inhibit Ih (Velumian 1997), consider at least some control experiments with a different internal for the main synaptic finding - maybe you'll find no big change ...

We thank the reviewer for the suggestion. Although K-Gluconate can inhibit HCN current, the use of this intracellular solution is often used in the literature to measure this current (Huang & Trussel 2014). We have chosen this intracellular solution to improve recording stability.  

(Biel 2009) is a very comprehensive HCN review, you may find it useful.

We thank the reviewer for bringing this to our attention, we have now included the citation in the introduction.

"Hidden" in your title seems too much.

We changed the title to more accurately describe our findings and removed ‘hidden’.

While I'm glad you didn't record at room temperature, the choice of 30C seems a bit unfortunate - if you go to the trouble to heat the bath, why not at least 34C, which is reasonably standard as an approximation for physiological temperature?

We thank the reviewer for pointing this out. The choice of 30C was made to approach physiological temperature levels, while preserving the slices for extended amounts of time which is a standard approach. Future experiments in vivo be performed to further understand the naturalistic relevance at ~37C.

Line 506: do you mean "Hz" here? It's not a frequency, is it? I think it's a unitless ratio?

Correct, we have amended the typo.

Line 95: you have not shown that HCN is "essential" for "excess" AP firing.

We have corrected the phrasing, we agree.

Fig. 2b,c: is this data from a single example neuron, maybe the same neuron as in 2a? Or from all recorded neurons pooled?

The data is from several recorded cells pooled.

Fig. 3 (important figure):

Why did you not use a paired test for panels e and f? You have the same number of neurons for each condition and the expectation is that you record each neuron in control and then in cesium condition, which would be a paired comparison. Or did you record only 1 condition per neuron?

This figure presents your main finding (in my opinion). You should show examples of the synaptic responses, i.e. raw traces, for each condition and panel, and overlaid in such a way that the reader can immediately see the relevant comparison - it's worth the space it requires.

We thank the reviewer for the suggestions. Traces are only overlaid in the paper when they come from the same cell. For Fig. 3d-i, EPSPs in every neuron were evoked in 2-3 different locations (i.e., 1-2 ‘L4’ locations for Type-I and Type-II synapses, and one ‘L1’ location in each) with the same stimulation pipette and one pharmacological condition per cell. Therefore two-sample t-test were used since the control and cesium conditions came from separate cells (i.e., separate observations). This was necessary, as we can never assume that the stimulating electrode can return back to the same synapse after moving it. We were not comfortable with showing overlaid traces from different cells, however, we did show representative traces from control and the Cs⁺ conditions in Fig. 3h. Complementary ZD-7288 experiments can be found on panel b and c, where we did perform within-cell pharmacology (and thus used paired t-tests) from one stimulation area/cell. We hope these complementary experiments increase overall confidence as neither pharmacological approach is 100% without off-target effects. We now also included more overlaid traces where appropriate (i.e., Fig. 3b, and in the new  Fig. 3k experiments using within-cell pharmacology comparisons). We do realize these complementary approaches could cause confusion to the reader, and have now done our best to make the slightly different approaches in this Figure clearer in the results section.

Consider repeating at least some of these critical experiments with ZD7288 instead of Cs+ (and not K-gluc), or even with ZD7288 pipette perfusion, if it's technically feasible here.

We thank the reviewer for the suggestions. Although many of our recordings using Cs⁺ already had complementary experiments (such as synaptic experiments Figure 3e vs Figure 3b), we recognize the need to extend the manuscript with more ZD-7288 experiments. We have now extended Figure 1 with three panels (Figure 1 c,d,e), which recapitulates a fundamental finding, the change in overall excitability upon HCN channel blockade, using ZD-7288 as well.

Fig. 3a, why show a schematic (and weirdly scaled) stimulating electrode? Don't you have a BF photo showing the actual stimulating electrode, which you could trace to scale or overlay? Could you use this panel to indicate what counts as "distal" and what as "proximal", visually?

The stimulating electrode was unfortunately not filled with florescent materials, therefore it was not captured during the z-stack.

Fig. 3b: is the y-axis labeled correctly? A "100% change" would mean a doubling, but based on the data points here I think y=100% means "no change"?

The scale is labeled correctly, 100% means doubling.

Fig. 3b, c: again, show traces representing distal and proximal, not just one example (without telling us how far it was). And use those traces to illustrate the half-width measurement, which may be non-trivial.

We have extended Figure 3b with an inset showing the effect of ZD-7288 on a proximal stimulating site. The legend now includes additional information indicating stimulating location 28 µm away from the soma in control conditions (black trace) and upon Z-7288 application (green trace).  

Line 543, 549: it seems you swapped labels "h" and "i"?

Typo corrected.

Fig. 4b: to me, MK-801 only *partially* blocks amplification, but in the text L198 you write "abolish".

We thank the reviewer for pointing this out. Indeed, there are several other subthreshold mechanisms that are still intact after pipette perfusion, which can cause amplification. We have now clarified this in the text (p7).

Fig. 4e,f: what is the message? Uniform NMDAR? The red asterisk in (e) is at a proximal/distal ratio of roughly 1. I don't understand the meaning of the asterisk (the legend is too basic) and I'm surprised to see a ratio of 1 as the best fit, and also that the red asterisk is at a dendritic distance of 0 um in (f). This could use more explanation (if you feel it's relevant).

We thank the reviewer for pointing this out. We have now included a better explanation in the results and figure legend. We have also updated the figure to make it clearer and added model traces in Fig. 4f, which correspond to example data from slices in Fig. 4g (both green). The graph suggests nonuniform, proximally abundant NMDA distribution. The color coding corresponds to the proximal EPSP halfwidth divided by distal EPSP halfwidth. It is true that the dendritic distance ‘center’ was best-fit very close to the soma, but also note the dispersion (distribution) half-width was >150mm, so there is quite a significant dendritic spread despite the proximal bias prediction. Based on this model there is likely NMDA spread throughout the entire dendrite, but biased proximally. Naturally, future work will need to map this at the spine level so this is currently an oversimplification. Nonetheless, a proximal NMDA bias was necessary to recapitulate findings from Fig. 3, and additional slice recordings in Fig. 4 were consistent with this interpretation.

Fig. 4g: I feel your choice of which traces to overlay is focusing on the wrong question. As the reader, what I want to see here is an overlay of all 4 conditions for one pathway. If this is a sequential recording in a single cell (Cs, Cs+MK801, wash out Cs, MK801), then the overlay would be ideal and need not be scaled. Otherwise, you can scale it. But the L1/L4 comparison does not seem appropriate to me. I find myself trying to imagine what all the dark lines would look like overlaid, and all the light lines overlaid separately. Also, the time axis is missing from this panel. Consider a subtraction of traces (if appropriate).

In these recordings, all EPSPs cells were measured using a stimulating electrode that was moved between L1 and L4 (only once, to keep the exact input consistent) to measure the different inputs in a single neuron. In separate sets of experiments, the same method was used but in the presence of Cs⁺, Cs⁺ + MK-801, or MK-801 alone. This was the most controlled method in our hands for this type of approach, as drug wash outs were either impractical or not possible.  Overlaying four traces would have presented a more cluttered image, and were not actually performed experimentally. As our aim was to resolve the proximal-distal halfwidth relationship, therefore we deemed the within-cell L1 vs. L4 comparison appropriate. We have nonetheless added model traces in Fig. 4f, which correspond to example data from slices in Fig. 4g (both green). The bar graphs should serve also serve to illustrate the input-specific  relationship- i.e., that the only time the L1 and L4 EPSP relationship was inverted was in the presence of Cs⁺ (green bars) and that this effect was occluded with simultaneous MK-801 in the pipette (red bars).

Line 579: should "hyperpolarized" be depolarized?

Corrected

Fig. 5a: it looks like the HCN density is high in the most basal dendrites (black curve above), then drops towards the soma, then rises again in the apicals (red curve). Is that indeed how the density was modeled? If so, this is completely at odds with the impression I received from reading your text and experimental data - there, "proximal" seems to mean where the L4 axons are, and "distal" seems to mean where the L1 axons are, in other words, high HCN towards the pia and low HCN towards the white matter. But this diagram suggests a biphasic hill-valley-hill distribution of HCN (meaning there is a second "distal" region below the soma). In that case, would the laterally-distant basal dendrites also be considered distal? How does the model implement the distribution - is it 1D, 2D or 3D? As you can probably tell, this figure raised more questions for me and made me wonder why I don't have a better understanding yet of your definitions.

We thank the reviewer for pointing this out. We agree our initial cartoon of the parameter fitting procedure was not accurate and should have just been depicted a single ‘curve’. We have now simplified it to better demonstrate what the model is testing, and also made the terms more consistent and accurate. There is no ‘second’ region in the model. We hope this better illustrates it now. We also edited the legend to be clearer. Because the model description in Fig. 4d suffered from similar shortcomings, we also modified it accordingly as well as the figure legend there.

Fig. 5b: why is the best fit at a proximal/distal ratio of 1, yet sigma is 50 um?

Proximal/distal bias on this figure was fitted to 0.985 (prox/distal ratio) as we modeled control conditions, with intact NDMA and HCN channels,  which closely approximated the control recording comparisons.

Fig. 6h, Line 662: "vs CsMeSO4 ... for putative LGN events" The panel shows proximal vs distal, not control vs Cs+. What's going on here?

Typo corrected.

Fig. 7e: the ctrl sag ratio here averages 0.02, while in Fig. S1 the average (for V1 and others) is about 0.07.  Please refer to our answer given to the previous question regarding sag ratio measurements. Briefly, recordings made with 5-CT application were made using a less severe, -2 pA/pF current injection to test seg responses. This more modest hyperpolarization activated less HCN channels, therefore the sag ratio is lower compared to previously reported datapoints.

We have included this explanation in the methods section (page 14)

Now hear you are using a paired test for this pharmacology, but you didn't previously (see my earlier comments/questions).

Paired t-test were used for these experiments as these control and test datapoints came from the same cell. Cells were recorded in control conditions, and after drug application.

Line 137: single-axon activation: but cortical axons make multi-synaptic contacts, at least for certain types of pre- and post-synaptic neurons, and (e.g. in L5-L5 pairs) those contacts can be distributed across the entire dendritic arbor. In other words, it's possible that when you stimulate in L1, you activate local axons, and the signal could then propagate to multiple synaptic contact locations, some being distal and some proximal. Maybe you have reasons to believe you're able to avoid this?

We thank the reviewer for this question. Cortical axons often make distributed contacts, however, top-down and bottom-up pathways innervating L2/3 PCs are at least somewhat restricted to L2/3/L4 and L1, respectively (Shen et al. 2022, Sermet et al. 2019). Therefore, due to the lack evidence suggesting a heavily mixed topographical distribution for top-down and bottom-up inputs, we have reason to believe that L1 stimulation will result in mainly distal input recruitment, while L4 stimulation will mainly excite proximal dendritic regions. The resolution of our experiments was also improved by the minimal stimulation and visual guidance (subset of experiments) of the stimulation. Furthermore, new optogenetic experiments stimulating LGN and LM axons, which have been anatomically defined previously as biased to deeper layers and L1, respectively, were now also performed (Fig. 3j-l) with analogous cesium effects as our local electrical stimulation experiments. Future work using varying optogenetic stimulation parameters will expand on this.

L140: "previous reports" ==> citation needed.

We have inserted the citation needed.

L149: "arriving to layer 1"; but I think earlier you noted that some or many L2/3 neurons lack a dendritic tuft; do they all nevertheless have dendrites in L1? Note that cortico-cortical long-range axons still need to pass through all cortical layers on their way up to L1.

We thank the reviewer for the question. Although the more superficial L2/3 PCs lack distinct apical tuft, their dendrites reach the pia similarly to deeper L2/3 PCs. All of our recorded and post-hoc recovered cells had dendrites in L1, except in cases where they were clearly cut during the slicing procedure, which cells were occluded from the study.

When you write "L4 axons" or "L4 inputs", do you specifically mean long-range thalamic axons? Or axons from local L4 neurons? What about axons in L4 that originate from L5 pyramidal neurons?

In case of ‘L4’ axons, we cannot disambiguate these inputs a priori, as they are both part of the bottom-up pathway, and are possibly experimentally indistinguishable. Even with restricted opto LGN stimulation, disynaptic inputs via L4 PCs cannot be completely ruled out under our conditions. On the other hand, the probability of L5 PC axons to terminate on L2/3 PCs is exceedingly low (single reported connection out of 1145 potential connections; Hage et al. 2022). We did find two clearly different synaptic subpopulations (Supp. Fig 3) in L4- which was tempting to classify as one or the other. However we felt there was not enough evidence in the literature as well as our additional optogenetic experiments to make a classification on the source of these different L4 inputs. Thus we deemed them as Type-I or Type-II for now.

Do you inject more holding current to compensate for the resting membrane potential when Cs+ or ZD7288 is in the bath?

We thank the reviewer for the question. We did not inject a compensatory current, as we wanted to investigate the dual, physiologically relevant action of HCN channels (George et al. 2009)

I'd like to see distributions (histograms) of L4 and L1 EPSP amplitudes, under control conditions and ideally also under HCN block.

We have now extended the manuscript with a supplementary figure (Supplementary Figure 6) to show that EPSP peak was not distance dependent in control conditions, and there was no relationship between peak and halfwidth in our dataset.

Line 186, custom pipette perfusion: why not use this for internal ZD7288, to make it cell-specific?

We thank the reviewer for the question, this is a good point. In future work we will consider this when applicable. It is certainly a way to control for bath application confounds in many ways.

L205: "recapitulate our experimental findings" - which findings do you mean? I think a bit of explanation/referencing would help.

Corrected.

Line 210: L4-evoked were narrower than L1-evoked: is this not expected based on filtering?

We thank the reviewer for pointing this out, the word “Intriguingly” has been omitted.

Line 231 and 235: "in L5 PCs" should be restricted to L5 PT-type PCs.

We have corrected this throughout the manuscript.

Neuromodulation, Fig. 7, L263-282: the neuromodulation finding is interesting. However, a bit like the developmental figure, it feels "tacked on" and the transition feels a bit awkward. I think you may want to discuss/cite more of the existing literature on neuromodulatory interactions with HCN (not just L2/3). Most importantly, what I feel is missing is a connection to your main finding, namely L1 and L4 inputs. Does serotonergic neuromodulation put L1 and L4 back on equal footing, or does it exaggerate the differences?

We thank the reviewer for the question. We agree with the reviewer that Figure 7 does not give a complete picture about how the adult brain can capitalize on this channel distribution, as our intention was to show that HCN channels are not a stationary feature of L2/3 PC, but a feature which can be regulated developmentally and even in the adult brain via neuromodulation. In other words, the subthreshold NMDA boosting we observed can be gated by HCN, depending on developmental stage and/or neuromodulatory state of the system. We have now added some brief language to better introduce the transition and its relevance to the current study in the results (p8), and discussed the implications in the discussion section of the original manuscript.

General comment: different types/sources of synapses may have different EPSP kinetics. I feel this is not mentioned/discussed adequately, considering your emphasis on EPSPs/HCN.

See points above on input-specific synaptic diversity.

Line 319/320: enriched distal HCN is found in L5 PT-type, not in all L5 PCs.

Corrected

L320: CA1 reportedly has a subset of pyramidal neurons that have higher proximal HCN than distal (I gave the citation above). In light of that, I think "unprecedented" is an overstatement.

Corrected.

Methods:

L367: What form of anesthesia was used?

Amended.

Which brain areas, and how?

Amended.

Why did you first hold slices at 34C, but during recording hold at 30C?

We held the slices at 34C to accelerate the degradation of superficial damaged parts of the slice, which is in line with currently used acute slice preparation methodologies, regardless of the subsequent recording temperature.

Pipette resistance/tip size?

Amended.

Cell-attached recordings (L385): provide details of recordings. What was the command potential (fixed value, or did you adjust it per neuron by some criteria)?

Amended.

What type of stimulating electrode did you use? If glass, what solution is inside, and what tip size?

We thank the reviewer for pointing these out, the specific points were added to the methods section.

L392/393: you adjusted the holding (bias) current to sit at -80 mV. What were the range and max values of holding current? Was -80 mV the "raw" potential, or did it account for liquid junction? If you did not account for liquid junction potential, then would -80 in your hands effectively be between -95 and -90 mV? That seems unusually hyperpolarized.

All cells were held with bias holding currents between -50 pA and 150 pA. To be clear, as mentioned below, we did not change the bias current after any drug applications. We did not correct for liquid junction potential, and cells were ‘held‘ with bias current at -80 mV as during our recordings, as 1) this value was apparently close to the RMP (i.e. little bias current needed at this voltage on average) (Fig. 2e) and 2) to keep consistent conditions across recordings. The uncorrected -80 mV is in the range of previously reported membrane potential values both in vivo and in vitro (Svoboda et al. 1999, Oswald et al. 2008, Luo et al. 2017), which found the (corrected) RMP to be below -80mV. Naturally this will not reflect every in vivo condition completely and further investigation using naturalistic conditions in the future are warranted.  

Did you adjust the bias current during/after pharmacology?

Bias current was not adjusted in order to resolve the effect on resting membrane potential.

L398: sag calculation could use better explanation: how did you combine/analyze multiple steps from a single neuron when calculating sag? Did you choose one level (how) or did you average across step sizes or ...?

Sag ratio was measured at -6 pA/pF current step except for one set of experiments in Fig. 7. Methods section was amended.

L400, 401: 10 uM Alexa-594 or 30 um Alexa-594, which is correct?

10 µM is correct, typo was corrected

L445: "PV cell" seems like a typo?

Typo is corrected.

L450: "altered", please describe the algorithm or manual process.

Alterations were made manually.

L474: NDMA, typo.

Typo is fixed.

L474: "were adjusted", again please describe the process.

Adjustments were made by a grid-search algorithm.

Biel, M., Wahl-Schott, C., Michalakis, S., & Zong, X. (2009). Hyperpolarization-activated cation channels: from genes to function. Physiological reviews, 89(3), 847-885. https://journals.physiology.org/doi/full/10.1152/physrev.00029.2008 - (very comprehensive review of HCN)

Bullis JB, Jones TD, Poolos NP. Reversed somatodendritic I(h) gradient in a class of rat hippocampal neurons with pyramidal morphology. J Physiol. 2007 Mar 1;579(Pt 2):431-43. doi: 10.1113/jphysiol.2006.123836. Epub 2006 Dec 21. PMID: 17185334; PMCID: PMC2075407. https://physoc.onlinelibrary.wiley.com/doi/full/10.1113/jphysiol.2006.123836 - (CA1 subset (PLPs) have a reversed HCN gradient; cell-attached patches, NMDAR)

Velumian AA, Zhang L, Pennefather P, Carlen PL. Reversible inhibition of IK, IAHP, Ih, and ICa currents by internally applied gluconate in rat hippocampal pyramidal neurones. Pflugers Arch. 1997 Jan;433(3):343-50. doi: 10.1007/s004240050286. PMID: 9064651. https://link.springer.com/article/10.1007/s004240050286 - (K-Gluc internal inhibits HCN)

Sheets, P. L., Suter, B. A., Kiritani, T., Chan, C. S., Surmeier, D. J., & Shepherd, G. M. (2011). Corticospinal-specific HCN expression in mouse motor cortex: I h-dependent synaptic integration as a candidate microcircuit mechanism involved in motor control. Journal of neurophysiology, 106(5), 2216-2231. https://journals.physiology.org/doi/full/10.1152/jn.00232.2011 - (L2/3 IT have same sag ratio as all other non-PT pyramidals, roughly 5% (vs 20% PT); intracellular ZD7288 used at 10 or 25 um)

Harris NC, Constanti A. Mechanism of block by ZD 7288 of the hyperpolarization-activated inward rectifying current in guinea pig substantia nigra neurons in vitro. J Neurophysiol. 1995 Dec;74(6):2366-78. doi: 10.1152/jn.1995.74.6.2366. PMID: 8747199. https://journals.physiology.org/doi/abs/10.1152/jn.1995.74.6.2366 - (comparison Cs+ and ZD7288)

Harris, N. C., Libri, V., & Constanti, A. (1994). Selective blockade of the hyperpolarization-activated cationic current (Ih) in guinea pig substantia nigra pars compacta neurones by a novel bradycardic agent, Zeneca ZM 227189. Neuroscience letters, 176(2), 221-225. https://www.sciencedirect.com/science/article/abs/pii/0304394094900876 - (Cs+ is not HCN-selective; it also broadens APs, reduces the AHP)

Chevaleyre, V., & Castillo, P. E. (2002). Assessing the role of Ih channels in synaptic transmission and mossy fiber LTP. Proceedings of the National Academy of Sciences, 99(14), 9538-9543. https://pnas.org/doi/abs/10.1073/pnas.142213199 - (Cs+ blocks K channels, increases transmitter release; but also ZD7288 affects synaptic transmission)

Thank you

Author response:

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

eLife Assessment

The modeling and experimental work described provide solid evidence that this model is capable of qualitatively predicting alterations to the swing and stance phase durations during locomotion at different speeds on intact or split-belt treadmills, but a revision of the figures to overlay the model predictions with the experimental data would facilitate the assessment of this qualitative agreement. This paper will interest neuroscientists studying vertebrate motor systems, including researchers investigating motor dysfunction after spinal cord injury.

Figures showing the overlay of the experimental data with the modeling predictions have been included as figure supplements for Figures 5-7. This highlights how accurate the model predictions were.

Public Reviews:

Reviewer #1 (Public review):

We thank the reviewer for the positive evaluation of our paper and emphasizing its strengths in the Summary.

Weaknesses:

(1) Could the authors provide a statement in the methods or results to clarify whether there were any changes in synaptic weight or other model parameters of the intact model to ensure locomotor activity in the hemisected model?

Such a statement has been inserted in Materials and Methods, section “Modeling”. Also, in the 1st paragraph of section “Spinal sensorimotor network architecture and operation after a lateral spinal hemisection”, we stated that no “additional changes or adjustments” were made.

(2) The authors should remind the reader what the main differences are between state-machine, flexor-driven, and classical half-center regimes (lines 77-79).

Short explanations/reminders have been inserted (see lines 80-83 of tracked changes document).

(3) There may be changes in the wiring of spinal locomotor networks after the hemisection. Yet, without applying any sort of plasticity, the model is able to replicate many of the experimental data. Based on what was experimentally replicated or not, what does the model tell us about possible sites of plasticity after hemisection?

Quantitative correspondence of changes in locomotor characteristics predicted by the model and those obtained experimentally provide additional validation of the model proposed in the preceding paper and used in this paper. This was our ultimate goal. None of the plastic changes during recovery were modeled because of a lack of precise information on these changes. The absence of possible plastic changes may explain the small discrepancies between our simulations and experimental data (see Supplemental Figures that have been added). However, the model only has a simplified description of spinal circuits without motoneurons and without real simulation of leg biomechanics. This limits our analysis or predictions of possible plastic changes within a reasonable degree of speculation. This issue is discussed in section: “Limitations and future directions” in the Discussion. We have also inserted a sentence: “The lack of possible plastic changes in spinal sensorimotor circuits of our model may explain the absence of exact/quantitative correspondences between simulated and experimental data.

(4) Why are the durations on the right hemisected (fast) side similar to results in the full spinal transected model (Rybak et al. 2024)? Is it because the left is in slow mode and so there is not much drive from the left side to the right side even though the latter is still receiving supraspinal drive, as opposed to in the full transection model? (lines 202-203).

This is correct. We have included this explanation in the text (lines 210-211 of tracked changes document).

(5) There is an error with probability (line 280).

This typo was corrected.

Reviewer #2 (Public review):

This is a nice article that presents interesting findings. One main concern is that I don't think the predictions from the simulation are overlaid on the animal data at any point - I understand the match is qualitative, which is fine, but even that is hard to judge without at least one figure overlaying some of the data.

We thank the Reviewer for the constructive comments. Figures showing the overlay of the experimental data with the modeling predictions have been included as figure supplements for Figures 5-7. This highlights how accurate the model predictions were.

Second is that it's not clear how the lateral coupling strengths of the model were trained/set, so it's hard to judge how important this hemi-split-belt paradigm is. The model's predictions match the data qualitatively, which is good; but does the comparison using the hemi-split-belt paradigm not offer any corrections to the model? The discussion points to modeling plasticity after SCI, which could be good, but does that mean the fit here is so good there's no point using the data to refine?

The model has not been trained or retrained, but was used as it was described in the preceding paper. Response: Quantitative correspondence of changes in locomotor characteristics predicted by the model and those obtained experimentally provide additional validation of the model proposed in the preceding paper and used in this paper. This was our ultimate goal. None of the plastic changes during recovery were modeled because of a lack of precise information on these changes. The absence of possible plastic changes may explain the small discrepancies between our simulations and experimental data (see figure supplements that have been added). However, the model only has a simplified description of spinal circuits without motoneurons and without real simulation of leg biomechanics. This limits our analysis or predictions of possible plastic changes within a reasonable degree of speculation. This issue is discussed in section: “Limitations and future directions” in the Discussion.

The manuscript is well-written and interesting. The putative neural circuit mechanisms that the model uncovers are great, if they can be tested in an animal somehow.

We agree and we are considering how we can do this in an animal model.

Page 2, lines 75-6: Perhaps it belongs in the other paper on the model, but it's surprising that in the section on how the model has been revised to have different regimes of operation as speed increases, there is no reference to a lot of past literature on this idea. Just one example would be Koditschek and Full, 1999 JEB Figure 3, where they talk about exactly this idea, or similarly Holmes et al., 2006 SIAM review Figure 7, but obviously many more have put this forward over the years (Daley and Beiwener, etc). It's neat in this model to have it tied down to a detailed neural model that can be compared with the vast cat literature, but the concept of this has been talked about for at least 25+ years. Maybe a review that discusses it should be cited?

We have revised the Introduction to include the suggested references.

Page 2, line 88: While it makes sense to think of the sides as supraspinal vs afferent driven, respectively, what is the added insight from having them coupled laterally in this hemisection model? What does that buy you beyond complete transection (both sides no supra) compared with intact?

We are trying to make one model that could reproduce multiple experimental data in quadrupedal locomotion, including genetic manipulations with (silencing/removal) particular neuron types (and commissural interneurons), as pointed out in the section “Model Description” in the Results. These lateral connections are critical for reproducing and explaining other locomotor behaviors demonstrated experimentally. However, even in this study, these lateral interactions are necessary to maintain left-right coordination and equal left-right frequency (step period) during split-belt locomotion and after hemisection.

I can see how being able to vary cycle frequencies separately of the two limbs is a good "knob" to vary when perturbing the system in order to refine the model. But there isn't a ton of context explaining how the hemi-section with split belt paradigm is important for refining the model, and therefore the science. Is it somehow importantly related to the new "regimes" of operation versus speed idea for the model?  

We did not refine the model in this paper. We just used it for new simulations. The predictions strengthen the organization and operation of the model we recently proposed.

Page 5, line 212: For the predictions from the model, a lot depends on how strong the lateral coupling of the model is, which, in turn, depends on the data the model was trained on. Were the model parameters (especially for lateral coupling of the limbs) trained on data in a context where limbs were pushed out of phase and neuronal connectivity was likely required to bring the limbs back into the same phase relationship? Because if the model had no need for lateral coupling, then it's not so surprising that the hemisected limbs behave like separate limbs, one with surpaspinal intact and one without.

Please see our response above concerning the need for lateral interactions incorporated to the model.

Page 8, line 360: The discussion of the mechanisms (increased influence of afferents, etc) that the model reveals could be causing the changes is exciting, though I'm not sure if there is an animal model where it can be tested in vivo in a moving animal.

We agree it may be difficult to test right now but we are considering experimental approaches.

Page 9, line 395: There are some interesting conclusions that rely on the hemi-split-belt paradigm here.

We agree with this comment. Thanks.

Reviewer #2 (Recommendations for the authors):

Figures: Why aren't there any figures with the simulation results overlaid on the animal data?

We followed this suggestion. Figures showing the overlay of the experimental data with the modeling predictions have been included as figure supplements.

Author response:

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

Reviewer #1 (Public Review):

Summary:

A nice study trying to identify the relationship between E. coli O157 from cattle and humans in Alberta, Canada.

Strengths:

(1) The combined human and animal sampling is a great foundation for this kind of study.

(2) Phylogenetic analyses seem to have been carried out in a high-quality fashion.

Weaknesses:

I think there may be a problem with the selection of the isolates for the primary analysis. This is what I'm thinking:

(1) Transmission analyses are strongly influenced by the sampling frame.

(2) While the authors have randomly selected from their isolate collections, which is fine, the collections themselves are not random.

(3) The animal isolates are likely to represent a broad swathe of diversity, because of the structured sampling of animal reservoirs undertaken (as I understand it).

(4) The human isolates are all from clinical cases. Clinical cases of the disease are likely to be closely related to other clinical cases, because of outbreaks (either detected, or undetected), and the high ascertainment rate for serious infections.

(5) Therefore, taking an equivalent number of animal and clinical isolates, will underestimate the total diversity in the clinical isolates because the sampling of the clinical isolates is less "independent" (in the statistical sense) than sampling from the animal isolates.

(6) This could lead to over-estimating of transmission from cattle to humans.

We appreciate the reviewer’s careful thoughts about our sampling strategy. We agree with points (1) and (2), and we have provided additional details on the animal collections as requested (lines 95-101).

We agree with point (3) in theory but not in fact. As shown in Figure 3, the cattle isolates were very closely related, despite the temporal and geographic breadth of sampling within Alberta. The median SNP distance between cattle sequences was 45 (IQR 36-56), compared to 54 (IQR 43-229) SNPs between human sequences from cases in Alberta during the same years. Additionally, as shown in Figure 2, only clade A and B isolates – clades that diverge substantially from the rest of the tree – were dominated by human cases in Alberta. We have better highlight this evidence in the revision (lines 234-236 and 247-249).

We agree with the reviewer in point (4) that outbreaks can be an important confounder of phylogenetic inference. This is why we down-sampled outbreaks (based on genetic relatedness, not external designation) in our extended analyses. We did not do this in the primary analysis, because there were no large clusters of identical isolates. Figure 3b shows a limited number of small clusters; however, clustered cattle isolates outnumbered clustered human isolates, suggesting that any bias would be in the opposite direction the reviewer suggests. In the revision, we down-sampled all analyses and, indeed, the proportion of human lineages descending from cattle lineages increased (lines 259-261). Regarding severe cases being oversampled among the clinical isolates, this is absolutely true and a limitation of all studies utilizing public health reporting data. We made this limitation to generalizability clearer in the discussion. However, as noted above, clinical isolates were more variable than cattle isolates, so it does not appear to have heavily biased the analysis (lines 490-495).

We disagree with the reviewer on point (5). While the bias toward severe cases could make the human isolates less independent, the relative sampling proportions are likely to induce greater distance between clinical isolates than cattle isolates, which is exactly what we observe (see response to point (3) above). Cattle are E. coli O157:H7’s primary reservoir, and humans are incidental hosts not able to sustain infection chains long-term. Not only is the bacteria prevalent among cattle, cattle are also highly prevalent in Alberta. Thus, even with 89 sampling points, we are still capturing a small proportion of the E. coli O157:H7 in the province. Being able to sample only a small proportion of cattle’s E. coli O157:H7 increases the likelihood of only sampling from the center of the distribution, making extreme cases such as that shown at the very bottom of the tree in Figure 4, rare and important. In comparison, sampling from human cases constitutes a higher proportion of human infections relative to cattle, and is therefore more representative of the underlying distribution, including extremes. We added this point to the limitations (lines 495-504). As with the clustering above, if anything, this outcome would have biased the study away from identifying cattle as the primary reservoir. Additionally, the relatively small proportion of cattle sampled makes our finding that 15.7% of clinical isolates were within 5 SNPs of a cattle isolate, the distance most commonly used to indicate transmission for E. coli O157:H7, all the more remarkable.

Because of the aforementioned points, we disagree with the reviewer’s conclusion in point (6). If a bias exists, we believe transmission from cattle-to-humans is likely underestimated for the reasons given above. Not only do all prior studies indicate ruminants as the primary reservoirs of E. coli O157:H7, and humans as only incidental hosts, our specific data do not support the reviewer’s individual contentions. The results of the sensitivity analysis the reviewer recommended is consistent with the points we outlined above, estimating that 94.3% of human lineages arose from cattle lineages (vs. 88.5% in the primary analysis). We have opted to retain the more conservative estimate of the primary analysis, which includes a more representative number of clinical cases.

(7) We hypothesize that the large proportion of disease associated with local transmission systems is a principal cause of Alberta's high E. coli O157:H7 incidence" - this seems a bit tautological. There is a lot of O157 because there's a lot of transmission. What part of the fact it is local means that it is a principal cause of high incidence? It seems that they've observed a high rate of local transmission, but the reasons for this are not apparent, and hence the cause of Alberta's incidence is not apparent. Would a better conclusion not be that "X% of STEC in Alberta is the result of transmission of local variants"? And then, this poses a question for future epi studies of what the transmission pathway is.

The reviewer is correct, and the suggestion for the direction of future studies was our intent with this statement. We have removed this sentence.

Reviewer #1 (Recommendations For The Authors):

(1) To address my concerns about the different sampling frames in humans and animals, I would suggest a sensitivity analysis, using something like the following strategy. Make a phylogeny of all the available genome sequences from humans and cattle from Alberta. Phylogenetically sub-sample the tree, using something like Treemer (https://github.com/fmenardo/Treemmer), to remove phylogenetically redundant isolates from the same host type. Randomly select 100 human and 100 animal isolates from this non-redundant tree, and re-do your analysis.

Although we originally down-sampled outbreaks for our analysis of the extended Alberta tree (2007-2019), we had not done this systematically for all analyses. We were not able to use the recommended Treemer tool, because we did not see a way to incorporate the timing of sequences. Because the objective of our study was to evaluate persistence, we did not want to exclude identical sequences that were separated in time and thus could be indicating persistence. To accomplish this, we developed a utility that allowed us to incorporate the temporality of sequences. Using this utility, we systematically down-sampled all sequences that met the following conditions: 1) within 0-2 SNPs of another sequence and 2) no gaps in sequence set >2 months. The second condition means that for any set of sequences within 0-2 SNPs of one another, there can be no more than 2 months without a sequence from the set. Similar sequences that occur beyond this 2-month-cutoff would be considered a separate set for down-sampling. This cutoff was chosen based on the epidemiology of E. coli O157 outbreaks, which are generally either point-source or continuous-source outbreaks. Intermittent outbreaks of a single strain are believed to arise from distinct contamination events and are exactly the type of phenomena we are seeking to identify. We have added details on down-sampling to the Methods (lines 178-180).

After down-sampling, our primary analysis included 115 human and 84 cattle isolates. T conduct the recommended sensitivity analysis, we further randomly subsampled the human isolates, selecting 84 to match the number of cattle isolates. As we suggested in our initial response, and contrary to the reviewer’s concern, subsampling in this way accentuated the results, with 94.3% of human lineages inferred as arising from cattle lineages, compared to 88.5% in the primary analysis. This sensitivity analysis also identified 10 of the 11 LPLs identified in the primary analysis. The LPL not identified had 5 isolates in the primary analysis, the minimum for definition as an LPL, and was reduced to 4 isolates through subsampling. This sensitivity analysis is shown in Suppl. Figure S3.

(2) This is the first time I've seen target diagrams used for SNP distances, I'm not sure of their value compared with histograms. They seem to emphasise the maximum distance, rather than the largest number of isolates. I.e. most isolates are closely related, but the diagram emphasises the small number of divergent ones.

In using the target diagrams, we sought to emphasize the bimodal distribution of human-to-closest-cattle SNP differences. However, this is still mostly visible in a histogram, so we have replaced the target diagrams with a histogram as suggested (Figure 3).

(3) L130 - fastqc doesn't trim adapters and read ends, there will be something else like trimmomatic which does.

The reviewer is correct, and we appreciate them catching this error. Trimmomatic is incorporated into the Shovill pipeline, which was the assembler we used through the Bactopia pipeline. We have updated the Methods to indicate this (lines 142-144).

(4) I find the flow of the article a bit confusing. You have your primary analysis, but Figure 2, which is a secondary analysis, comes before Figure 3. Which is the primary analysis? For me, primary analysis results should come first, or at least signpost a bit better.

Figure 2 is not a secondary analysis. It is intended to provide an overview of the isolates used from the phylogenetic perspective, just as the diagram in Figure 1 provides an overview of the isolates by analysis. The secondary analyses are shown in Figures 5-7. We have added a sub-header, “Description of Isolates”, to the section referring to Figure 2, to clarify (line 232).

(5) Locally persistent lineage definition. What is the rationale for the different criteria signifying locally persistent lineages? There is nothing in some of your criteria e.g. all isolates <30 SNPs from each other, which indicates that it is locally persistent - could have been transmitted to Japan (just to pick a place at random), causing a bunch of cases there, and then come back for all we know. Would that be a locally persistent lineage? Did you use the MCC tree here? That is a sub-sample of your full dataset, I am not sure what exactly you're trying to say with the LPLs, but maybe using a larger dataset would be better? Also, there are lots of STEC genomes available from e.g. UK and USA, by only including a fraction of these, you limit the strength of the inferences you can make about locally persistent lineages unless you know that they don't see the G sub-lineage that you observe.

The reviewer raises multiple points here. First, regarding our definition of LPLs, it is intended to identify those lineages that pose a threat to populations in the specific geographic area (“local”) for at least 1 year (“persistent”) that are likely to be harbored in local reservoirs. Each of the criteria contributes to this definition.

(1) A single lineage of the MCC tree with a most recent common ancestor (MRCA) with ≥95% posterior probability: This criterion provides confidence in the given isolates being part of a single, defined lineage. The posterior probability gives the probability that the topology of the tree is accurate, based on the data provided and the chosen model of evolution. In other words, we required at least 95% probability that the lineage was correct, and in practice the posterior probability of the lineages we defined as LPLs was 99.7-100% (we have added this detail to the text, lines 269-270). We also added a sensitivity analysis, shown in Suppl. Figure S4, which shows all sampled trees. We find that the essential structure of the tree around the LPLs we defined is well-supported.

(2) All isolates ≤30 core SNPs from one another: This criterion limited LPLs to those lineages where the isolates were closely related. We did not want to limit LPLs to those that might define an outbreak, for example using a 5-10 SNP threshold, because the point of the study is to identify lineages that persistently cause disease over longer periods than a normal outbreak. Pathogens evolve over time in their reservoirs, leading to greater SNP distances, and we wanted to allow for this. The U.S. CDC has acknowledged a similar concern for such persistent lineages in its definition of REP strains, which it has defined based on ranges of 13-104 allele differences by cgMLST. Thus, our choice of 30 core SNPs as the threshold is in line with current practice in the emerging science on persistence of enteric pathogens. We have also added a sensitivity analysis examining alternate SNP thresholds, shown in Suppl. Figure S5, which results in clusters of LPLs identified in the primary analysis being grouped into larger lineages. Additionally, in the tree showing our primary analysis (Figure 4), we now note the minimum number of SNPs all isolates within the lineage differ by.

(3) Contained at least 1 cattle isolate: This criterion increases confidence that the lineage is indeed “local”. Unlike humans, cattle are not known to be routinely infected by imported food products, and they do not make roundtrip journeys to other locations, as humans infected during travel do. Cattle themselves may be imported into Alberta while infected, and cattle in Alberta can be infected by other imported animals. In these cases, if the STEC strains the cattle harbor persist for ≥1 year, they become the type of lineages we are interested in as LPLs, regardless where they previously came from, because they are now potential persistent sources of infection in Alberta. By including at least one cattle isolate in each LPL, the only way an identified LPL is not actually local is if cattle are imported from the lineage’s reservoir community elsewhere (e.g., in Japan, as the reviewer suggested), the lineage is persisting in that non-Alberta reservoir, and newly infected cattle are imported repeatedly over 1 or more years. This could feasibly explain G(vi)-AB LPL 5 (Figure 4), which is entirely composed of cattle. Indeed, such an explanation would be consistent with the lack of new cases from this LPL after 2015 in the extended analysis (Figure 5). However, for all other LPLs, which contain both cattle and human isolates, for the LPL to not be local, both cattle and human cases would have to be imported from the same non-Alberta reservoir. While this is possible, the probability of such a scenario is low, and it decreases the more isolates are in an LPL. For the average LPL, this means 4 human and 6 cattle cases would need to be imported from a non-Alberta reservoir over several years. Given that our study is only a random sample of the total STEC cases and cattle in Alberta from 2007-2015, these numbers are underestimates of the true absolute number of cases and cattle associated with LPLs that would have to be explained by importation if the LPL were not local. We have added some explanation of the possibility of importation in the Discussion where we discuss the LPL criteria (lines 376-380).

(4) Contained ≥5 isolates: In concert with criterion 3, this criterion guards against anomalies being counted as LPLs. By requiring at least 5 isolates in an LPL after down-sampling, at least 5 infection events must have occurred from the LPL, reducing the likelihood of importation explaining the LPL and emphasizing more significant LPLs.

(5) The isolates were collected at sampling events (for cattle) or reported (for humans) over a period of at least 1 year: This criterion defines the persistence aspect of the LPL. In the primary analysis, the LPLs we identified persisted for an average of 8 years, with the shortest persisting for 5 years (these details have been added to the text, lines 268-269). Incorporating the extended analysis, several LPLs persisted for the full 13 years of the study.

Regarding using additional non-Alberta isolates to help rule out importation, we have expanded the number of U.S. and global isolates included in the importation analysis, over-sampling clade G isolates from the U.S. (Figure 7). As cattle trade is substantially more common with the U.S. than other countries, we felt it most important to focus on the U.S. as a potential source of both imported cattle and human cases. Our results from this analysis show that only 9 of 494 (1.8%) U.S. isolates occurred in the LPLs we defined in the primary analysis, and all occurred after Alberta isolates (lines 313-317). Although we also added more global isolates, we still found that none were associated with the Alberta LPLs.

(6) Given the importance of sampling for a study like this, some more information on animal sampling studies should be included here.

We have added details on the cattle sampling to the Methods (lines 95-101).

(7) L172 - do you mean an MRCA with >- 95% probability of location in Alberta?

Location in Alberta was not determined from the primary analysis, which defined the LPLs, as only Alberta isolates were included in that analysis. As described above, this criterion meant that we required at least 95% probability that the tree topology at the lineage’s MRCA was correct, and in practice the posterior probability of the lineages we defined as LPLs was 99.7-100%.

(8) Need a supplementary figure of just clade G from Figure 2.

We have added a sub-tree diagram of clade G(vi) as Figure 2b.

Reviewer #2 (Public Review):

This study identified multiple locally evolving lineages transmitted between cattle and humans persistently associated with E. coli O157:H7 illnesses for up to 13 years. Furthermore, this study mentions a dramatic shift in the local persistent lineages toward strains with the more virulent stx2a-only profile. The authors hypothesized that this phenomenon is the large proportion of disease associated with local transmission systems is a principal cause of Alberta's high E. coli O157:H7 incidence. These opinions more effectively explain the role of the cattle reservoir in the dynamics of E. coli O157:H7 human infections.

(1) The authors acknowledge the possibility of intermediate hosts or environmental reservoirs playing a role in transmission. Further discussion on the potential roles of other animal species commonly found in Alberta (e.g., sheep, goats, swine) could enhance the understanding of the transmission dynamics. Were isolates from these species available for analysis? If not, the authors should clearly state this limitation.”

We have expanded the discussion of other species in Alberta, as suggested, including other livestock, wildlife, and the potential role of birds and flies (lines 353-360). Unfortunately, we did not have sequences available from other species, which we have added to the limitations (lines 487-490).

(2) The focus on E. coli O157:H7 is understandable given its prominence in Alberta and the availability of historical data. However, a brief discussion on the potential applicability of the findings to non-O157 STEC serogroups, and the limitations therein, would be beneficial. Are there reasons to believe the transmission dynamics would be similar or different for other serogroups?

We appreciate this comment and have expanded our discussion of relevance to non-O157 STEC (lines 452-460). Other authors have proposed that transmission dynamics differ, and studies of STEC risk factors, including our own, support this. However, there has been very little direct study of non-O157 transmission dynamics and there is even less cross-species genomic and metadata available for non-O157 isolates of concern.

(3) The authors briefly mention the need for elucidating local transmission systems to inform management strategies. A more detailed discussion on specific public health interventions that could be targeted at the identified LPLs and their potential reservoirs would strengthen the paper's impact.

We agree with the reviewer that this would be a good addition to the manuscript. The public health implications for control are several and extend to non-STEC reportable zoonotic enteric infections, such as Campylobacter and Salmonella. We have added a discussion of these (lines 460-465, 467-485).

(4) Understanding the relationship between specific risk factors and E. coli O157:H7 infections is essential for developing effective prevention strategies. Have case-control or cohort studies been conducted to assess the correlation between identified risk factors and the incidence of E. coli O157:H7 infections? What methodologies were employed to control for potential confounders in these studies?

Yes, there have been several case-control studies of reported cases. Many of these are referenced in the discussion in terms of the contribution of different sources to infection. As risk factors were not the focus of the current study, we believe a thorough discussion of the literature on the aspects of these various studies is beyond our scope. However, we have added some details on the risk factors themselves (lines 72-79).

(5) The study's findings are noteworthy, particularly in the context of E. coli O157:H7 epidemiology. However, the extent to which these results can be replicated across different temporal and geographical settings remains an open question. It would be constructive for the authors to provide additional data that demonstrate the replication of their sampling and sequencing experiments under varied conditions. This would address concerns regarding the specificity of the observed patterns to the initial study's parameters.

We appreciate the reviewer’s comment, as we are currently building on this analysis with an American dataset with different types of data available than were used in this study. Aligned with this work, we have added a comment on the adaptation of our method to other settings with different types of data (lines 448-450). We also added a sensitivity analysis to the manuscript simulating a different sampling approach (Suppl. Fig. S3), which should be informative to this question.

Reviewer #2 (Recommendations For The Authors):

Minor comments.

(1) Figure 1: The figure is a critical visual representation of the study's findings and should be given prominent emphasis. It is essential that the key discoveries of the research are clearly depicted and explained in this visual format. The authors should ensure that Figure 1 is detailed and informative enough to stand out as a central piece of the study.

Figure 1 is the diagram of sample numbers, locations, and corresponding analyses. We assume that the reviewer means to refer to Figure 2. Although the inclusion of >1,200 isolates makes the tree difficult to see in detail, we have made some modifications to make the findings clearer. First, we changed the clade coloration such that the only subclade differentiated is G(vi). We have removed the stx metadata ring to focus attention on the location and species of the isolates, as stx data are described in Table 1. Finally, we have added a sub-tree diagram of clade G(vi), colored by location. This makes clear the large sections of the subclade dominated by isolates from one location or another, and the limited areas where they overlap.

(2) Figures 2 and 4: While these figures contribute to the presentation of the data, they appear to be somewhat rudimentary in their current form. The lack of detailed annotations regarding the clustering of different strains is a notable omission. I recommend that the authors refine these figures to include comprehensive labeling that clearly delineates the various bacterial clusters. Enhanced graphical representation with clear annotations will aid readers in better understanding the study's findings.

We appreciate this suggestion. We have remade all trees generated by the BEAST 2 analyses in R, rather than FigTree. This has allowed us to annotate the trees with additional information on the LPLs and we believe provides a clearer picture of each LPL.

(3) Supplemental Table S1: The supplemental tables are an excellent opportunity to showcase additional data and findings that support the study's conclusions. For Supplemental Table S1, it is recommended that the authors highlight the innovative aspects or novel discoveries presented in this table.

Suppl. Table S1 shows the modeling specifications and priors used in the analyses. These decisions were not in and of themselves novel. The innovation in our methods is due to the development of the LPLs based on the trees resulting from the analyses detailed in Suppl. Table S1, as well as from the application of these models to E. coli O157:H7 for the first time. However, we understand the reviewers point and have emphasized the importance of the results shown in Suppl. Table S2 (lines 391-395).

(4) Line 35: "We assessed the role of persistent cross-species transmission systems in Alberta's E. coli O157:H7 epidemiology." change to "We assessed the impact of persistent cross-species transmission systems on the epidemiology of E. coli O157:H7 in Alberta."

We have made this change.

(5) To facilitate a deeper understanding of the core findings of the manuscript and to enable the development of effective response strategies, I suggest that the authors provide more information regarding the sequencing data used in the study. This information should at least include aspects such as data accessibility and quality control measures.

We have included a Supplemental Data File that lists all isolates used in the analysis, and the QC measures are detailed in the Methods.

Author response:

Reviewer #1 (Public review):

Summary:

Can a plastic RNN serve as a basis function for learning to estimate value. In previous work this was shown to be the case, with a similar architecture to that proposed here. The learning rule in previous work was back-prop with an objective function that was the TD error function (delta) squared. Such a learning rule is non-local as the changes in weights within the RNN, and from inputs to the RNN depends on the weights from the RNN to the output, which estimates value. This is non-local, and in addition, these weights themselves change over learning. The main idea in this paper is to examine if replacing the values of these non-local changing weights, used for credit assignment, with random fixed weights can still produce similar results to those obtained with complete bp. This random feedback approach is motivated by a similar approach used for deep feed-forward neural networks.

This work shows that this random feedback in credit assignment performs well but is not as well as the precise gradient-based approach. When more constraints due to biological plausibility are imposed performance degrades. These results are not surprising given previous results on random feedback. This work is incomplete because the delay times used were only a few time steps, and it is not clear how well random feedback would operate with longer delays. Additionally, the examples simulated with a single cue and a single reward are overly simplistic and the field should move beyond these exceptionally simple examples.

Strengths:

• The authors show that random feedback can approximate well a model trained with detailed credit assignment.

• The authors simulate several experiments including some with probabilistic reward schedules and show results similar to those obtained with detailed credit assignments as well as in experiments.

• The paper examines the impact of more biologically realistic learning rules and the results are still quite similar to the detailed back-prop model.

Weaknesses:

• The authors also show that an untrained RNN does not perform as well as the trained RNN. However, they never explain what they mean by an untrained RNN. It should be clearly explained. These results are actually surprising. An untrained RNN with enough units and sufficiently large variance of recurrent weights can have a high-dimensionality and generate a complete or nearly complete basis, though not orthonormal (e.g: Rajan&Abbott 2006). It should be possible to use such a basis to learn this simple classical conditioning paradigm. It would be useful to measure the dimensionality of network dynamics, in both trained and untrained RNN's.

Thank you for pointing out the lack of explanation about untrained RNN. Untrained RNN in our simulations (except Fig. 6D/6E-gray-dotted) was randomly initialized RNN (i.e., connection weights were drawn from a pseudo normal distribution) that was used as initial RNN for training of value-RNNs. As you suggested, the performance of untrained RNN indeed improved as the number of units increased (Fig. 2J), and its highest part was almost comparable to the highest performance of trained value-RNNs (Fig. 2I). In the revision we will show the dimensionality of network dynamics (as you have suggested), and eigenvalue spectrum of the network.

• The impact of the article is limited by using a network with discrete time-steps, and only a small number of time steps from stimulus to reward. What is the length of each time step? If it's on the order of the membrane time constant, then a few time steps are only tens of ms. In the classical conditioning experiments typical delays are of the order to hundreds of milliseconds to seconds. Authors should test if random feedback weights work as well for larger time spans. This can be done by simply using a much larger number of time steps.

Thank you for pointing out this important issue, for which our explanation was lacking and our examination was insufficient. We do not consider that single time step in our models corresponds to the neuronal membrane time constant. Rather, for the following reasons, we assume that the time step corresponds to several hundreds of milliseconds:

- We assume that single RNN unit corresponds to a small neuron population that intrinsically (for genetic/developmental reasons) share inputs/outputs and are mutually connected via excitatory collaterals.

- Cortical activity is suggested to be sustained not only by fast synaptic transmission and spiking but also, even predominantly, by slower synaptic neurochemical dynamics (Mongillo et al., 2008, Science "Synaptic Theory of Working Memory" https://www.science.org/doi/10.1126/science.1150769).

- In line with such theoretical suggestion, previous research examining excitatory interactions between pyramidal cells, to which one of us (the corresponding author Morita) contributed by conducting model fitting (Morishima, Morita, Kubota, Kawaguchi, 2011, J Neurosci, https://www.jneurosci.org/content/31/28/10380), showed that mean recovery time constant from facilitation for recurrent excitation among one of the two types of cortico-striatal pyramidal cells was around 500 milliseconds.

If single time step corresponds to 500 milliseconds, three time steps from cue to reward in our simulations correspond to 1.5 sec, which matches the delay in the conditioning task used in Schultz et al. 1997 Science. Nevertheless, as you pointed out, it is necessary to examine whether our random feedback models can work for longer delays, and we will examine it in our revision.

• In the section with more biologically constrained learning rules, while the output weights are restricted to only be positive (as well as the random feedback weights), the recurrent weights and weights from input to RNN are still bi-polar and can change signs during learning. Why is the constraint imposed only on the output weights? It seems reasonable that the whole setup will fail if the recurrent weights were only positive as in such a case most neurons will have very similar dynamics, and the network dimensionality would be very low. However, it is possible that only negative weights might work. It is unclear to me how to justify that bipolar weights that change sign are appropriate for the recurrent connections and inappropriate for the output connections. On the other hand, an RNN with excitatory and inhibitory neurons in which weight signs do not change could possibly work.

Our explanation and examination about this issue were insufficient, and thank you for pointing it out and giving us helpful suggestion. In the Discussion (Line 507-510) of the original manuscript, we described "Regarding the connectivity, in our models, recurrent/feed-forward connections could take both positive and negative values. This could be justified because there are both excitatory and inhibitory connections in the cortex and the net connection sign between two units can be positive or negative depending on whether excitation or inhibition exceeds the other." However, we admit that the meaning of this description was not clear, and more explicit modeling will be necessary as you suggested.

Therefore in our revision, we will examine models, in which inhibitory units (modeling fast-spiking (FS) GABAergic cells) will be incorporated, and neuron will follow Dale’s law.

• Like most papers in the field this work assumes a world composed of a single cue. In the real world there many more cues than rewards, some cues are not associated with any rewards, and some are associated with other rewards or even punishments. In the simplest case, it would be useful to show that this network could actually work if there are additional distractor cues that appear at random either before the CS, or between the CS and US. There are good reasons to believe such distractor cues will be fatal for an untrained RNN, but might work with a trained RNN, either using BPPT or random feedback. Although this assumption is a common flaw in most work in the field, we should no longer ignore these slightly more realistic scenarios.

Thank you very much for this insightful comment. In our revision, we will examine situations where there exist not only reward-associated cue but also randomly appeared distractor cues.

Reviewer #2 (Public review):

Summary:

Tsurumi et al. show that recurrent neural networks can learn state and value representations in simple reinforcement learning tasks when trained with random feedback weights. The traditional method of learning for recurrent network in such tasks (backpropagation through time) requires feedback weights which are a transposed copy of the feed-forward weights, a biologically implausible assumption. This manuscript builds on previous work regarding "random feedback alignment" and "value-RNNs", and extends them to a reinforcement learning context. The authors also demonstrate that certain non-negative constraints can enforce a "loose alignment" of feedback weights. The author's results suggest that random feedback may be a powerful tool of learning in biological networks, even in reinforcement learning tasks.

Strengths:

The authors describe well the issues regarding biologically plausible learning in recurrent networks and in reinforcement learning tasks. They take care to propose networks which might be implemented in biological systems and compare their proposed learning rules to those already existing in literature. Further, they use small networks on relatively simple tasks, which allows for easier intuition into the learning dynamics.

Weaknesses:

The principles discovered by the authors in these smaller networks are not applied to deeper networks or more complicated tasks, so it remains unclear to what degree these methods can scale up, or can be used more generally.

In our revision, we will examine more biologically realistic models with excitatory and inhibitory units, as well as more complicated tasks with distractor cues. We will also consider whether/how the depth of networks can be increased, though we do not currently have concrete idea on this last point. Thank you also for giving us the detailed insightful 'recommendations for authors'. We will address also them in our revision.

Reviewer #3 (Public review):

Summary:

The paper studies learning rules in a simple sigmoidal recurrent neural network setting. The recurrent network has a single layer of 10 to 40 units. It is first confirmed that feedback alignment (FA) can learn a value function in this setting. Then so-called bio-plausible constraints are added: (1) when value weights (readout) is non-negative, (2) when the activity is non-negative (normal sigmoid rather than downscaled between -0.5 and 0.5), (3) when the feedback weights are non-negative, (4) when the learning rule is revised to be monotic: the weights are not downregulated. In the simple task considered all four biological features do not appear to impair totally the learning.

Strengths:

(1) The learning rules are implemented in a low-level fashion of the form: (pre-synaptic-activity) x (post-synaptic-activity) x feedback x RPE. Which is therefore interpretable in terms of measurable quantities in the wet-lab.

(2) I find that non-negative FA (FA with non negative c and w) is the most valuable theoretical insight of this paper: I understand why the alignment between w and c is automatically better at initialization.

(3) The task choice is relevant since it connects with experimental settings of reward conditioning with possible plasticity measurements.

Weaknesses:

(4) The task is rather easy, so it's not clear that it really captures the computational gap that exists with FA (gradient-like learning) and simpler learning rule like a delta rule: RPE x (pre-synpatic) x (post-synaptic). To control if the task is not too trivial, I suggest adding a control where the vector c is constant c_i=1.

Thank you for this insightful comment. We have realized that this is actually an issue that would need multilateral considerations. A previous study of one of us (Wärnberg & Kumar, 2023 PNAS) assumed that DA represents a vector error rather than a scalar RPE, and thus homogeneous DA was considered as negative control because it cannot represent vector error other than the direction of (1, 1, .., 1). In contrast, the present work assumed that DA represents a scalar RPE, and then homogeneous DA (i.e., constant feedback) would not be said as a failure mode because it can actually represent a scalar RPE and FA to the direction of (1, 1, .., 1) should in fact occur. And this FA to (1, 1, ..., 1) may actually be interesting because it means that if heterogeneity of DA inputs is not large and the feedback is not far from (1, 1, ..., 1), states are learned to be represented in such a way that simple summation of cortical neuronal activity approximates value, thereby potentially explaining why value is often correlated with regional activation (fMRI BOLD signal) of not only striatal but also cortical regions (which I have been considering as an unresolved mystery). But on the other hand, the case with constant feedback is the same as the simple delta rule, as you pointed out, and then what could be obtained from the present analyses would be that FA is actually occurring behind the successful operation of such a simple rule. Anyway we will make further examinations and considerations on this issue.

(5) Related to point 3), the main strength of this paper is to draw potential connection with experimental data. It would be good to highlight more concretely the prediction of the theory for experimental findings. (Ideally, what should be observed with non-negative FA that is not expected with FA or a delta rule (constant global feedback) ?).

In response to this insightful comment, we considered concrete predictions of our models. In the FA model, the feedback vector c and the value-weight vector w are initially at random (on average orthogonal) relationships and become gradually aligned, whereas in the non-negative model, the vectors c and w are loosely aligned from the beginning. We considered how the vectors c and w can be experimentally measured. Each element of the feedback vector c is multiplied with TD-RPE, modulating the degree of update in each pyramidal cell (more accurately, pyramidal cell population that corresponds to single RNN unit). Thus each element of c could be measured as the magnitude of response of each pyramidal cell to DA stimulation. The element of the value-weight vector w corresponding to a given pyramidal cell could be measured, if striatal neuron that receives input from that pyramidal cell can be identified (although technically demanding), as the magnitude of response of the striatal neuron to activation of the pyramidal cell.

Then, the abovementioned predictions can be tested by (i) identify cortical, striatal, and VTA regions that are connected by meso-cortico-limbic pathway and cortico-striatal-VTA pathway, (ii) identify pairs of cortical pyramidal cells and striatal neurons that are connected, (iii) measure the responses of identified pyramidal cells to DA stimulation, as well as the responses of identified striatal neurons to activation of the connected pyramidal cells, and (iv) test whether the DA->pyramidal responses and the pyramidal->striatal responses are associated across pyramidal cells, and whether such associations develop through learning. We will elaborate this tentative idea, and also other ideas, in our revision.

(6a) Random feedback with RNN in RL have been studied in the past, so it is maybe worth giving some insights how the results and the analyzes compare to this previous line of work (for instance in this paper [https://www.nature.com/articles/s41467-020-17236-y]). For instance, I am not very surprised that FA also works for value prediction with TD error. It is also expected from the literature that the RL + RNN + FA setting would scale to tasks that are more complex than the conditioning problem proposed here, so is there a more specific take-home message about non-negative FA? or benefits from this simpler toy task?

In reply to this suggestion, we will explore how our results compare to the previous studies including the paper [https://www.nature.com/articles/s41467-020-17236-y], and explore benefits of our models. At preset, we think of one possible direction. According to our results (Fig. 6E), under the non-negativity constraint, the model with random feedback and monotonic plasticity rule (bioVRNNrf) performed better, on average, than the model with backprop and non-monotonic plasticity rule (revVRNNbp) when the number of units was large, though the difference in the performance was not drastic. We will explore reasons for this, and examine if this also applies to cases with more realistic models, e.g., having separate excitatory and inhibitory units (as suggested by other reviewer).

(6b) Related to task complexity, it is not clear to me if non-negative value and feedback weights would generally scale to harder tasks. If the task in so simple that a global RPE signal is sufficient to learn (see 4 and 5), then it could be good to extend the task to find a substantial gap between: global RPE, non-negative FA, FA, BP. For a well chosen task, I expect to see a performance gap between any pair of these four learning rules. In the context of the present paper, this would be particularly interesting to study the failure mode of non-negative FA and the cases where it does perform as well as FA.

In reply to this comment and also other reviewer's comment, we will examine the performance of the different models in more complex tasks, e.g., having distractor cues or longer delays. We will also see whether or not the better performance of bioVRNNrf than revVRNNbp mentioned in the previous point applies to the different tasks.

(7) I find that the writing could be improved, it mostly feels more technical and difficult than it should. Here are some recommendations:

(7a) for instance the technical description of the task (CSC) is not fully described and requires background knowledge from other paper which is not desirable.

(7b) Also the rationale for the added difficulty with the stochastic reward and new state is not well explained.

(7c) In the technical description of the results I find that the text dives into descriptive comments of the figures but high-level take home messages would be helpful to guide the reader. I got a bit lost, although I feel that there is probably a lot of depth in these paragraphs.

Thank you for your helpful suggestions. We will thoroughly revise our writings.

(8) Related to the writing issue and 5), I wished that "bio-plausibility" was not the only reason to study positive feedback and value weights. Is it possible to develop a bit more specifically what and why this positivity is interesting? Is there an expected finding with non-negative FA both in the model capability? or maybe there is a simpler and crisp take-home message to communicate the experimental predictions to the community would be useful?

We will make considerations on whether/how the non-negative constraints could have any benefits other than biological plausibility, in particular, in theoretical aspects or applications using neuro-morphic hardware, while we will also elaborate the links to biology and concretize the model's predictions.

I think you could maybe make McKittrick's book an even bigger part of DxD, maybe even moving it into the introduction, too? Your team is mounting a strong alternative to the simple and instantaneous impression and its associated epistemology, in favor of an epistemology that is still related to empirical experience and quantification but that does not aim to make experience rapidly extractable. I think this is a big point of resonance between your work and Dear Science—to reconceive science as wondering about things we don’t know through creative representations of experience that is located at the intersection of our bodies, our relations to colonial knowledge systems, and grounds that may be outside those systems.

Author response:

Reviewer #1 (Evidence, reproducibility and clarity):

This is an interesting manuscript where the authors systematically measure rG4 levels in brain samples at different ages of patients affected by AD. To the best of my knowledge this is the first time that BG4 staining is used in this context and the authors provide compelling evidence to show an association with BG4 staining and age or AD progression, which interestingly indicates that such RNA structure might play a role in regulating protein homeostasis as previously speculated. The methods used and the results reported seem robust and reproducible.

In terms of the conclusions, however, I think that there are 2 main things that need addressing prior to publication:

(1) Usually in BG4 staining experiments to ensure that the signal detected is genuinely due to rG4 an RNase treatment experiment is performed. This does not have to be extended to all the samples presented but having a couple of controls where the authors observe loss of staining upon RNase treatment will be key to ensure with confidence that rG4s are detected under the experimental conditions. This is particularly relevant for this brain tissue samples where BG4 staining has never been performed before.

With what is now known about RNA rG4s and the recent reconciliation of the controversy on rG4 formation (Kharel, Nature Communications 2023), this experiment is no longer strictly required for demonstration of rG4 formation. Despite this change, we did attempt this experiment at the reviewer’s suggestion, but the controls were not successful, suggesting it may not be feasible with our fixing and staining conditions. That said, we agree that despite the G4 staining appearing primarily outside the nucleus, it would be helpful to have some direct indication of whether we were observing primarily RNA or DNA G4s, and so we performed an alternate experiment to determine this.

In our previous submission, we had performed ribosomal RNA staining  (Figure S7), and the staining patterns were similar to that of BG4, especially the punctate pattern near the nuclei. Therefore, we directly asked whether the BG4 was largely binding to rRNA and have now shown the resulting co-stain in Figure 3b. These results show that at least a large amount of the BG4 staining does arise from rG4s in ribosomes. At high magnification, we observe that the BG4 stains a subset of the ribosomes, consistent with previous observations of high rG4 levels in ribosomes both in vitro and in cells (Mestre-Fos, 2019 J Mol Biol, Mestre-Fos 2019 PLoS One, Mestre-Fos 2020 J Biol Chem), but this had never been demonstrated in tissue. This experiment has therefore both answered the primary question of whether we are primarily observing rG4s, as well as provided more detailed information on the cellular sublocalization of rG4 formation, and provided the first evidence of rG4 formation on ribosomes in tissue.

(2) The authors have an association between rG4-formation and age/disease progression. They also observe distribution dependency of this, which is great. However, this is still an association which does not allow the model to be supported. This is not something that can be fixed with an easy experiment and it is what it is, but my point is that the narrative of the manuscript should be more fair and reflect the fact that, although interesting, what the authors are observing is a simple correlation. They should still go ahead and propose a model for it, but they should be more balanced in the conclusion and do not imply that this evidence is sufficient to demonstrate the proposed model. It is absolutely fine to refer to the literature and comment on the fact that similar observations have been reported and this is in line with those, but still this is not an ultimate demonstration.

We agree that these are correlative studies (of necessity when studying human tissue), but recent experiments have shown that rG4s affect the aggregation of Tau in vitro – and we have now better clarified this in the text itself. We have now also been more careful in drawing causative conclusions as shown in the revised text.

Minor point:

(3) rG4s themselves have been shown to generate aggregates in ALS models in the absence of any protein (Ragueso et al. Nat Commun 2023). I think this is also important in the light of my comment on the model, could well be that these rG4s are causing aggregates themselves that act as nucleation point for the proteins as reported in the paper I mentioned. Providing a broader and more unbiased view of the current literature on the topic would be fair, rather than focusing on reports more in line with the model proposed.

We agree and have modified the discussion and added a broader context, including the Ragueso report described above.

Reviewer #1 (Significance):

This is a significant novel study, as per my comments above. I believe that such a study will be of impact in the G4 and neurodegenerative fields. Providing that the authors can address the criticisms above, I strongly believe that this manuscript would be of value to the scientific community. The main strength is the novelty of the study (never done before) the main weakness is the lack of the RNase control at the moment and the slightly over interpretation of the findings (see comments above).

Reviewer #2 (Evidence, reproducibility and clarity):

RNA guanine-rich G-quadruplexes (rG4s) are non-canonical higher order nucleic acid structures that can form under physiological conditions. Interestingly, cellular stress is positively correlated with rG4 induction.  In this study, the authors examined human hippocampal postmortem tissue for the formation ofrG4s in aging and Alzheimer Disease (AD). rG4 immunostaining strongly increased in the hippocampus with both age and with AD severity. 21 cases were used in this study (age range 30-92).  This immunostaining co-localized with hyper-phosphorylated tau immunostaining in neurons. The BG4 staining levels were also impacted by APOE status. rG4 structure was previously found to drive tau aggregation. Based on these observations, the authors propose a model of neurodegeneration in which chronic rG4 formation drives proteostasis collapse.

This model is interesting, and would explain different observations (e.g., RNA is present in AD aggregates and rG4s can enhance protein oligomerization and tau aggregation).

Main issue:

There is indeed a positive correlation between Braak stage severity and BG4 staining, but this correlation is relatively weak and borderline significant ((R = 0.52, p value = 0.028). This is probably the main limitation of this study, which should be clearly acknowledged (together with a reminder that "correlation is not causality”.

We believe that we had not explained this clearly enough in the text (based on the reviewer’s comment), as the correlation mentioned by the Reviewer was for the CA4 region only, and not the OML, which was substantially more correlated and statistically significant (Spearman R= 0.72, p = 0.00086). As a result, we believe this was a miscommunication that is rectified by the revised text:

“In the OML, plotting BG4 percent area versus Braak stage demonstrated a strong correlation (Spearman R= 0.72) with highly significantly increased BG4 staining with higher Braak stages (p = 0.00086) (Fig. 2b).”

Related to this, here is no clear justification to exclude the four individuals in Fig 1d (without them R increases to 0.78). Please remove this statement. On the other hand, the difference based on APOE status is more striking.

We did not mean to imply that deleting these outliers was correct, but merely were demonstrating that they were in fact outliers. To avoid this misinterpretation, we have now deleted the sentence in the Figure 1d caption mentioning the outliers.

Minor suggestions

- "BG4 immunostaining was in many cases localized in the cytoplasm near the nucleus in a punctate pattern". Define "many"

This is seen in nearly every cells and this is now altered in the text and is now identified as ribosomes containing rG4s using the rRNA antibody (Fig. 3b).

- Specify that MABE917 corresponds to the specific single-chain version of the BG4 antibody

Yes, this is correct, and this clarification has been added to the manuscript

- Define PMI, Braak, CERAD (add a list of acronyms or insert these definitions in Fig 1b legend)

These definitions have all been added when they first appear.

- Fig 3: scale bar legend missing (50 micrometers?)

This has been added, and the reviewer was correct that it was 50 micrometers.

- Supplementary data Table 1: indicate target for all antibodies

The target for each antibody has been added to supplementary Table 1.

- Supplementary data Table 2: why give ages with different levels of precision? (e.g. 90.15 vs 63)

We apologize for this oversight and have altered the ages to the same (whole years) in the figure.

- Supplementary data Fig 1 X-axis legend: add "(nm)" after wavelength. Sequence can also be added in the legend. Why this one? Max/Min Wavelengths in the figure do not match indications in the experimental part. Not sure if that part is actually relevant for this study.

The CD spectrum in Sup Fig 1 is the sequence that had previously been shown to aid in tau aggregation seeding, but had not been suspected by those authors to be a quadruplex. So we tested that here and showed it is a quadruplex, as described at the end of the introduction. We have added wording to the figure legend to clarify where its corresponding description in the main text can be found. We have also checked and corrected the wavelength and units.

- Supplementary data Fig 7: Which ribosomal antibody was used?

The details of this antibody have now been added to Supplementary Table 2 which lists all the antibodies used.

Reviewer #2 (Significance):

Provide a link between Alzheimer disease and RNA G-quadruplexes.

Reviewer #3 (Evidence, reproducibility and clarity):

This study investigated the formation of RNA G quadruplexes (rG4) in aging and AD in human hippocampal postmortem tissue. The rG4 immunostaining in the hippocampus increases strongly with age and with the severity of AD. Furthermore, rG4 is present in neurons with an accumulation of phosphorylated tau immunostaining.

Major comments

(1) The method used in this study is primarily immunostaining of BG4, and the results cannot be considered correct without additional data from more multifaceted analyses (biochemical analysis, RNA expression analysis, etc.).

We respectfully disagree with the Reviewer’s assessment of the value of these experiments. The most relevant biochemical experiments at the cellular and molecular level showing the role of G4s in aggregation in general and Tau in particular have been done and are referenced in the text. The results here stand on their own and are highly novel and significant, as evaluated by both of the other reviewers. There has been no previous work demonstrating the presence of rG4s in human brain – either in controls or in patients with AD. AD is a complex condition that only occurs spontaneously in the human brain and no other species; because of this complexity, novel aspects are best first studied in human brain tissue using the methods employed here.

(2) Overall, the quality of the stained images is poor, and detailed quantitative analysis using further high quality data is essential to conclude the authors' conclusions.

We have again looked at our images and they are not poor quality -they are confocal images taken at recommended resolution of the confocal microscope. It is possible the poor quality came from pdf compression by the manuscript submission portal, which is beyond our control as they were uploaded at high resolution. These data were quantified by scientists who were blinded to the diagnosis of each case. The level of description on the detailed quantification is higher than we have observed in similar studies. We therefore disagree with the reviewer’s conclusion.

Reviewer #3 (Significance):

Overall, this study is not a deeply analyzed study. In addition, the authors of this study need further understanding regarding G4.

It is also unclear why the reviewer believes that we do not have sufficient understanding of G4s, and would request that the reviewer instead provides specific comments regarding what is lacking in terms of knowledge on G4s, as we respectfully disagree with this judgement of our knowledge-base (see other G4 papers from the Horowitz lab, Begeman, 2020, Litberg 2023, Son, 2023 referenced below).

Litberg TJ, Sannapureddi RKR, Huang Z, Son A, Sathyamoorthy B, Horowitz S. Why are G-quadruplexes good at preventing protein aggregation? Jan;20(1):495-509. doi: 10.1080/15476286.2023.2228572. RNA Biol. (2023)

Son A, Huizar Cabral V, Huang Z, Litberg TJ, Horowitz S. G-quadruplexes rescuing protein folding. May 16;120(20):e2216308120. doi: 10.1073/pnas.2216308120. Proc Natl Acad Sci U S A (2023)

Guzman BB, Son A, Litberg TJ, Huang Z, Dominguez , Horowitz S. Emerging Roles for G-Quadruplexes in Proteostasis FEBS J.doi: 10.1111/febs.16608. (2022)

Begeman A, Son A, Litberg TJ, Wroblewski TH, Gehring T, Huizar Cabral V, Bourne J, Xuan Z, Horowitz S. G-Quadruplexes Act as Sequence Dependent Protein Chaperones. EMBO Reports Sep 18;e49735. doi: 10.15252/embr.201949735. (2020)

Author response:

Reviewer #1 (Public review):

Summary:

The authors present an interesting study using RL and Bayesian modelling to examine differences in learning rate adaptation in conditions of high and low volatility and noise respectively. Through "lesioning" an optimal Bayesian model, they reveal that apparently a suboptimal adaptation of learning rates results from incorrectly detecting volatility in the environment when it is not in fact present.

Strengths:

The experimental task used is cleverly designed and does a good job of manipulating both volatility and noise. The modelling approach takes an interesting and creative approach to understanding the source of apparently suboptimal adaptation of learning rates to noise, through carefully "lesioning" and optimal Bayesian model to determine which components are responsible for this behaviour.

We thank the reviewer for this assessment.

Weaknesses:

The study has a few substantial weaknesses; the data and modelling both appear robust and informative, and it tackles an interesting question. The model space could potentially have been expanded, particularly with regard to the inclusion of alternative strategies such as those that estimate latent states and adapt learning accordingly.

We thank the reviewer for this suggestion. We agree that it would be interesting to assess the ability of alternative models to reproduce the sub-optimal choices of participants in this study. The Bayesian Observer Model described in the paper is a form of Hierarchical Gaussian Filter, so we will assess the performance of a different class of models that are able to track uncertainty-- RL based models that are able to capture changes of uncertainty (the Kalman filter, and the model described by Cochran and Cisler, Plos Comp Biol 2019). We will assess the ability of the models to recapitulate the core behaviour of participants (in terms of learning rate adaption) and, if possible, assess their ability to account for the pupillometry response.

Reviewer #2 (Public review):

Summary:

In this study, the authors aimed to investigate how humans learn and adapt their behavior in dynamic environments characterized by two distinct types of uncertainty: volatility (systematic changes in outcomes) and noise (random variability in outcomes). Specifically, they sought to understand how participants adjust their learning rates in response to changes in these forms of uncertainty.

To achieve this, the authors employed a two-step approach:

(1) Reinforcement Learning (RL) Model: They first used an RL model to fit participants' behavior, revealing that the learning rate was context-dependent. In other words, it varied based on the levels of volatility and noise. However, the RL model showed that participants misattributed noise as volatility, leading to higher learning rates in noisy conditions, where the optimal strategy would be to be less sensitive to random fluctuations.

(2) Bayesian Observer Model (BOM): To better account for this context dependency, they introduced a Bayesian Observer Model (BOM), which models how an ideal Bayesian learner would update their beliefs about environmental uncertainty. They found that a degraded version of the BOM, where the agent had a coarser representation of noise compared to volatility, best fit the participants' behavior. This suggested that participants were not fully distinguishing between noise and volatility, instead treating noise as volatility and adjusting their learning rates accordingly.

The authors also aimed to use pupillometry data (measuring pupil dilation) as a physiological marker to arbitrate between models and understand how participants' internal representations of uncertainty influenced both their behavior and physiological responses. Their objective was to explore whether the BOM could explain not just behavioral choices but also these physiological responses, thereby providing stronger evidence for the model's validity.

Overall, the study sought to reconcile approximate rationality in human learning by showing that participants still follow a Bayesian-like learning process, but with simplified internal models that lead to suboptimal decisions in noisy environments.

Strengths:

The generative model presented in the study is both innovative and insightful. The authors first employ a Reinforcement Learning (RL) model to fit participants' behavior, revealing that the learning rate is context-dependent-specifically, it varies based on the levels of volatility and noise in the task. They then introduce a Bayesian Observer Model (BOM) to account for this context dependency, ultimately finding that a degraded BOM - in which the agent has a coarser representation of noise compared to volatility - provides the best fit for the participants' behavior. This suggests that participants do not fully distinguish between noise and volatility, leading to the misattribution of noise as volatility. Consequently, participants adopt higher learning rates even in noisy contexts, where an optimal strategy would involve being less sensitive to new information (i.e., using lower learning rates). This finding highlights a rational but approximate learning process, as described in the paper.

We thank the reviewer for their assessment of the paper.

Weaknesses:

While the RL and Bayesian models both successfully predict behavior, it remains unclear how to fully reconcile the two approaches. The RL model captures behavior in terms of a fixed or context-dependent learning rate, while the BOM provides a more nuanced account with dynamic updates based on volatility and noise. Both models can predict actions when fit appropriately, but the pupillometry data offers a promising avenue to arbitrate between the models. However, the current study does not provide a direct comparison between the RL framework and the Bayesian model in terms of how well they explain the pupillometry data. It would be valuable to see whether the RL model can also account for physiological markers of learning, such as pupil responses, or if the BOM offers a unique advantage in this regard. A comparison of the two models using pupillometry data could strengthen the argument for the BOM's superiority, as currently, the possibility that RL models could explain the physiological data remains unexplored.

We thank the reviewer for this suggestion. In the current version of the paper, we use an extremely simple reinforcement learning model to simply measure the learning rate in each task block (as this is the key behavioural metric we are interested in). As the reviewer highlights, this simple model doesn’t estimate uncertainty or adapt to it. Given this, we don’t think we can directly compare this model to the Bayesian Observer Model—for example, in the current analysis of the pupillometry data we classify individual trials based on the BOM’s estimate of uncertainty and show that participants adapt their learning rate as expected to the reclassified trials, this analysis would not be possible with our current RL model. However, there are more complex RL based models that do estimate uncertainty (as discussed above in response to Reviewer #1) and so may more directly be compared to the BOM. We will attempt to apply these models to our task data and describe their ability to account for participant behaviour and physiological response as suggested by the Reviewer.

The model comparison between the Bayesian Observer Model and the self-defined degraded internal model could be further enhanced. Since different assumptions about the internal model's structure lead to varying levels of model complexity, using a formal criterion such as Bayesian Information Criterion (BIC) or Akaike Information Criterion (AIC) would allow for a more rigorous comparison of model fit. Including such comparisons would ensure that the degraded BOM is not simply favored due to its flexibility or higher complexity, but rather because it genuinely captures the participants' behavioral and physiological data better than alternative models. This would also help address concerns about overfitting and provide a clearer justification for using the degraded BOM over other potential models.

Thank you, we will add this.

I found this paragraph in Chapter 1 really interesting because the author suggests we should look at design, and situations in general, in a different lens. Too often we focus on what's the most obvious target and work backwards from there, but it can also be beneficial to first consider multiple perspectives and determine other stakeholders in the process. Having a different lens when viewing design choices can allow you to make better decisions and more aware of the user. I think what the author is suggesting overall is that we should not be hyper fixate on particular group.

I agree that looking at human values is important when considering "fixing" and "improving" the lives of specific groups. As mentioned, while a mobile app may help a specific group, it can also unintentional but another group at a disadvantage. In my opinion, I think it is easy to get so focused on fixing an issue, that it's easy to neglect or forget about the others involved. I agree that viewing it from this perspective does allow designers to consider those who may be affected "negatively" by the design.

Author response:

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

Reviewer #1 (Public review):

Summary:

How reconsolidation works - particularly in humans - remains largely unknown. With an elegant, 3-day design, combining fMRI and psychopharmacology, the authors provide evidence for a certain role for noradrenaline in the reconsolidation of memory for neutral stimuli. All memory tasks were performed in the context of fMRI scanning, with additional resting-state acquisitions performed before and after recall testing on Day 2. On Day 1, 3 groups of healthy participants encoded word-picture associates (with pictures being either scenes or objects) and then performed an immediate cued recall task to presentation of the word (answering is the word old or new, and whether it was paired with a scene or an object). On Day 2, the cued recall task was repeated using half of the stimulus set words encoded on Day 1 (only old words were presented, with subjects required to indicate prior scene vs object pairing). This test was immediately preceded by the oral administration of placebo, cortisol, or yohimbine (to raise noradrenaline levels) depending on group assignment. On Day 3, all words presented on Day 1 were presented. As expected, on Day 3, memory was significantly enhanced for associations that were cued and successfully retrieved on Day 2 compared to uncued associations. However, for associative d', there was no Cued × Group interaction nor a main effect of Group, i.e., on the standard measure of memory performance, post-retrieval drug presence on Day 2 did not affect memory reconsolidation. As further evidence for a null result, fMRI univariate analyses showed no Cued × Group interactions in whole-brain or ROI activity.

Strengths:

There are some aspects of this study that I find impressive. The study is well-designed and the fMRI analysis methodology is innovative and sound. The authors have made meticulous and thorough physiological measurements, and assays of mood, throughout the experiment. By doing so, they have overcome, to a considerable extent, the difficulties inherent in the timing of human oral drug delivery in reconsolidation tasks, where it is difficult to have the drug present in the immediate recall period without affecting recall itself. This is beautifully shown in Figure 3. I also think that having some neurobiological assay of memory reactivation when studying reconsolidation in humans is critical, and the authors provide this. While multi-voxel patterns of hemodynamic responses are, in my view, very difficult to equate with an "engram", these patterns do have something to do with memory.

We thank the reviewer for considering aspects of our work impressive, the study to be well-designed, and the methodology to be innovative and sound.

Weaknesses:

I have major issues regarding the behavioral results and the framing of the manuscript.

(1) To arrive at group differences in memory performance, the authors performed median splitting of Day 3 trials by short and long reaction times during memory cueing on Day 2, as they took this as a putative measure of high/low levels of memory reactivation. Associative category hits on Day 3 showed a Group by Day 2 Reaction time (short, long) interaction, with post-hocs showing (according to the text) worse memory for short Day 2 RTs in the Yohimbine group. These post-hocs should be corrected for multiple comparisons, as the result is not what would be predicted (see point 2). My primary issue here is that we are not given RT data for each group, nor is the median splitting procedure described in the methods. Was this across all groups, or within groups? Are short RTs in the yohimbine group any different from short RTs in the other two groups? Unfortunately, we are not given Day 2 picture category memory levels or reaction times for each group. This is relevant because (as given in Supplemental Table S1) memory performance (d´) for the Yohimbine group on Day 1 immediate testing is (roughly speaking) 20% lower than the other 2 groups (independently of whether the pairs will be presented again the following day). I appreciate that this is not significant in a group x performance ANOVA but how does this relate to later memory performance? What were the group-specific RTs on Day 1? So, before the reader goes into the fMRI results, there are questions regarding the supposed drug-induced changes in behavior. Indeed, in the discussion, there is repeated mention of subsequent memory impairment produced by yohimbine but the nature of the impairment is not clear.

Thank you for the opportunity to clarify these important issues.

Reaction times are well established proxies (correlates) of memory strength and memory confidence in previous research, as they reflect cognitive processes involved in retrieving information. Faster reaction times indicate stronger mnemonic evidence and higher confidence in the accuracy of a memory decision, while slower responses suggest weaker evidence and decision uncertainty or doubt. This relationship is supported by an extensive literature (e.g., Starns 2021; Robinson et al., 1997; Ratcliff & Murdock, 1976; amongst others). Importantly, distinguishing between high and low confidence choices in a memory task serves the purpose of differentiating between particularly strong memory evidence (e.g., in associative cued recall, when remembering is particularly vivid) and weaker memory evidence. Separating low from high confidence responses based on participants’ reaction times was especially important in the current analyses, because previous research demonstrates that reaction times during cued recall tasks inversely correlate with hippocampal involvement (Heinbockel et al., 2024; Gagnon et al. 2019) and that stress-effects on human memory may be particularly pronounced for high-confidence memories (Gagnon et al., 2019).

In response to the Reviewer 1’s comments, we have elaborated on our rationale for the distinction between short and long reaction times in the introduction, results, and methods. Please see page 4, lines 144 to 148:

“We distinguished between responses with short and long reaction times indicative of high and low confidence responses because previous research showed that reaction times are inversely correlated with hippocampal memory involvement(58-60) and memory strength(61,62), and that high confidence memories associated with short reaction times may be particularly sensitive to stress effects(63).”

On page 13, lines 520 to 523:

“Reaction times in the Day 2 Memory cueing task revealed a trial-specific gradient in reactivation strength. Thus, we turned to single-trial analyses, differentiating Day 3 trials by short and long reaction times during memory cueing on Day 2 (median split), indicative of high vs. low memory confidence(58–60) and hippocampal reactivation(26,63).”

And on page 26, lines 1046 to 1053:

“Reaction times serve as a proxy for memory confidence and memory strength, with faster responses reflecting higher confidence/strength and slower responses suggesting greater uncertainty/weaker memory. The association between reaction times and memory confidence has been established by previous research(58–60), suggesting that the distinction between high from low confidence responses differentiates vividly recalled associations from decisions based on weaker memory evidence. Reaction times are further linked to hippocampal activity during recall tasks(26,53), and stress effects on memory are particularly pronounced for high-confidence memories(53).”

With respect to behavioral data reporting, we agree that the critical median-split procedure was not sufficiently clear in the original manuscript. We elaborate on this important aspect of the analysis now on page 26, lines 1053 to 1057:

“We conducted a median-split within each participant to categorize trials as fast vs. slow reaction time trials during Day 2 memory cueing. We conducted this split on the participant- and not group-level because there is substantial inter-individual variability in overall reaction times. This approach also results in an equal number of trials in the low and high confidence conditions.”

We completely agree that the relevant post-hoc test should be corrected for multiple comparisons. Please note that all reported post-hoc tests had been Bonferroni-corrected already. We clarify this now by explicitly referring to corrected p-values (P_corr) and indicate in the methods that P_corr refers to Bonferroni-corrected p-values. (please see page 25, lines 1036 to 1038).

We further agree that for a comprehensive overview of the behaviour in terms of memory performance and RTs, these data need to be provided for each group and experimental day. Therefore, we now extended Supplementary Table S1 to include descriptive indices of memory performance (hits, dprime) and RTs for each group for each day. Moreover, we now report ANOVAs for reaction times for each of the experimental days in the main text.

The ANOVA for Day 1 is now reported on page 6, lines 200 to 204: “To test for potential group differences in reaction times for correctly remembered associations on Day 1, we fit a linear model including the factors Group and Cueing. Critically, we did not observe a significant Group x Cueing interaction, suggesting no RT difference between groups for later cued and not cued items (F(2,58) = 1.41, P = .258, η² = 0.01; Supplemental Table S1).”

The ANOVA for Day 2 is now reported on page 7, lines 243 to 248: “To test for potential group differences in reaction times for correctly remembered associations on Day 2, we fit a linear model including the factors Group and Reaction time (slow/fast) following the subject specific median split. The model did not reveal any main effect or interaction including the factor Group (all Ps > .535; Supplemental Table S1), indicating that there was no RT difference between groups, nor between low and high RT trials in the groups.”

The ANOVA for Day 3 is reported on page 13 lines 487 to 494: “To test for potential group differences in reaction times for correctly remembered associations on Day 3 we fit a linear model including the factors Group and Cueing. This model did not reveal any main effect or interaction including the factor Group (all Ps > .267), indicating that there was no average RT difference between groups. As expected we observed a main effect of the factor Cueing, indicating a significant difference of reaction times across groups between trials that were successfully cued and those not cued on Day 2 (F(2,58) = 153.07, P < .001, η² = 0.22; Supplemental Table S1).”

(2) The authors should be clearer as to what their original hypotheses were, and why they did the experiment. Despite being a complex literature, I would have thought the hypotheses would be reconsolidation impairment by cortisol and enhancement by yohimbine. Here it is relevant to point out that - only when the reader gets to the Methods section - there is mention of a paper published by this group in 2024. In this publication, the authors used the same study design but administered a stress manipulation after Day 2 cued recall, instead of a pharmacological one. They did not find a difference in associative hit rate between stress and control groups, but - similar to the current manuscript - reported that post-retrieval stress disrupts subsequent remembering (Day 3 performance) depending on neural memory reinstatement during reactivation (specifically driven by the hippocampus and its correlation with neocortical areas).

Instead of using these results, and other human studies, to motivate the current work, reference is made to a recent animal study: Line 169 "Building on recent findings in rodents (Khalaf et al. 2018), we hypothesized that the effects of post-retrieval noradrenergic and glucocorticoid activation would critically depend on the reinstatement of the neural event representation during retrieval". It is difficult to follow that a rodent study using contextual fear conditioning and examining single neuron activity to remote fear recall and extinction would be relevant enough to motivate a hypothesis for a human psychopharmacological study on emotionally neutral paired associates.

We agree that our recent publication utilizing a very similar experimental design including three days is highly relevant in the context of the current study and we now refer to this recent study earlier in our manuscript. Please see page 3, lines 89 to 94:  

“Recently, we showed a detrimental impact of post-retrieval stress on subsequent memory that was contingent upon reinstatement dynamics in the Hippocampus, VTC and PCC during memory reactivation26. While this study provided initial insights into the potential brain mechanisms involved in the effects of post-retrieval stress on subsequent memory, the underlying neuroendocrine mechanisms remained elusive.”

Moreover, we explicitly state our hypothesis regarding the neural mechanism, with reference to our recent work, on page 5, lines 166 to 169:

“Building on our recent findings in humans(26) as well as current insights from rodents(47), we hypothesized that the effects of post-retrieval noradrenergic and glucocorticoid activation would critically depend on the reinstatement of the neural event representation during retrieval.”

Concerning the potential direction of the effects of post-retrieval cortisol and noradrenaline, the literature is indeed mixed with partially contradicting results, which made it, in our view, difficult to derive a clear hypothesis of potentially opposite effects of cortisol and yohimbine. We summarize the relevant evidence in the introduction on pages 3 to 4, lines 100 to 113:

“Some studies, using emotional recognition memory or fear conditioning in healthy humans, suggest enhancing effects of post-retrieval glucocorticoids on subsequent memory(30,31). However, rodent studies on neutral recognition memory(21), fear conditioning(32), as well as evidence from humans on episodic recognition memory(33) report impairing effects of glucocorticoid receptor activation on post-retrieval memory dynamics. For noradrenaline, post-retrieval blockade of noradrenergic activity impairs putative reconsolidation or future memory accessibility in human fear conditioning(34), as well as drug (alcohol) memory(35) and spatial memory in rodents(36). However, this effect is not consistently observed in human studies on fear conditioning(40), speaking anxiety(37), inhibitory avoidance(39), traumatic mental imagination (PTSD patients)(38), and might depend on the arousal state of the individual(21) or the exact timing of drug administration as suggested by studies in humans(41) and rodents(42). Thus, while there is evidence that glucocorticoid and noradrenergic activation after retrieval can affect subsequent memory, the direction of these effects remains elusive.”

In addition to these reviewer comments and in response to the eLife assessment, we would like to emphasize that the present findings are in our view not only relevant for a subfield but may be of considerable interest for researchers from various fields, beyond experimental memory research, including Neurobiology, Psychiatry, Clinical Psychology, Educational Psychology, or Law Psychology. We highlight the relevance of the topic and our findings now more explicitly in the introduction and discussion. Please see page 3:

“The dynamics of memory after retrieval, whether through reconsolidation of the original trace or interference with retrieval-related traces, have fundamental implications for educational settings, eyewitness testimony, or mental disorders(5,11,12). In clinical contexts, post-retrieval changes of memory might offer a unique opportunity to retrospectively modify or render less accessible unwanted memories, such as those associated with posttraumatic stress disorder (PTSD) or anxiety disorders(13–15). Given these potential far reaching implications, understanding the mechanisms underlying post-retrieval dynamics of memory is essential.”

On page 17:

“Upon their retrieval, memories can become sensitive to modification(1,2). Such post-retrieval changes in memory may be fundamental for adaptation to volatile environments and have critical implications for eyewitness testimony, clinical or educational contexts(5,11–15). Yet, the brain mechanisms involved in the dynamics of memory after retrieval are largely unknown, especially in humans.”

And on page 19:

“Beyond their theoretical relevance, these findings may have relevant implications for attempts to employ post-retrieval manipulations to modify unwanted memories in anxiety disorders or PTSD(97,98). Specifically, the present findings suggest that such interventions may be particularly promising if combined with cognitive or brain stimulation techniques ensuring a sufficient memory reactivation.“

Reviewer #1 (Recommendations for the authors):

(1) Related to major issue 2 in the Public Review. In the introduction, it would be helpful to be specific about the type of memory being probed in the different studies referenced (episodic vs conditioning). For the former, please make it clear whether stimuli to be remembered were emotional or neutral, and for which stimulus class drug effects were observed. This is particularly important given that in the first paragraph, you describe memory reactivation in the context of traumatic memories via mention of PTSD. It would also be helpful to know to which species you refer. For example, in line 115, "timing of drug administration..." a rodent and a human study are cited.

We completely agree that these aspects are important. We have therefore rewritten the corresponding paragraph in the introduction to clarify the type of memory probed, the emotionality of the stimuli and the species tested. Please see pages 3 to 4, lines 100 to 113:

“Some studies, using emotional recognition memory or fear conditioning in healthy humans, suggest enhancing effects of post-retrieval glucocorticoids on subsequent memory(30,31). However, rodent studies on neutral recognition memory(21), fear conditioning(32), as well as evidence from humans on episodic recognition memory(33) report impairing effects of glucocorticoid receptor activation on post-retrieval memory dynamics. For noradrenaline, post-retrieval blockade of noradrenergic activity impairs putative reconsolidation or future memory accessibility in human fear conditioning(34), as well as drug (alcohol) memory(35) and spatial memory in rodents(36). However, this effect is not consistently observed in human studies on fear conditioning(40), speaking anxiety(37), inhibitory avoidance(39), traumatic mental imagination (PTSD patients)(38), and might depend on the arousal state of the individual(21) or the exact timing of drug administration as suggested by studies in humans(41) and rodents(42). Thus, while there is evidence that glucocorticoid and noradrenergic activation after retrieval can affect subsequent memory, the direction of these effects remains elusive.”

(2) The Bos 2014 reference appears incorrect. I think you mean the Frontiers paper of the same year.

Thank you for noticing this mistake, which has been corrected.

(3) Line 734 "The study employed a fully crossed, placebo-controlled, double-blind, between-subjects design". What is a fully crossed design?

A fully-crossed design refers to studies in which all possible combinations of multiple between-subjects factors are implemented. However, because the factor reactivation/cueing was manipulated within-subject in the present study and there is only one between-subjects factor (group/drug), “fully-crossed” may be misleading here. We removed it from the manuscript.

(4) Supplemental Table S3. Are these ordered in terms of significance? A t- or Z-value for each cluster (either of the peak or a summed value) would be helpful.

We agree that the ordering of the clusters was not clearly described. In the revised Supplemental Table S3, we have now added a column with the cluster-peak specific T-values and added an explanation in the table caption: “Depicted clusters are ordered by cluster-peak T-values.”

(5) Please provide the requested memory performance and reaction time data, and relevant group comparisons.

In response to general comment #1 above, we now provide all relevant accuracy and reaction time data for all groups and experimental days in the revised Supplemental Table S1. Moreover, we now report the relevant group comparisons in the main text on page 6, lines 200 to 204, on page 7, lines 243 to 248, and on page 13, lines 487 to 494.

(6) Please rewrite the introduction with specific hypotheses, mention your recent results published in Science Advances, and attend to suggestions made in the first comment above.

We have rewritten parts of the introduction to make the link to our recent publication clearer and to clarify the types of memories and species tested, as suggested by the reviewer (please see pages 3 to 4, lines 100 to 113). Moreover, we explicitly state our hypothesis regarding the neural mechanism on page 5, lines 166 to 169:

“Building on our recent findings in humans(26) as well as current insights from rodents(47), we hypothesized that the effects of post-retrieval noradrenergic and glucocorticoid activation would critically depend on the reinstatement of the neural event representation during retrieval.”

In terms of the direction of the potential cortisol and yohimbine effects, we have elaborated on the relevant literature, which in our view does not allow a clear prediction regarding the nature of the drug effects. We have made this explicit by stating that “… while there is evidence that glucocorticoid and noradrenergic activation after retrieval can affect subsequent memory, the direction of these effects remains elusive.” (please see page 4, lines 111 to 113). It would be, in our view, inappropriate to retrospectively add another, more specific “hypothesis”.

Reviewer #2 (Public review):

Summary:

The authors aimed to investigate how noradrenergic and glucocorticoid activity after retrieval influence subsequent memory recall with a 24-hour interval, by using a controlled three-day fMRI study involving pharmacological manipulation. They found that noradrenergic activity after retrieval selectively impairs subsequent memory recall, depending on hippocampal and cortical reactivation during retrieval.

Overall, there are several significant strengths of this well-written manuscript.

Strengths:

(1) The study is methodologically rigorous, employing a well-structured three-day experimental design that includes fMRI imaging, pharmacological interventions, and controlled memory tests.

(2) The use of pharmacological agents (i.e., hydrocortisone and yohimbine) to manipulate glucocorticoid and noradrenergic activity is a significant strength.

(3) The clear distinction between online and offline neural reactivation using MVPA and RSA approaches provides valuable insights into how memory dynamics are influenced by noradrenergic and glucocorticoid activity distinctly.

We thank the reviewer for these very positive and encouraging remarks.

Weaknesses:

(1) One potential limitation is the reliance on distinct pharmacodynamics of hydrocortisone and yohimbine, which may complicate the interpretation of the results.

We agree that the pharmacodynamics of hydrocortisone and yohimbine are different. However, we took these pharmacodynamics into account when designing the experiment and have made an effort to accurately track the indicators for noradrenergic arousal and glucocorticoids across the experiment. As shown in Figure 2, these indicators confirm that both drugs are active within the time window of approximately 40-90 minutes after reactivation. This time window corresponds to the proposed reconsolidation window, which is assumed to open around 10 minutes post-reactivation and to remain open for a few hours (approximately 90 minutes; Monfils & Holmes, 2018; Lee et al., 2017; Monfils et al., 2009).

We have now acknowledged the distinct pharmacodynamics of hydrocortisone and yohimbine on page 21, lines 845 to 847: “We note that yohimbine and hydrocortisone follow distinct pharmacodynamics(104,105), yet selected the administration timing to ensure that both substances are active within the relevant post-retrieval time window.”

In the results section, on page 11, lines 437 to 439, we further emphasize this differential dynamic: “Our data demonstrate that, despite the distinct pharmacodynamics of CORT and YOH, both substances are active within the time window that is critical for potential reconsolidation effects(3,4,43).”

(2) Another point related above, individual differences in pharmacological responses, physiological and cortisol measures may contribute to memory recall on Day 3.

The administered drugs elicit a pronounced adrenergic and glucocorticoid response, respectively. Specifically, the cortisol levels reached by 20mg of hydrocortisone correspond to those observed after a significant stressor exposure. Moreover, individual variation in stress system activation following drug intake tends to be less pronounced than in response to a natural stressor. Nevertheless, we fully agree that individual factors, such as metabolism or body weight, can influence the drug's action.

We therefore re-analysed the reported Day 3 models, now including individual measures of baseline-to-peak changes in cortisol and systolic blood pressure, respectively. We report these additional analyses in the supplement and refer the interested reader to these analyses on page 15, lines 580 to 586:

“As individual factors, such as metabolism or body weight, can influence the drug's action, we ran an additional analysis in which we included individual (baseline-to-peak) differences in salivary cortisol and (systolic) blood pressure, respectively. This analysis did not show any group by baseline-to-peak difference interaction suggesting that the observed memory effects were mainly driven by the pharmacological intervention group per se and less by individual variation in responses to the drug (see Supplemental Results).”

And in the Supplemental Results:

“To account for individual differences in cortisol responses after pill intake, we fit additional GLMMs predicting Day 3 subsequent memory of cued and correct trials including the factors Individual baseline-to-peak cortisol and Group. Doing so allowed us to account for variation in Day 3 performance, which might have resulted from within-group variation in cortisol responses, in particular in the CORT group. Importantly, none of the models predicting Day 3 memory performance by Day 2 cortisol-increase and Group, median-split RTs (high/low), hippocampal activity and RTs, or hippocampal activity and VTC category reinstatement revealed a significant group x baseline-to-peak cortisol interaction (all Ps > .122). These results suggest that inter-individual differences in cortisol responses did not have a significant impact on subsequent memory, beyond the influence of group per se. The same analyses were repeated for systolic blood pressure employing GLMMs predicting Day 3 subsequent memory of cued and correct trials including the factors Individual baseline-to-peak systolic blood pressure and Group to account for variation in Day 3 performance, which might have resulted from within-group variation in blood pressure response, in particular in the YOH group. While the model predicting Day 3 memory performance revealed a significant Individual baseline-to-peak systolic blood pressure × Group × median-split RTs (high/low) interaction (β = -0.05 ± 0.02, z = -2.04, P = .041, R²_conditional = 0.01), post-hoc slope tests, however, did not show any significant difference between groups (all P_Corr > .329). The remaining models including hippocampal activity and RTs, or hippocampal activity and VTC category reinstatement did not reveal a significant Group × Individual baseline-to-peak systolic blood pressure interaction (all Ps > .101). These results suggest that inter-individual differences in systolic blood pressure responses did not have a significant impact on subsequent memory, beyond the influence of group per se.”

Although we acknowledge that our study may not have been sufficiently powered for an analysis of individual differences, these data suggest that our memory effects were mainly driven by the pharmacological intervention group per se and less by individual variation in responses. It is to be noted, however, that all participants of the respective groups showed a pronounced increase in cortisol concentrations (on average > 1000% in the CORT group) and autonomic arousal (on average > 10% in the YOH group), respectively. These increases appeared to be sufficient to drive the observed memory effects, irrespective of some individual variation in the magnitude of the response.

(3) Median-splitting approach for reaction times and hippocampal activity should better be justified.

Reaction times are well established proxies (correlates) of memory strength and memory confidence in previous research, as they reflect cognitive processes involved in retrieving information. Faster reaction times indicate stronger mnemonic evidence and higher confidence in the accuracy of a memory decision, while slower responses suggest weaker evidence and decision uncertainty or doubt. This relationship is supported by an extensive literature (e.g., Starns 2021; Robinson et al., 1997; Ratcliff & Murdock, 1976; amongst others). Importantly, distinguishing between high and low confidence choices in a memory task serves the purpose to differentiating between particularly strong memory evidence (e.g., is associative cued recall, when remembering is particularly vivid) and weaker memory evidence. Separating low from high confidence responses based on participants’ reaction times was especially important in the current analyses, because previous research demonstrates that reaction times during cued recall tasks inversely correlate with hippocampal involvement  Heinbockel et al., 2024; Gagnon et al. 2019) and that stress-effects on human memory may be particularly pronounced for high-confidence memories (Gagnon et al., 2019).

In response to the Reviewer comments, we have elaborated on our rationale for the distinction between short and long reaction times in the introduction, results, and methods. Please see page 4, lines 144 to 148:

“We distinguished between responses with short and long reaction times indicative of high and low confidence responses because previous research showed that reaction times are inversely correlated with hippocampal memory involvement(58–60) and memory strength(61,62), and that high confidence memories associated with short reaction times may be particularly sensitive to stress effects(63).”

On page 13, lines 520 to 523:

“Reaction times in the Day 2 Memory cueing task revealed a trial-specific gradient in reactivation strength. Thus, we turned to single-trial analyses, differentiating Day 3 trials by short and long reaction times during memory cueing on Day 2 (median split), indicative of high vs. low memory confidence(58–60) and hippocampal reactivation(26,63).”

And on page 26, lines 1046 to 1053:

“Reaction times serve as a proxy for memory confidence and memory strength, with faster responses reflecting higher confidence/strength and slower responses suggesting greater uncertainty/weaker memory. The association between reaction times and memory confidence has been established by previous research(58–60), suggesting that the distinction between high from low confidence responses differentiates vividly recalled associations from decisions based on weaker memory evidence. Reaction times are further linked to hippocampal activity during recall tasks(26,53), and stress effects on memory are particularly pronounced for high-confidence memories(53).”

We agree that the critical median-split procedure was not sufficiently clear in the original manuscript. We elaborate on this important aspect of the analysis now on page 26, lines 1053 to 1057:

“We conducted a median-split within each participant to categorize trials as slow vs. fast reaction time trials during Day 2 memory cueing. We chose to conduct this split on the participant- and not group-level because there is substantial inter-individual variability in overall reaction times and to retain an equal number of trials in the low and high confidence conditions.”

In addition to these reviewer comments and in response to the eLife assessment, we would like to emphasize that the present findings are in our view not only relevant for a subfield but may be of considerable interest for researchers from various fields, beyond experimental memory research, including Neurobiology, Psychiatry, Clinical Psychology, Educational Psychology, or Law Psychology. We highlight the relevance of the topic and our findings now more explicitly in the introduction and discussion. Please see page 3:

“The dynamics of memory after retrieval, whether through reconsolidation of the original trace or interference with retrieval-related traces, have fundamental implications for educational settings, eyewitness testimony, or mental disorders5,11,12. In clinical contexts, post-retrieval changes of memory might offer a unique opportunity to retrospectively modify or render less accessible unwanted memories, such as those associated with posttraumatic stress disorder (PTSD) or anxiety disorders(13–15). Given these potential far reaching implications, understanding the mechanisms underlying post-retrieval dynamics of memory is essential.”

On page 17:

“Upon their retrieval, memories can become sensitive to modification(1,2). Such post-retrieval changes in memory may be fundamental for adaptation to volatile environments and have critical implications for eyewitness testimony, clinical or educational contexts(5,11–15), Yet, the brain mechanisms involved in the dynamics of memory after retrieval are largely unknown, especially in humans.”

And on page 19:

“Beyond their theoretical relevance, these findings may have relevant implications for attempts to employ post-retrieval manipulations to modify unwanted memories in anxiety disorders or PTSD(97,98). Specifically, the present findings suggest that such interventions may be particularly promising if combined with cognitive or brain stimulation techniques ensuring a sufficient memory reactivation.“

Reviewer #2 (Recommendations for the authors):

My comments and/or questions for the authors to improve this well-written manuscript.

(1) This study identifies the modulatory role of the hippocampus and VTC in the effects of norepinephrine on subsequent memory. Are there functional interactions between these ROIs and other brain regions that could be wise to consider for a more comprehensive understanding of the underlying neural mechanisms?

We agree that functional interactions of hippocampus and VTC and other regions that were active during Day 2 memory cueing are relevant for our understanding of the underlying mechanisms. We therefore now performed connectivity analyses using general psycho-physiological interaction analysis (gPPI; as implemented in SPM) and report the results of this analysis on page 16, lines 635 to 644, and added Supplemental Table S4 including gPPI statistics.

“We conducted general psycho-physiological interaction analysis (gPPI) analyses on the Day 2 memory cueing task (remembered – forgotten), which revealed that successful cueing was accompanied by significant functional connectivity between the left hippocampus, VTC, PCC and MPFC (see Supplemental Table S4). However, using these connectivity estimates to predict Day 3 subsequent memory performance (dprime) via regression did not reveal any significant Group × Connectivity interactions, indicating that the pharmacological manipulation (i.e. noradrenergic stimulation) did not modulate subsequent memory based on functional connectivity during memory cueing (all P_Corr > .228). The same pattern of results was observed when including single trial beta estimates from multiple ROIs during memory cueing to predict Day 3 memory (all interaction effects P_Corr > .288).”

(2) In theory, noradrenergic activity would have a profound impact on activity in widespread brain regions that are closely related to memory function. It would be interesting to know other possible effects beyond the hippocampus and VTC.

We agree and included in our analysis additional ROIs beyond the HC and VTC; we now report these explorative results on page 16, lines 616 to 633:

“Beyond hippocampal and VTC activity during memory cueing (Day 2), we exploratively reanalysed the GLMMs predicting Day 3 memory performance including the PCC, which was relevant during memory cueing in the current study and in our previous work(26).  Predicting Day 3 memory performance by the factors Group and Single trial beta activity during memory cueing in the PCC did not reveal a significant interaction (P_Corr  = 1); adding the factor Reaction time to the model also did not result in a significant interaction (P_Corr = 1). We also included the Medial Prefrontal Cortex (MPFC) to predict Day 3 memory performance, as the MPFC has been shown to be sensitive to noradrenergic modulation in previous work(75). Predicting Day 3 memory performance by the factors Group and Single trial beta activity during memory cueing in the MPFC did not reveal a significant interaction (P_Corr  = 1); adding the factor Reaction time to the model also did not result in a significant interaction (P_Corr = 1), which indicates that the MPFC was not modulated by either pharmacological intervention. Finally, we investigated memory cueing from all remaining ROIs that were significantly activated during the Day 2 memory cueing task (Day 2 whole-brain analysis; correct-incorrect; Supplemental Table S3). We again fit GLMMs predicting Day 3 memory performance by the factors Group and Single trial beta activity during memory cueing. Again, we did not observe any significant interaction effect any of the ROIs (all interaction P_Corr > .060) and these results did not change when adding the factor Reaction time to the respective models (all  P_Corr > .075).”

(3) There are substantial individual differences in pharmacological responses, physiological and cortisol measures, as shown in Figure 3A&B. If such individual differences are taken into account, are there any potential effects on subsequent recall on Day 3 pertaining to the hydrocortisone group?

In response to this comment (and the General comment #1 of this reviewer), we now re-analyzed the respective models including individual measures of baseline-to-peak cortisol and systolic blood pressure.

We re-analysed the reported Day 3 models, now including individual measures of baseline-to-peak changes in cortisol and systolic blood pressure, respectively. We report these additional analyses in the supplement and refer the interested reader to these analyses on page 15, lines 580 to 586:

“As individual factors, such as metabolism or body weight, can influence the drug's action, we ran an additional analysis in which we included individual (baseline-to-peak) differences in salivary cortisol and (systolic) blood pressure, respectively. This analysis did not show any group by baseline-to-peak difference interaction suggesting that the observed memory effects were mainly driven by the pharmacological intervention group per se and less by individual variation in responses to the drug (see Supplemental Results).”

And in the Supplemental Results:

“To account for individual differences in cortisol responses after pill intake, we fit additional GLMMs predicting Day 3 subsequent memory of cued and correct trials including the factors Individual baseline-to-peak cortisol and Group. Doing so allowed us to account for variation in Day 3 performance, which might have resulted from within-group variation in cortisol responses, in particular in the CORT group. Importantly, none of the models predicting Day 3 memory performance by Day 2 cortisol-increase and Group, median-split RTs (high/low), hippocampal activity and RTs, or hippocampal activity and VTC category reinstatement revealed a significant group x baseline-to-peak cortisol interaction (all Ps > .122). These results suggest that inter-individual differences in cortisol responses did not have a significant impact on subsequent memory, beyond the influence of group per se. The same analyses were repeated for systolic blood pressure employing GLMMs predicting Day 3 subsequent memory of cued and correct trials including the factors Individual baseline-to-peak systolic blood pressure and Group to account for variation in Day 3 performance, which might have resulted from within-group variation in blood pressure response, in particular in the YOH group. While the model predicting Day 3 memory performance revealed a significant Individual baseline-to-peak systolic blood pressure × Group × median-split RTs (high/low) interaction (β = -0.05 ± 0.02, z = -2.04, P = .041, R²_conditional = 0.01), post-hoc slope tests, however, did not show any significant difference between groups (all P_Corr > .329). The remaining models including hippocampal activity and RTs, or hippocampal activity and VTC category reinstatement did not reveal a significant Group × Individual baseline-to-peak systolic blood pressure interaction (all Ps > .101). These results suggest that inter-individual differences in systolic blood pressure responses did not have a significant impact on subsequent memory, beyond the influence of group per se.”

(4) Median-splitting approach for reaction times and hippocampal activity should better be justified.

Reaction times are well established proxies (correlates) of memory strength and memory confidence in previous research, as they reflect cognitive processes involved in retrieving information. Faster reaction times indicate stronger mnemonic evidence and higher confidence in the accuracy of a memory decision, while slower responses suggest weaker evidence and decision uncertainty or doubt. This relationship is supported by an extensive literature (e.g., Starns 2021; Robinson et al., 1997; Ratcliff & Murdock, 1976; amongst others). Importantly, distinguishing between high and low confidence choices in a memory task serves the purpose to differentiating between particularly strong memory evidence (e.g., is associative cued recall, when remembering is particularly vivid) and weaker memory evidence. Separating low from high confidence responses based on participants’ reaction times was especially important in the current analyses, because previous research demonstrates that reaction times during cued recall tasks inversely correlate with hippocampal involvement ( Heinbockel et al., 2024; Gagnon et al. 2019) and that stress-effects on human memory may be particularly pronounced for high-confidence memories (Gagnon et al., 2019).

In response to the Reviewer comments, we have elaborated on our rationale for the distinction between short and long reaction times in the introduction, results, and methods. Please see page 4, lines 144 to 148:

“We distinguished between responses with short and long reaction times indicative of high and low confidence responses because previous research showed that reaction times are inversely correlated with hippocampal memory involvement(58–60) and memory strength(61,62), and that high confidence memories associated with short reaction times may be particularly sensitive to stress effects(63).”

On page 13, lines 520 to 523:

“Reaction times in the Day 2 Memory cueing task revealed a trial-specific gradient in reactivation strength. Thus, we turned to single-trial analyses, differentiating Day 3 trials by short and long reaction times during memory cueing on Day 2 (median split), indicative of high vs. low memory confidence(58–60) and hippocampal reactivation(26,63).”

And on page 26, lines 1046 to 1053:

“Reaction times serve as a proxy for memory confidence and memory strength, with faster responses reflecting higher confidence/strength and slower responses suggesting greater uncertainty/weaker memory. The association between reaction times and memory confidence has been established by previous research(58–60), suggesting that the distinction between high from low confidence responses differentiates vividly recalled associations from decisions based on weaker memory evidence. Reaction times are further linked to hippocampal activity during recall tasks(26,53), and stress effects on memory are particularly pronounced for high-confidence memories(53).”

Minor comments:

(5) Please include the full names of key abbreviations in the figure legends, such as "ass.cat.hit" and among others.

We now include the full names of key abbreviations in all figure legends (e.g., ass.cat.hit = associative category hit).

(6) Please introduce various metrics used in the study to aid readers in better understanding the measurements they utilized.

We agree that various measures that were included in our analyses had not been described clearly enough before, especially concerning the multivariate analyses. We therefore added short explanations across the results section.

Page 8, lines 279 to 280: “Classifier accuracy is derived from the sum of correct predictions the trained classifier made in the test-set, relative to the total amount of predictions.”

Page 8, lines 290 to 292:  “Neural reinstatement reflects the extent to which a neural activity pattern (i.e., for objects) that was present during encoding is reactivated during retrieval (e.g., memory cueing).”

Page 8, lines 299 to 301:  “The logits here reflect the log-transformed trial-wise probability of a pattern either representing a scene or an object.”

Page 10, lines 378 to 380:  “Beyond category-level reinstatement, we assessed event-level memory trace reinstatement from initial encoding (Day 1) to memory cueing (Day 2), via RSA, correlating neural patterns in each region (hippocampus, VTC, and PCC) across days.”

(7) Please explain what the different colors represent in Figures 5B and 5C to avoid confusion. It would be good to indicate significant differences in the figures if applicable.

We now added line legends to the figure and also the caption to clarify what exactly is depicted. We added asterisks to mark significant differences.

References:

Monfils, M. H., Cowansage, K. K., Klann, E., & LeDoux, J. E. (2009). Extinction-reconsolidation boundaries: key to persistent attenuation of fear memories. science, 324(5929), 951-955.

Monfils, M. H., & Holmes, E. A. (2018). Memory boundaries: opening a window inspired by reconsolidation to treat anxiety, trauma-related, and addiction disorders. The Lancet Psychiatry, 5(12), 1032-1042.

Lee, J. L. C., Nader, K. & Schiller, D. An Update on Memory Reconsolidation Updating. Trends Cogn. Sci. 21, 531–545 (2017).

Radley, J. J., Williams, B., & Sawchenko, P. E. (2008). Noradrenergic innervation of the dorsal medial prefrontal cortex modulates hypothalamo-pituitary-adrenal responses to acute emotional stress. Journal of Neuroscience, 28(22), 5806-5816.

Heinbockel, H., Wagner, A. D., & Schwabe, L. (2024). Post-retrieval stress impairs subsequent memory depending on hippocampal memory trace reinstatement during reactivation. Science Advances, 10(18), eadm7504.

This statement discusses how the community's values are often portrayed in the schools as they are able to vote in school elections. It is then brought up that this can create "bigotry and zenophobia." Which I think raises a question for schools in general, not just the public ones. And that is; Should we embrace differences from other communities or should we keep it how it is? Now, this is where it gets complicated. Some may ask, why should people who are not a part of "said" community be able to make decisions on it. Another thing is, if this was possible, how effective would it be? Would we see a sharp positive reaction or would it eventually decline?

I think this excerpt can really speak to some people and even help people be more open minded. There are people out there that may be overlooked, or their capabilities may surprise you. Everyone deserves a chance. We should have a goal as society to make better for all so that recognizing brilliance doesnt come from social advantage.

I definitely agree with this statement as lived-experiences and unique needs of a community will always be more in-depth and might present hidden challenges that a designer who has only done research - no matter how extensive - may miss. I think there is a misconception that inclusion is something they can change individually in their life by including more resources and research on a community, but I think it is more of a systemic issue. In general, the principle seems so simple and even beautiful to assume the design we make for the world should be done by communities of the world instead of just a select few who use abstracted information about the world, yet we still struggle with inclusitivity in design.

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

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Reply to the reviewers

We thank the reviewers for their general comment and for the critical evaluation of our analyses and results interpretation. Their comments greatly helped us to improve the manuscript.

• *

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

Summary: An analysis of an Arabidopsis VSP13 presumed lipid transport is provided. The analysis pretty much follows similar studies done on yeast and human homologs. Key findings are the identification of multiple products from the locus due to differential splicing, analysis of lipid binding and transport properties, subcellular location, tissue specific promoter activity, mutant analysis suggesting a role in lipid remodeling following phosphate deprivation, but no physiological or growth defects of the mutants. Major points: The paper is generally written and documented, the experiments are well conducted and follow established protocols. The following major points should be considered:

1. There are complementary lipid binding assays that should be considered such as liposome binding assays, or lipid/western dot blots. All of these might give slightly different results and may inform a consensus. Of course, non-membrane lipids such as TAG cannot be tested in a liposome assay.

Concerning lipid transfer proteins (LTPs), it is important to differentiate the lipid binding capacity related to the transport specificity (which lipids are transported by a LTP?) from the lipid binding capacity linked to the targeting of a LTP to a specific membrane (a LTP can bind a specific lipid via a domain distinct from the lipid transfer domain to be targeted in cells, but will not transport this lipid). Both aspects are of high interest to be determined. Our goal here was to focus on the identification of the lipids bound to AtVPS13M1 and to be likely transported, which is why we used a truncation (1-335) corresponding to the N-term part of the hydrophobic tunnel. Liposome binding assays and lipid dot blots are necessary to answer the question of the membrane binding capacity of the protein. We think that this aspect is out of the scope of the current article as it will require to express and purify other AtVPS13M1 domains that are known to bind lipids such as the two PH domains and the C2. This will be the scope of future investigations in our lab.

Similarly, lipid transfer based only on fluorophore-labeled lipids may be misleading because the fluorophore could affect binding. It is mentioned that the protein in this assay is tethered by 3xHis to the liposomes. Un less I ma missing something, I do not understand how that should work. This needs to be better explained.

We truly agree with Reviewer 1 that the presence of a fluorophore could affect lipid binding to the protein. In this assay, lipids are labeled on their polar head and it is therefore difficult to conclude about the specificity of our protein in term of transport. This assay is used as a qualitative assay to show that AtVPS13M1(1-335) is able to transfer lipids in vitro, and in the manuscript, we did not make any conclusion about its transport specificity based on this assay, but rather used the binding assay to assess the binding, and likely transport, specificity of AtVPS13M1. FRET-based assay is a well-accepted assay in the lipid transfer community to easily probe lipid transport in vitro and has been used in the past to assess transfer capacity of different proteins, including for VPS13 proteins (for examples, see (Kumar et al., 2018; Hanna et al., 2022; Valverde et al., 2019)).

To be able to transfer lipids from one liposome to another, both liposomes have to be in close proximity. Therefore, we attached our protein on donor acceptors, to favor the transport of the fluorescent lipids from the donor to the acceptor liposomes. Then, we progressively increased acceptor liposomes concentration to favor liposome proximity and the chance to have lipid transfer. We added a scheme on Figure 3B of the revised version of the manuscript to clarify the principle of the assay. In addition, we provided further control experiments suggested by Reviewers 2 and 3 showing that the fluorescence signal intensity depend on AtVPS13M1(1-335) protein concentration and that no fluorescence increase is measured with a control protein (Tom20.3) (see Figure 3C-D of the revised manuscript).

The in vivo lipid binding assay could be obscured by the fact that the protein was produced in insect cells and lipid binding occurs during the producing. What is the evidence that added plants calli lipids can replace lipids already present during isolation.

Actually we don’t really know whether the insect cells lipids initially bound to AtVPS13M1(1-335) are replaced by calli lipids or whether they bound to still available lipid binding sites on the protein. But we have two main lines of evidence showing that our purified protein can bind plant lipids even in the presence of insect cells lipids: 1) our protein can bind SQDG and MGDG, two plants specific lipids, and 2) as explained p.8 (lines 243-254), lipids coming from both organisms have a specific acyl-chain composition, with insect cells fatty acids mainly composed of C16 and C18 with 0 or 1 unsaturation whereas plant lipids can have up to 3 unsaturations. By analyzing and presenting on the histograms lipid species from insect cells, calli and those bound to AtVPS13M1(1-335), we were able to conclude that for all the lipid classes besides PS, a wide range of lipid species deriving from both organisms was bound to our protein. The data about the lipid species bound to AtVPS13M1(1-335) are presented in Figure 2E and S2.

The effects on lipid composition of the mutants are not very drastic from what I can tell. Furthermore, how does this fit with the lipid composition of mitochondria where the protein appears to be mostly located?

It is true that lipid composition variations in the mutants are not drastic but still statistically significant. As a general point in the field of lipid transfer, it is not very common to have major changes in total lipidome on single mutants of lipid transfer proteins because of a high redundancy of lipid transport pathway in cells. This is particularly true for VPS13 proteins, as exemplified by multiple studies. Major lipid phenotypes can be revealed in specific conditions, such as phosphate starvation in our case, or when looking at specific organelles or specific tissues and/or developmental stages. This is explained and illustrated by examples in the discussion part p. 16 (line 526-532). In addition, as suggested by Reviewer 3, we performed further lipid analysis on calli and also on rosettes under Pi starvation and found a similar trend (Figure 4 and S4 of the revised version of the manuscript). Thus, we believe that, even if not drastic, these variations during Pi starvation are a real phenotype of our mutants.

As we found that our protein is located at the mitochondrial surface, we agree that Reviewer 1’s suggestion to perform lipidomic analyses on isolated mitochondria will be of high interest but this will be the scope of future studies that we will performed in our lab. First, we would like to identify all the organelles at which AtVPS13M1 is localized before performing subfractionations of these different organelles from the same pool of cell cultures grown in presence or absence of phosphate.

For the localization of the fusion protein, has it been tested whether the furoin is functional? This should be tested (e.g. by reversion of lipid composition).

As we did not observe major developmental phenotypes in our mutants, complementation should be indeed tested by performing lipidomic analyses in calli or plants grown in presence or absence of Pi, which is a time-consuming and expensive experiment. Because we used the fusions mainly for tissue expression study and subcellular localization and not for functional analyses, we believe that this is not an essential control to be performed for this work.

It is speculated that different splice forms are located to different compartments. Can that be tested and used to explain the observed subcellular location patterns?

Indeed some splice forms can modify the sequence of domains putatively involved in protein localization. This could be tested by producing synthetic constructs with one specific exon organization, which is challenging according to the size of AtVPS13M1 cDNA (around 12kb). In addition, our long-read sequencing experiment and PCR analyses revealed the existence of six transcripts, a major one representing around 92% and the five others representing less than 2.5% (Figure 1D). Among the five less abundant transcripts, four produce proteins with a premature stop codon and are likely to arise from splicing defects as explained in the discussion part p. 15 (lines 488-496). One produces a full-length protein with an additional loop in the VAB domain but because of the low abundance of this alternative transcript (1.4%), we believe it does not contribute significantly to the major localization we observed in plants and did not attend to analyze its localization.

GUS fusion data only probe promoter activity but not all levels of gene expression. That caveat should be discussed.

We are aware of this drawback and that is the reason why we fused the GUS enzyme directly to our protein expressed under its native locus (i.e. with endogenous promoter and exons/introns) as depicted in Figure 5A. Therefore, our construction allows to assess directly AtVPS13M1 protein level in plant tissues.

Minor points: 1. Extraplastidic DGDG and export from chloroplasts following phosphate derivation was first reported in PMID: 10973486.

We added this reference in the text.

Check throughout the correct usage of gene expression as genes are expressed and proteins produced.

Many thanks for this remark, we modified the text accordingly

In general, the paper is too long. Redundancies between introduction, results and discussion should be removed to streamline.

We reduced the text to avoid redundancy.

I suggest to redraw the excel graphs to increase line thickness and enlarge font size to increase presentation and readability.

We tried as much as we can to enlarge graphs and font size increasing readability.

Reviewer #1 (Significance (Required)):

Significance: Interorganellar lipid trafficking is an important topic and especially under studied in plants. Identifying components involved represents significant progress in the field. Similarly, lipid remodeling following phosphate derivation is an important phenomenon and the current advances our understanding.

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

Summary: The manuscript "AtVPS13M1 is involved in lipid remodelling in low phosphate and is located at the mitochondria surface in plants" by Leterme et al. identifies the protein VPS13M1 as a lipid transporter in Arabidopsis thaliana with important functions during phosphate starvation. The researchers were able to localise this protein to mitochondria via GFP-targeting in Arabidopsis. Although VPS13 proteins are well described in yeast and mammals, highlighting their importance in many vital cellular processes, there is very little information on them in plants. This manuscript provides new insights into plant VPS13 proteins and contributes to a better understanding of these proteins and their role in abiotic stress responses, such as phosphate starvation.

Major points: - Please describe and define the domains of the VPS13M1 protein in detail, providing also a figure for that. Figure 1 is mainly describing possible splice variants, whereas the characteristics of the protein are missing.

We have added information on AtVPS13M1 domain organization in the introduction (p.4, lines 103-109) and referred to Figure 1A that described protein domain organization. We did not added too much details as plant VPS13 protein domains organization was extensively described in two previous studies cited several times in the manuscript (Leterme et al., 2023; Levine, 2022).

• Please compare the expression level of VPS13M1 in the presence and in the absence of phosphate.

Many thanks for this suggestion. We performed qRT-PCR analyses of AtVPS13M1 from mRNA extracted from calli grown six days in presence and absence of phosphate. The results obtained did not reveal variations in mRNA level. The results were added in Figure S1A of the revised version of the manuscript and discussed in p.5 (lines 154-156).

• Page 9, second paragraph: Here, the lipid transport capability of AtVPS13M1 is described. Varying concentrations of this recombinant protein should be used in this test. Further, it is not highlighted, that a truncated version of VSP13M1 is able to transport lipids. This is surprising, since this truncated version is less than 10% of the total protein (only aa 1-335).

We agree with reviewer 2 that increasing protein concentration is an important control to perform. We included an experiment with an increasing quantity of protein (2X and 4X) in the revised version of the manuscript and showed that the signal intensity increased faster when protein concentration is higher (Figure 3D of the revised manuscript). As requested by Reviewer 3, we also included a negative control with Tom20.3 to show that the signal increase after the addition of AtVPS13M1(1-335) is specific to this protein (Figure 3C of the revised manuscript).

The transport ability of the N-terminal part of VPS13 was demonstrated in yeast and mammals VPS13D (Kumar et al., 2018; Wang et al., 2021). We highlighted this p. 7 (lines 213-218) of the revised version of the manuscript. This is explained by the inherent structure of VPS13 proteins that are composed of several repeats of the same domain type called RBG (for repeating β-groove), each forming a β-sheet with a hydrophobic surface. The higher the number of RBG repeats, the longer the hydrophobic tunnel is. The (1-335) N-terminal region corresponds to two RBG unit repeats forming a “small” tunnel able to bind and transfer lipids. The number of RBG repeats has influence on the quantity of lipids bound per protein in vitro, the longest the protein is, the highest the number of lipid molecules bound is (Kumar et al., 2018), but the effect on protein length on in vitro lipid transfer capacity has not been investigated yet to the best of our knowledge.

• Also, for phenotype analysis, T-DNA insertion mutants are used that still contain VPS13M1 transcripts. Although protein fragments where not detected by proteomic analysis, this might be due to low sensitivity of the proteomic assay. Further the lipid transport domain of VPS13M1 (aa 1-335) might not be affected by the T-DNA insertions at all. Here more detailed analysis needs to be done to prove that indeed loss-of protein function occurs in the mutants.

We do not have other methods than proteomic to test whether our mutants are KO or not. We tried unsuccessfully to produce antibodies. Mass spectrometry is the most sensitive method but the absence of detection indeed does not mean the absence of the protein. From proteomic data, we can conclude that at least, our mutants present a decrease in AtVPS13M1 protein level, thus we called them “knock down” in the revised version of the manuscript and added the following sentence p. 9 (lines 297-300): “As the absence of detection of a protein by mass spectrometry-based proteomics does not allow us to strictly claim the absence of this protein in the sample, we concluded that AtVPS13M1 expression in both atvps13m1-1 and atvps13m1-4 was below the detection limit and consider them as knock down (KD) for AtVPS13M1.”

• Localisation in mitochondria: As the Yepet signal is very weak, a control image of not transfected plant tissue needs to be included. Otherwise, it might be hard to distinguish the Yepet signal from background signal. The localisation data presented in Figure 5 does not allow the conclusion that VPS13M1 is localized at the surface of mitochondria as stated in the title. It only indicates (provided respective controls see above) that VPS13M1 is in mitochondria. Please provide more detailed analysis such as targeting to tobacco protoplasts, immunoblots or in vitro protein import assays. Also test +Pi vs. -Pi to see if VPS13M1 localisation is altered in dependence of Pi.

Indeed our Yepet signal is not very strong but on the experiments we performed on Col0 non-transformed plants, we did not very often see fluorescence background in the leaves’ vascular tissue, that is why we focused our study on this tissue. We sometimes observed some background signals in some cells that are clearly different from AtVPS13M1-3xYepet signals and never co-localized with mitochondria. Examples of these aspecific signals are presented in Figure S6E of the revised version of the manuscript.

We agree with reviewer 2 that our confocal images suggested, but not demonstrated, a localization at the surface of mitochondria. To confirm the localization, we generated calli cell cultures from AtVPS13M1-3xYepet lines and performed subcellular fractionations and western blot analyses confirming that AtVPS13M1 was indeed enriched in mitochondria and also in microsomal fractions (Figure 6G of the revised version). Then we performed mild proteolytic digestion of the isolated mitochondria with thermolysin and show that AtVPS13M1 was degraded, as the outer membrane protein Tom20.3, but not the inner membrane protein AtMic60, showing that AtVPS13M1 is indeed at the surface of mitochondria (Figure 5H of the revised manuscript). We believe that this experiment, in addition to the confocal images showing a signal around mitochondria, convincingly demonstrates that AtVPS13M1 is located at the surface of mitochondria.

The localization of AtVPS13M1 under Pi starvation is a very important question that we tried to investigate without success. Indeed, we intended to perform confocal imaging on seedlings grown in liquid media to easily perform Pi starvation as described for the analysis of AtVPS13M1 tissue expression with β-glucuronidase constructs. However, the level of fluorescence background was very high in seedlings and no clear differences between non-transformed and AtVPS13M1-3xYepet lines were observed, even in root tips where the protein is supposed to be the most highly expressed according to β-glucuronidase assays. Example of images obtained are presented in Figure R1. We concluded that the level of expression of our construct was too low in seedlings. The constructions of lines with a higher AtVPS13M1 expression level, by changing the promotor, to better analyze AtVPS13M1 in different tissues or in response to Pi starvation will be the scope of future work in our laboratory in order to investigate AtVPS13M1 localization under low Pi.

Phenotype analysis needs to be done under Pi stress and not under cold stress! Further, root architecture and root growth should also be done under Pi depletion. Here the title is also misleading, it is not at all clear why the authors switch from phosphate starvation to cold stress.

In the revised version of the manuscript, we analyzed the seedlings root growth of two mutants (atvps13m1-3 and m1-4) under low Pi and did not notice significant differences (Figure 7E, S7D of the revised version). We analyzed growth under cold stress because this stress also promotes remodeling of lipids, but we agree that it goes beyond the scope of this article that is focused on Pi starvation and we removed this part from the revised manuscript.

Minor points: Page 3, line 1: what does the abbreviation VPS stand for?

The definition of VPS (Vacuolar Protein Sorting) was added.

Page 3, line 1: change "amino acids residues" to "amino acid residues"

This was done.

Page 3, line 8 - 12: please rewrite this sentence. You write, that because of their distribution VPS13 proteins do exhibit many important physiological roles. The opposite is true: They are widely distributed in the cell because of their involvement in many physiological processes.

We changed the sentence to “ VPS13 proteins localize to a wide variety of membranes and membrane contact sites (MCSs) in yeast and human (Dziurdzik and Conibear, 2021). This broad distribution on different organelles and MCSs is important to sustain their important roles in numerous cellular and organellar processes such as meiosis and sporulation, maintenance of actin skeleton and cell morphology, mitochondrial function, regulation of cellular phosphatidylinositol phosphates level and biogenesis of autophagosome and acrosome (Dziurdzik and Conibear, 2021; Hanna et al., 2023; Leonzino et al., 2021).”

Page 6, line6: change "cDNA obtained from A. thaliana" to "cDNA generated from A. thaliana.

This was done.

Page 6, line 10: change" 7.6kb" to "7.6 kb"

This was done.

Page 7: address this question: can the isoforms form functional VPS13 proteins? This might help to postulate whether these isoforms are a result of defective splicing events.

We addressed this aspect in the discussion p.15 at lines 486-502.

Figure 2 B: Change "AtVPS13M1"to "AtVPS13M1(1-335)"

This was done.

Figure 2, legend: -put a blank before µM in each case.

This was done.

-Change 0,125µM to 0.125 µM

This was done.

-what does "in absence (A-0µM)" mean?

This means that the Acceptor liposomes are at 0 µM. To clarify, we changed it to “Acceptor 0 µM” in the revised version of the manuscript (Figure 3C).

-Which statistical analysis was employed?

We performed a non-parametric Mann-Whitney test in the revised version of the manuscript. This was indicated in the legend.

-Further, rewrite the sentence "Mass spectrometry (MS) analysis of lipids bound to AtVPS13M1(1-335) or Tom20 (negative control) after incubation with calli total lipids. Results are expresses in nmol of lipids per nmol of proteins (C) or in mol% (D)". -"C" and "D" are not directly comparable, as in "C" no Tom20 was used and in "C" no insect cells were used.

-Further, in "D" the experimental setup is not clear. AtVPS13(1-335) is supposed to be purified protein after incubation with calli lipids (figure 2, A). Further, in the same figure, lipid composition of "insect cells" and "calli-Pi" are compared àwhy? Please clarify this.

C and D are two different representations of the same results providing different types of information. In C., the results are expressed in nmol of lipids / nmol of proteins to assess 1) that the level of lipids found in AtVPS13M1(1-335) purifications is significantly higher than what we can expect from the background (assessed using Tom20) and 2) what are the classes of lipids that associate or not to AtVPS13M1(1-335). In D. the lipid distribution in mol% is presented for AtVPS13M1(1-335) as well as for total extracts from calli and insect cells to be able to compare if one lipid class is particularly enriched or not in AtVPS13M1(1-335) purifications compared to the initial extracts with which the protein was incubated. As an example, it allows to deduce that the absence of DGDG detected in the AtVPS13M1(1-335) purifications is not linked to a low level of DGDG in the calli extract, because it represented around 15 mol%, but likely to a weak affinity of the protein for this lipid. We did not represent the Tom20 lipid distribution on this graph because it represents background of lipid binding to the purification column and might suggest that Tom20 binds lipids. We changed the legend in this way and hope that it is clearer now: “C-D. Mass spectrometry (MS) analysis of lipids bound to AtVPS13M1(1-335) or Tom20 (negative control) after incubation with calli total lipids and repurification. Results are expresses in nmol of lipids per nmol of proteins in order to analyze the absolute quantity of the different lipid classes bound to AtVPS13M1(1-335) compared to Tom20 negative control (C), and in mol% to assess the global distribution of lipid classes in AtVPS13M1(1-335) purifications compared to the total lipid extract of insect cells and calli (D).”

Figure 3: -t-test requires a normal distribution of the data. This is not possible for an n=3. Please use an adequate analysis.

We performed more replicates and used non-parametric Mann-Whitney analyses in the revised version of the manuscript.

-Please clarify the meaning of the letters on the top of the bars in the legend.

This corresponded to the significance of t-tests performed in the first version of the manuscript that were reported in Table S3. As in the new version we performed Mann-Whitney tests, we highlighted the significance by stars and in the figure legends.

Please, make it clear that two figures belong to C.

This was clarified in the legend.

-Reorganise the order of figure 3 (AàBàCàD)

Because of the configuration of the different histograms presented in the figure, we were not able to change the order but we believed that the graphs can be easily red this way.

Page 10, 3. Paragraph: since the finding, that no peptides were found in the VSP13M1 ko lines, although transcription was not altered, is surprising, please include the proteomic data in the supplement

Proteomic data were deposited on PRIDE with the identifier PXD052019. They will remain not publicly accessible until the acceptance of the manuscript.

Page 11, line 17: The in vitro experiments showed a low affinity of VSP13M1 towards galactolipids. It is further claimed that this is consistent with the finding of the AtVSP13M1 Ko line in vivo, that in absence of PI, no change in DGDG content could be observed. However, the "absence" of VSP13M1 in vivo might still result in a bigger VSP13M1 protein, than the truncated form (1-335) used for the in vitro experiments

It is true that our in vitro experiments were performed only with a portion of AtVPS13M1 and that the length of the protein could influence protein binding specificity. We removed this assessment from the manuscript.

Page 13, lane 8: you should reconsider the use of a triple Yepet tag: If two or more identical fluorescent molecules are in close proximity, their fluorescence emission is quenched, which results in a weak signal (as the one that you obtained). See: Zhuang et al. 2000 (PNAS) Fluorescence quenching: A tool for single-molecule protein-folding study

Many thanks to point this paper. We use a triple Yepet because AtVPS13M1 has a very low level of expression and because this strategy was used successfully to visualize proteins for which the signal was below the detection level with a single GFP (Zhou et al., 2011). The quenching of the 3xYepet might also depend on the conformation they adopt on the targeting protein.

Page 13, line 14: change 1µm to 1 µm

This was done.

Page 13, line 29: please reduce the sentence to the first part: if A does not colocalize with B, it is not necessary to mention that B does not colocalise with A.

The sentence was modified accordingly.

Page 14, 2. Paragraph: it is not conclusive that phenotype analysis is suddenly conducted with plants under cold stress, since everything was about Pi-starvation and the role of VSP13M1. Lipid remodelling under Pi stress completely differs from the lipid remodelling under cold stress.

We eliminated this part in the revised version of the manuscript.

Page 14, line 20: change figure to Figure

This was done.

Page 07, line 17: change artifact to artefact

This was done.

Reviewer #2 (Significance (Required)):

General assessment: The paper is well written and technically sound. However, some points could be identified, that definitely need a revision. Overall, we got the impression that so far, the data gathered are still quite preliminary and need some more detailed investigations prior to publication (see major points).

Advance: The study definitely fills a gap of knowledge since not much is known on the function of plant VPS13 proteins so far.

Audience: The study is of very high interest to the plant lipid community but as well of general interest for Plant Molecular Biology and intracellular transport.

Our expertise: Plant membrane transport and lipid homeostasis.

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

The manuscript by Leterme et al. (2024) describes the characterization of VPS13M1 from Arabidopsis. VPS13 proteins have been analyzed in yeast and animals, where they establish lipid transfer connections between organelles, but not much is known about VPS13 proteins in plants. First, different splicing forms were characterized, and the form A was identified as the most relevant one with 92% of the transcripts. The protein (just N-terminal 335 amino acids out of ca. 3000 amino acids) was expressed in insect cells and purified. Next, the protein was used for lipid binding assays with NBD-labeled lipids followed by analysis in polyacrylamide gel electrophoresis. VPS13M1 bound to PC, PE, PS and PA. Then, the protein from insect cells was incubated with Arabidopsis callus lipids, and lipids bound to VPS13M1 analyzed by LC-MS/MS. Lipid transfer between liposomes was measured by the change in fluorescence in donor liposomes derived from two labeled lipids after addition of the protein caused by lipid transfer and dilution to acceptor liposomes. T-DNA insertion mutants were isolated and the lipids measured in callus derived from these mutants. Protein localization in different plant organs was recorded with a GUS fusion construct transferred into transgenic plants. The protein was localized to mitochondria using a VPS13M1-Yepet fusion construct transferred into mutant plants. The mutant plants show no visible difference to wild type, even when the plants were grown under stress conditions like low temperature. The main message of the title is that VPS13M1 localizes to the mitochondria which is well documented, and it is involved in lipid remodeling under low phosphate conditions.

The lipid transfer assay shown in Figure 2F lacks a negative control. This would be the experiment with donor and acceptor liposomes in the presence of another protein like Tom20.

Many thanks for this suggestion. In the revised version of the manuscript, we performed a fluorescent lipid transport assay with Tom20.3 in the presence of 25 µM of donor liposomes and 1.5 mM of acceptor liposomes, the condition for which we observed a maximum of transport for AtVPS13M1(1-335). As expected, no fluorescence increase was observed. The results are presented in the Figure 3C of the revised manuscript.

The lipid data (Fig. 3 and Fig. S4) do not sufficiently support the second claim, i.e. that the protein is involved in lipid remodeling under low P. Data in Fig. 3C are derived from only 3 replicates and in Fig. S4 from only 2 replicas with considerable error bars. Having only 2 replicates is definitely not sufficient. Fig. 3C shows a suppression in the decrease in PE and PC at 4 d of P deprivation (significant for two mutants for PE, for only one for PC). Fig. S4A shows suppression of the decrease in PC at 6 d after P deprivation (significant for both mutants), but no significant effect on PE. Fig. 4SB shows no significant change in PE or PC at -P after 8 d of P deprivation. The data are not consistent. There are also problems with the statistics in Fig. 3 and Fig. S4. The authors used T-test, but place letters a, b, c on top of the bars. Usually, asterisks should be used to indicate significant differences. Data indicate medians and ranges, not mean and SD. In Fig. S4, how can you indicate median and range if you have only 2 replicates? Why did the authors use callus for lipid measurements? Why not use leaves and root tissues? What does adjusted nmol mean? What does the dashed line at 1.05 on the y axis mean? Taken together, I suggest to repeat lipid measurements with leaves and roots from plantets grown under +P and -P conditions in tissue culture with 5 replcates. Significant differences can be analyzed on the level of absolute (nmol per mg FW/DW) or relative (%) amounts.

Here are our answers to concerns about the design of our lipidomics experiments:

We used calli for lipid measurement because it is very easy to control growth conditions and to performed phosphate starvation from this cell cultures. The second reason is that it is a non-photosynthetic tissue with a high level of phospholipids and a low level of galactoglycerolipids and it is easier to monitor the modification of the balance phospholipids/galactoglycerolipids in this system. The lipid analysis on calli at 4 days of growth in presence or absence of Pi were performed on 3 biological replicates but on two different mutants (atvps13m-1 and m1-3) and we drew our conclusions based on variations that were significant for both mutants. In the revised version of the manuscript, we performed further lipidomic analyses on calli from Col0 and another mutant (atvps13m1-2) after 6 days of growth in presence or absence of Pi (Figure 4E, S4A-C, n=4-5) and added new data on a photosynthetic tissue (rosettes) from Col0 and atvps13m1-3 mutant. For rosettes analysis, seeds were germinated 4 days in plates with 1 mM Pi and then transferred on plates with 1 mM or 5 µM of Pi. Rosettes were harvested and lipids analyzed after 6 days (Figure 4F-G, S4D, n=4-5). All the data were represented with medians and ranges because we believe that median is less sensitive to extreme values than mean and might better represent what is occurring. Ranges highlight the minimal and maximal value of the data analyzed and we believe it is a representative view of the variability we obtained between biological samples.

Lipid measurement are done by mass spectrometry. As it was already reported, mass spectrometry quantification is not trivial as the intensity of the response depends on the nature of the molecule (for a review, see (Jouhet et al., 2024)). To counteract this ionisation problem, we developed a method with an external standard that we called Quantified Control (QC) corresponding to an A. thaliana callus lipid extract for which the precised lipid composition was determined by TLC and GC-FID. All our MS signals were “adjusted” to the signal of this QC as described in (Jouhet et al., 2017). Therefore our lipid measurement are in adjusted nmol. In material and method we modified the sentence accordingly p22 lines 720-723: “Lipid amounts (pmol) were adjusted for response differences between internal standards and endogenous lipids and by comparison with a quality control (QC).” This allows to represent all the lipid classes on a same graph and to have an estimation of the lipid classes distribution. To assess the significance of our results, we used in the revised version of the manuscript non-parametric Mann-Whitney tests and added stars representing the p-value on charts. This was indicated in the figure legends.

Here are our answers to concerns about the interpretation of our lipidomics experiments:

To summarize, in the revised version of the manuscript, lipid analyses were performed in calli from 3 different mutants (two at day 4, one at day 6) and in the rosettes from one of these mutants. All the results are presented in Figure 4 and S4. In all the experiments, we found that in +Pi, there is no major modifications in the lipid content or composition. In –Pi, we found that the total glycerolipid content is always higher in the mutant compared to the Col0, whatever the tissue or mutant considered (Figure 4A and S4A, D). In calli, this higher increase in lipid content is mainly due to an accumulation of phospholipids and in rosettes, of galactolipids. Because of high variability between our biological replicates, we did not always found significant differences in the absolute amount of lipids in –Pi. However, the analysis of the fold change in lipid content in –Pi vs +Pi always pointed toward a reduced extent of phospholipid degradation. We also added in these graphs the fold change for the total phospholipids and total galactolipids contents in the revised version of the manuscript. We believe that the new analyses we performed strengthen our conclusion about the role of AtVPS13M1 in phospholipid degradation and not on the recycling of precursors backbone to feed galactoglycerolipids synthesis at the chloroplast envelope.

Page 9, line 15: Please use the standard form of abbreviations of lipid molecular species with colon, e.g. PC32:0, not PC32-0

The lipid species nomenclature has been changed accordingly.

Page 11, line 4, (atvps13m1.1 and m1.3: please indicate the existence of mutant alleles with dashes, i.e. (atvps13m1-1 and atvps13m1-3

Names of the mutants have been changed accordingly.

Page 14, line 21: which line is indicated by atvps13m1.2-4? What does -4 indicate here?

This indicates that mutants m1-2 to m1-4 were analyzed.

Page 16, line 25: many abbreviations used here are very specific and not well known to the general audience e.g. ONT, IR, PTC, NMD etc. I think it is OK to mention them here, but still use the full terms, given that they are not used very frequently in the manuscript.

We kept ONT abbreviation because it was cited many times in both the results and discussion part. IR, PTC and NMD were cited only in the discussion and were eliminated.

Page 19, line 11. The authors cite Hsueh et al and Yang et al for LPTD1 playing a role in lipid homeostasis during P deficiency. But Yang et al. described the function of a SEC14 protein in Arabidopsis and rice during P deficiency. Is SEC14 related to LPTD1?

Many thanks for noticing this mistake. We removed the citation Yang et al. in the revised version of the manuscript.

Reference Tangpranomkorn et al. 2022: In the text, it says that this is a preprint, but in the Reference list, this is indicated with "Plant Biology" as Journal. In the internet, I could only find this manuscript in bioRxiv.

This manuscript was accepted in “New Phytologist” in December 2024 and is now cited accordingly in the new version of the manuscript.

Reviewer #3 (Significance (Required)):

The manuscript by Leterme et al describes the characterization of the lipid binding and transport protein VTPS13M1 from Arabidopsis. I think that the liposome assay needs to be done with a negative control. Furthermore, I have major concerns with the lipid data in Fig. 3C and Fig. S4. These lipid data of the current manuscript need to be redone. I do not agree that the lipid data allow the conclusion that "AtVPS13M1 is involved in lipid remodeling in low phosphate" as stated in the title.

References cited in this document:

Dziurdzik, S.K., and E. Conibear. 2021. The Vps13 Family of Lipid Transporters and Its Role at Membrane Contact Sites. Int J Mol Sci. 22:2905. doi:10.3390/ijms22062905.

Hanna, M., A. Guillén-Samander, and P. De Camilli. 2023. RBG Motif Bridge-Like Lipid Transport Proteins: Structure, Functions, and Open Questions. Annu Rev Cell Dev Biol. 39:409–434. doi:10.1146/annurev-cellbio-120420-014634.

Hanna, M.G., P.H. Suen, Y. Wu, K.M. Reinisch, and P. De Camilli. 2022. SHIP164 is a chorein motif lipid transfer protein that controls endosome–Golgi membrane traffic. Journal of Cell Biology. 221:e202111018. doi:10.1083/jcb.202111018.

Jouhet, J., E. Alves, Y. Boutté, S. Darnet, F. Domergue, T. Durand, P. Fischer, L. Fouillen, M. Grube, J. Joubès, U. Kalnenieks, J.M. Kargul, I. Khozin-Goldberg, C. Leblanc, S. Letsiou, J. Lupette, G.V. Markov, I. Medina, T. Melo, P. Mojzeš, S. Momchilova, S. Mongrand, A.S.P. Moreira, B.B. Neves, C. Oger, F. Rey, S. Santaeufemia, H. Schaller, G. Schleyer, Z. Tietel, G. Zammit, C. Ziv, and R. Domingues. 2024. Plant and algal lipidomes: Analysis, composition, and their societal significance. Progress in Lipid Research. 96:101290. doi:10.1016/j.plipres.2024.101290.

Jouhet, J., J. Lupette, O. Clerc, L. Magneschi, M. Bedhomme, S. Collin, S. Roy, E. Maréchal, and F. Rébeillé. 2017. LC-MS/MS versus TLC plus GC methods: Consistency of glycerolipid and fatty acid profiles in microalgae and higher plant cells and effect of a nitrogen starvation. PLoS ONE. 12:e0182423. doi:10.1371/journal.pone.0182423.

Kumar, N., M. Leonzino, W. Hancock-Cerutti, F.A. Horenkamp, P. Li, J.A. Lees, H. Wheeler, K.M. Reinisch, and P. De Camilli. 2018. VPS13A and VPS13C are lipid transport proteins differentially localized at ER contact sites. J Cell Biol. 217:3625–3639. doi:10.1083/jcb.201807019.

Leonzino, M., K.M. Reinisch, and P. De Camilli. 2021. Insights into VPS13 properties and function reveal a new mechanism of eukaryotic lipid transport. Biochimica et Biophysica Acta (BBA) - Molecular and Cell Biology of Lipids. 1866:159003. doi:10.1016/j.bbalip.2021.159003.

Leterme, S., O. Bastien, R.A. Cigliano, A. Amato, and M. Michaud. 2023. Phylogenetic and Structural Analyses of VPS13 Proteins in Archaeplastida Reveal Their Complex Evolutionary History in Viridiplantae. Contact (Thousand Oaks). 6:1–23. doi:10.1177/25152564231211976.

Levine, T.P. 2022. Sequence Analysis and Structural Predictions of Lipid Transfer Bridges in the Repeating Beta Groove (RBG) Superfamily Reveal Past and Present Domain Variations Affecting Form, Function and Interactions of VPS13, ATG2, SHIP164, Hobbit and Tweek. Contact. 5:251525642211343. doi:10.1177/25152564221134328.

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Reviewer 1. Rie Shimizu

This manuscript deciphers the complicated genome of an octoploid species, Cardamine chenopodiifolia. They successfully assembled a chromosome-level genome with 32 chromosomes, consistent with the chromosome counting. They evaluated the quality of the genome by several methods (mapping Omni-C reads, BUSCO, variant calling etc.). All benchmarks ensured the high quality of their assembly. They even tried to phase the chromosomes into four subgenomes, and one subgenome was successfully phased thanks to its higher divergence compared to the other three sets. Despite their intensive effort, the other three subgenomes could not be phased, suggesting the relationship originated from the same or closely related species. As a whole, the manuscript is very well written and describes enough details, and the genome data looks like it is already available in a public database. They even added a description of the biological application of this assembly about the amphicarpy.

I only found a few minor points for which I kindly suggest reconsideration/rephrasing before publication, as listed below. *As the review PDF does not contain the line numbers, I suggest the original description at the first line and then write my comments.

–C. chenopodiifolia genome is octoploid …, suggesting that its genome is octoploid. They compare the 8C peak of C. hirsuta and 2C peak of the target, but considering the genome size variation among Cardamine species, I do not think this is an appropriate expression. The pattern may mean ‘consistent’ with the expectation from C. hirsuta peaks but does not ‘suggest’ octoploidy. -C. chenopodiifolia chromosome-level genome assembly PacBio Sequel II platform. Here and nowhere, they do not mention the mode of sequencing (only found in method and the title of a table). Maybe ‘HiFi’ could be added here to make the method clearer. -Table 2. It would make more sense to overview the genome quality if the N90 and L90 (or similar, if it is already fragmented at L90) values are added. (maybe the same for Table 1). Otherwise Nx curves would be also fine for the same purpose. -We obtained only 20800 variants,…as expected for a selfing species. It might be partially due to selfing in wild habitat, but also by selfing (5 times) in the lab. This should be mentioned here to avoid misleading. -Table 4 The unit of each item (bp, number, frequency…?) should be suggested. In addition to the points listed above, I appreciate more Information about the phased chromosomes set: Total subgenome sizes of this set and the other three sets?(1:3 or imbalanced?) It would be even better with a synteny plot in addition to the colinear plot as Fig 3C. (e.g. by GENESPACE or something similar, including phased and unphased chenopodiifolia chromosome sets and C. hirsuta)

Reviewer 2. .Qing Liu

This manuscript “Polyploid genome assembly of Cardamine chenopodiifolia” produced a chromosome-scale assembly of the octoploid C. chenopodiifolia genome using highfidelity long read sequencing with the Pacific Biosciences platform with two organelle genomes with a total length of 597.2 Mb and an N50 of 18.8 Mb together with BUSCO analysis (99.8% genome completeness), and phased one of the four sub-genomes. This study provides a valuable resource to investigate the understudied trait of amphicarpy and the origin of new traits by allopolyploidy. The manuscript is suitably edited and significant data for amphicarpy breeding of C. chenopodiifolia except for the below revision points. The major revision is suggested for the current version of the manuscript.

1 Please elucidate “an N50 of 18.8 Mb”, which is Contig or Scaffold N50 length. 2 Please elucidate “originated via allo- rather than auto-polyploidy”, which is “originated via allopolyploidy rather than autopolyploidy”. 3 Please substitute the word “understudied trait” using alternative sensible word. 4 “to phase this set of chromosomes by gene tree topology analysis”, it is suggested to be “to phase this set of chromosomes by gene phylogeney analysis”. 5 In the first section of Resuts, Cardamine chenopodiifolia genome is octoploid is suggested. 6 Could Table 1 and Table2 be combined as one table to present the sequencing and assembly characterization of C. chenopodiifolia genome. 7 Could the entromere locations be predicted in Table 5, which is the 32 chromosome summary of C. chenopodiifolia genome. 8 In Table 2, assembly 32 chromosomes including two organelles, which is not close related with the C. chenopodiifolia genome, from my point of view, two organelle genome assembly do not critical section of manuscript. 9 Could all figure numbers are ordered below each group figures, for example the below figure should be numbered before the Figure 2A (according group figure presence order). I wonder it is Figure 2, authors want to elucidate the chromosome number 2n=42, while I can’t count out 42 chromosomes from present format.Could authors using alternative clear figure to show the cytological evidence of C. chenopodiifolia chromosome number. 10 In Figure 5A, it is difficult to point out the clear meaning for first-diverged chromosome from gene tree, which is a phylogenetic meaning tree or just framework, could author redraw this Figure 5A in order to reader got what you mean.

Reviewer 3. Kang Zhang.

The paper produced a chromosome-scale assembly of the C. chenopodiifolia genome in the Brassicaceae family, and offers a valuable resource to investigate the understudied trait of amphicarpy and the origin of new traits by allopolyploidy. I have the following comments which can be considered to improve the ms.

Major points. 1.The introduction states that Cardamine is among the largest genera within the Brassicaceae family. The octaploid model species C. occulta and the diploid C. hirsuta have been sequenced. Therefore, I propose that a description of the evolutionary relationships among various species be included here. Additionally, the significance of the amphicarpic trait in the study of plant evolution and adaptation could be highlighted when discussing their octoploid characteristics. 2.The paper omits a detailed description of genome annotation and significant genomic features, which are essential for clearly illustrating the characteristics of the genome. To enhance this aspect, it would be beneficial to include a circular chart that displays fundamental components such as gene density, CG content, TE density, and collinearity links, among others. 3.The authors employed various techniques to differentiate the four subgenomic sets within the C. chenopodiifolia genome and ultimately managed to isolate a single sub-genomic set. The paper references the assembly of the octaploid genome of another model plant, C. occulta, within the same genus. Could it be utilized to compare with C. chenopodiifolia to achieve improvements? In addition, I suggest the authors to examine the gene density differences among these subgenomes, which could be helpful in distinguishing them. 4.Little important information were included in Table 1, 3, and Figure 4. These tables and figures should be moved to Supplementary data. 5.Evidence from Hi-C heatmap should be provided to validate the structural variations among different sets of subgenomes, such as those in Figure 3.

Minor points. 1.Figure 5B, please change the vertical coordinate ‘# gene pairs’ to ‘Number of gene pairs’. The fonts in some figures are a little bit small. I suggest to adjust them to make it easy to read.

This work has been published in GigaByte Journal under a CC-BY 4.0 license (https://doi.org/10.46471/gigabyte.144). These reviews are as follows.

Reviewer 1. Darrin T. Schultz

Are all data available and do they match the descriptions in the paper?

No. The genome is also not yet on NCBI, but it would be good to upload it.

Are the data and metadata consistent with relevant minimum information or reporting standards?

Yes. I suggest later that there should be more information about the HiFi library preparation details, as the manuscript lacks them and it appears to be a non-standard (large insert size) library.

Is the data acquisition clear, complete and methodologically sound?

No. See above comment-

Is there sufficient detail in the methods and data-processing steps to allow reproduction?

No. No parameters are provided for the genome assembly software, for read trimming, or for other software used.

Is there sufficient data validation and statistical analyses of data quality?

No. See extended comments - the read data could use more QC, as well as the genome assembly.

Is the validation suitable for this type of data?

No.

Is there sufficient information for others to reuse this dataset or integrate it with other data?

Yes. There is a degree of information missing about the data, but another researcher could use them for their study.

Additional Comments:

Thank you for the opportunity to review the work, The genome of the sapphire damselfish Chrysiptera cyanea: a new resource to support further investigation of the evolution of Pomacentrids, by Gairin and colleagues. In this manuscript, the authors collect an individual of the pomocentrid fish, Chrysiptera cyanea, in Okinawa, Japan. After isolating DNA, the sequencing center at OIST prepared and sequenced a SMRT sequencing library. Additionally, the authors generated some bulk RNA-seq data and sequenced it on the Illumina platform. The authors assembled the genome with two assemblers, and performed some comparisons of the C. cyanea contigs aligned to the chromosome-scale scaffolds of closely related pomacentrids. Given my background, I will mostly comment on the genomic analyses.

I appreciate the authors' diligence in exploring different genome assembly methods and their efforts in running BUSCO and QUAST to QC the assemblies. The DNA sequencing data and assembly produced contigs that align well with the chromosomes of closely related species (which is convenient for comparative genomics!), and the manuscript presents a solid foundation for better understanding the chromosomal evolutionary history of the Pomacentridae.

While this work represents an important step toward providing a new genomic resource for Chrysiptera cyanea, I see a few areas where the manuscript could be refined to enhance it as a community resource:

(1) More information about data generation: Including additional details about the HiFi library preparation, specifically the chemistries used, the number of SMRT cells sequenced, and the bioinformatics steps used to generate the HiFi reads, would improve the manuscript's clarity and reproducibility. I have some questions regarding whether these libraries were prepared for HiFi sequencing: the reported mean read length of 25kbp is 10kbp longer than the standard HiFi library insert size; and the reported amount of bases in the reads, 84 Gbp, is more data than one would expect from a single CCS-processed SMRT cell, but could be the amount of data produced from one CLR run. Characterizing the quality score vs read length distribution could be helpful to characterize the read data. Clarifying these steps taken before the genome was assembled would strengthen the reliability of these reads as a resource.

(2) Incorporating a few more important quality control (QC) steps would better clarify the completeness of the genome assembly. For instance, an estimate of genome size from the HiFi reads could be performed with jellyfish and GenomeScope, taking advantage of the k-mer fidelity of HiFi reads. This would provide a more conclusive estimate than the current comparison. Additionally, steps such as checking for contamination and providing an explanation for decisions like haplotig removal would make the assembly process more transparent. Lastly, supplementing the QC analysis with Merqury will provide a reliable answer to how complete the assembly represents the information in the individual HiFi reads in a way that complements BUSCO and QUAST.

(3) The initial analyses of chromosome structure are a promising look into some yet-unexplored chromosomal changes in the Pomacentridae, and I think that incorporating a deeper phylogenetic analysis would build on this strength. Situating the chromosomal findings within a phylogenetic framework could provide stronger support, or actually resolve, the evolutionary interpretations presented. Doing this analysis likely could also help resolve whether the structures seen are genome misassemblies, or instead reflect lineage-specific chromosomal changes. The authors could supplement their beautiful figures using other tools that leverage whole-genome alignments and chromosome visualization to help answer these questions. One tool to try for two-genome comparisons, that the authors may have explored already in place of their ggplot script, is D-GENIES.

Overall, this is a valuable resource, and I commend the authors for taking the steps to analyze the chromosomal evolutionary history within the pomacentrids. I look forward to seeing the authors’ future contributions to the field of genomics and chromosome evolution.

Minor Points Line 125: Sharing the specific Trimmomatic settings used would enhance the reproducibility of the RNA-seq data processing. The parameters for genome assembly should also be added. Line 212: Are there any replicates for the RNA-seq data? Line 294: Consider uploading the assembly to NCBI for broader visibility and accessibility.

Reviewer 2. Yue Song.

Are all data available and do they match the descriptions in the paper?

No. The authors have provided clues for accessing the data in public databases such as NCBI, but it seems that the data has not been released; At least, I haven't been able to obtain available data using the provided accession number (e.g. PRJNA1167451). I'm not sure if I've missed any information, but I believe it would be better if the data could be easily accessible to the public.

Is the data acquisition clear, complete and methodologically sound?

No. The authors used PacBio's third-generation sequencing technology for genome sequencing, which has become a "necessary option" for obtaining high-quality genomes in current genomic research. However, they did not further advance on the path of "assembling a chromosome-level genome" based on this version. Providing a chromosome-level genome would likely be more meaningful.

Is there sufficient detail in the methods and data-processing steps to allow reproduction?

No. Regarding the genome assembly and annotation process, the method described by the authors is overly simplistic and lacks detailed information on the parameters and procedures used. This makes it difficult for other researchers to effectively replicate the results described in the article.

Is there sufficient data validation and statistical analyses of data quality?

No. The authors have calculated the N50 of contigs and the completeness of BUSCO genes, which are indeed two commonly used indicators for assessing the quality of genome assemblies. However, it is still challenging to gain a clear understanding of the assembly quality based solely on these two indicators. Could other measurements be added, such as comparing the continuity and completeness of the assembly with those of closely related species or other comparable species' genomes? Additionally, there is a point that is difficult to understand: the authors report a BUSCO completeness of approximately 94% for the genome, yet a BUSCO completeness of 97% for the gene set. It is puzzling how BUSCO genes that are not annotated in the genome can still be present in the gene set.

Is there sufficient information for others to reuse this dataset or integrate it with other data?

No. As I mentioned earlier, the authors did not provide detailed information about the processing procedures and parameters, which makes it difficult for other researchers to replicate their results.

Additional Comments: It is recommended that the authors provide a detailed description of the methods and easily accessible data retrieval methods. It would be even better if the authors could further provide a chromosome-level genome, as T2T (telomere-to-telomere) level genomes are becoming increasingly popular.

Reviewer #2 (Public review):

Summary:

This paper by Misra and Pessoa uses switching linear dynamical systems (SLDS) to investigate the neural network dynamics underlying threat processing at varying levels of proximity. Using an existing dataset from a threat-of-shock paradigm in which threat proximity is manipulated in a continuous fashion, the authors first show that they can identify states that each has their own linear dynamical system and are consistently associated with distinct phases of the threat-of-shock task (e.g., "peri-shock", "not near", etc). They then show how activity maps associated with these states are in agreement with existing literature on neural mechanisms of threat processing, and how activity in underlying brain regions alters around state transitions. The central novelty of the paper lies in its analyses of how intrinsic and extrinsic factors contribute to within-state trajectories and between-state transitions. A final set of analyses shows how the findings generalize to another (related) threat paradigm.

Strengths:

The analyses for this study are conducted at a very high level of mathematical and theoretical sophistication. The paper is very well written and effectively communicates complex concepts from dynamical systems. I am enthusiastic about this paper, but I think the authors have not yet exploited the full potential of their analyses in making this work meaningful toward increasing our neuroscientific understanding of threat processing, as explained below.

Weaknesses:

(1) I appreciate the sophistication of the analyses applied and/or developed by the authors. These methods have many potential use cases for investigating the network dynamics underlying various cognitive and affective processes. However, I am somewhat disappointed by the level of inferences made by the authors based on these analyses at the level of systems neuroscience. As an illustration consider the following citations from the abstract: "The results revealed that threat processing benefits from being viewed in terms of dynamic multivariate patterns whose trajectories are a combination of intrinsic and extrinsic factors that jointly determine how the brain temporally evolves during dynamic threat" and "We propose that viewing threat processing through the lens of dynamical systems offers important avenues to uncover properties of the dynamics of threat that are not unveiled with standard experimental designs and analyses". I can agree to the claim that we may be able to better describe the intrinsic and extrinsic dynamics of threat processing using this method, but what is now the contribution that this makes toward understanding these processes?

(2) How sure can we be that it is possible to separate extrinsically and intrinsically driven dynamics?

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Reply to the reviewers

Response to Reviewers

We thank the reviewers for their fair and thorough review. With regards to the reviewers’ comments, both largely focused on something that is a misunderstanding. For unclear reasons, both reviewers thought that most of the data shown was in pregnant or previously pregnant mice and both requested a significant amount of preliminary data regarding virgin mice (R1 comment #3, #4, R2 comment #1). This may be due to a (now-corrected) typo in the results section despite the methods section being correct, or the very few instances of pregnant mice being used for analyses that led to confusion. As mentioned below, the entire manuscript evaluates virgin mice, with a few specific exceptions, so the preliminary revisions have emphasized the parity status of the mice used in every experiment. We regret this misunderstanding happened and we are concerned this may have led to reviews that were biased towards a negative viewpoint. We hope the completed preliminary revisions (indicated in red text in the manuscript) and the planned revisions will, combined, satisfy the reviewer’s concerns and clarify points of confusion, while leading to a greatly improved manuscript.

Reviewer 1:

Major points

1. Major Comment 1: “Several of the conclusions are made based on a limited number of replicates (often n=3) which is not a robust sample size to make a rigorous conclusion.”

We have consulted with a biostatistician (Adam Lane, now included in acknowledgements) and plan to add at least 3 more mice per group to bring the total sample size to 6-7. Given our results are already statistically significant with an n=3-4, we do not anticipate any changes in the overall results of our data. We have already collected at least 3 more age-matched and parity-matched mice per group for the molecular analyses and are working on performing the immunohistochemical stains, western blots, etc.

Major Comment 2: The main text for Figure 1C mentions repression of luciferase expression by doxycycline chow, however the figure does not show any discernable repression in the Dek-OE conditions.

We believe the reviewer may have mis-interpreted the figure. The mouse on the far left (“control”) with no luciferase signal is the dox chow-repressed condition. We have revised the figure label to specify that “Control” is the “+dox condition” and throughout the manuscript have specified “+dox controls” instead of just “controls.”

Major Comments 3: To evaluate the impact of prolonged Dek overexpression on mammary epithelium in Figure 1G and 1H, the authors used multiparous females. One confounding factor with this experimental set up is the impact of previous pregnancies on the development of the mammary epithelium and in lowering tumorigenesis. Therefore, the impact of Dek on tumorigenesis cannot be determined in multiparous animals alone. To get a full picture, nulliparous animals should also be examined.

__We have revised the text on page 6 to explain that we have monitored tumor growth in both aged virgins and in multiparous mice (our female breeders) and neither group develops tumors. __

Major Comment 4: “To elucidate the molecular underpinning of Dek-OE phenotypes, the authors performed bulk RNA sequencing in Figure 2. Similar to point 2 however, only multiparous animals were used. As it has been previously shown that pregnancy significantly impacts the transcriptome of mammary glands, the effects of Dek overexpression can't be generalized to mammary glands as a whole. To make it generalizable, nulliparous Dek-OE animals must also be characterized.”

As mentioned in the introduction to the review, the reviewer has misunderstood the experimental design, perhaps through a single typo in the Results section when the Methods were correct, or through poor writing on our behalf. Regardless, the RNA-Seq, whole mounts, and all subsequent molecular validations were conducted on virgin mice. The only exceptions are in Figure 4, where we do explore the expression of endogenous Dek during pregnancy and the impact of pregnancy in the transgenic model. We have revised the typographical error, confirmed the parity status of all mice in the study to date, and have specifically added the parity status to each experiment in Results section and/or Figure Legend.

Major Comment 5: To validate findings from their transcriptomics work, the authors used IHC and western blots of candidate proteins that were found to be down regulated. In Figure 3A and 3C, the decrease in p21 protein levels through western blot seem much more modest than what the decrease seen in 3A would suggest.

We thank the reviewer for pointing this out. With increased sample sizes, as requested, we hope this will resolve. We plan to increase sample size and quantify the p21 western blot to potentially resolve the concern. In addition, we would like to note that the p21 IHC is specific for mammary epithelium signal while the western blot is whole mammary gland lysate that includes quiescent stromal cells, which may explain the slight discrepancy between the two methods.

Major Comment 6: In Figure 3G-3I, the authors test the CDK4/6 inhibitor palbociclib to establish a direct link between the phenotypes seem in Dek-OE and cell cycle progression in organoid culture. Have the authors verified these findings with treatment of Dek-OE mice with palbociclib? In addition, have the authors checked to see if palbociclib corrected any of the transcriptional features associated with the Dek-OE model found in their transcriptomics data? In addition, the authors claim that the effect is specific to Dek-OE organoids as the effects of palbociclib on growth are not seen in control organoids. However, the data on unperturbed growth of control cells are not seen. To determine the specificity of the effects of palbociclib on Dek-OE derived organoids, the authors must show a time course tracking the growth of organoids with and without palbociclib. Rather than conclude the effects of palbociclib being specific to Dek-OE organoids, the authors most likely wanted to conclude that the increased growth of Dek-OE organoids compared to control organoids is dependent on the increase in cell cycle factors. (The validity of this is also weird though because even if division and growth were triggered through other transcriptional changes they found, like increased metabolism, growth in that scenario would be stopped by palbo as well)

1. Because the hyperplasia phenotype accumulates over the lifetime of the animal, the amount of treatment time required to abrogate the hyperplasia phenotype could be from days to weeks to months. For this reason, we believe it is outside the scope of this revision to test the effects of palbociclib in vivo.
2. We plan to re-do this experiment with palbociclib treatment to test organoid growth over time as suggested and, time permitting, perform immunofluorescence for some of the transcription targets such as cyclins, CDKs, Ki67, and p27/p21
3. We have revised the text on page 8 to say “____We observed that the increased growth of Dek over-expressing organoids was dependent on the Dek-induced increase in CDK4/6, since palbociclib treatment resulted in smaller Dek over-expressing organoids that were comparable to organoids from +dox controls.” We also agree that CDK inhibitor treatment may impact multiple downstream signaling pathways. However, the authors do not see this as a negative because cell proliferation, induced by cyclin/CDK complexes, requires metabolic regulation to support physical growth of the cell. The two processes are intricately integrated and have a bidirectional relationship. Thus, it is possible that DEK induces both processes, or it may only promote one process (i.e.: cell cycle) and the other one (i.e.: metabolism) is induced as a secondary result of cell cycle demands. This is one reason why we indicate that metabolic dysregulation should be further studied in the Discussion section. Indeed, a colleague in the DEK field (Susanne Wells) is already working on the relationship between DEK over-expression and metabolic dysfunction, thus this particular aspect of the request is outside the scope of this manuscript.

Major Comment 7: In the main text of Figure 4, the authors conclude that markers for luminal hormone sensing cells were unchanged in Dek-OE mammary glands, however the data to show this is not shown. This is problematic because the authors are directly drawing the conclusion that Dek-OE specifically upregulates luminal alveolar markers using this data.

We have revised the manuscript to include a new supplementary figure (now Fig S4) to include a western blot for HER2 and ERa and a summary of RNA expression data from the bulk RNA-Seq experiment. We will also perform additional western blots to increase the sample size to demonstrate this negative data as part of our planned

Major comment 8: In figure 7, the authors look at a conditional knockout of Dek and conclude that pup death in the knockout was due to insufficient milk production by dams. While the authors establish that H3K27me3 and Ezh2 expression are abrogated, morphological analysis of the ducts is missing and would present convincing data. For instance, in the Dek conditional knockout, are luminal alveolar cells unable to differentiate fully, or are there far fewer? Decreased levels of histone modifications does not tell you much about whether repressive chromatin has changed its landscape in Dek KO mice, which is actually what influences transcription.

__We plan to add histological and whole mount imaging of Dek knockout mammary glands in the revision. We have preliminary data that supports this from 2 mice and will be collecting more samples for the revision. However, as noted in Fig 7C-D, heterozygous females also have small litter sizes and this will pose a breeding challenge for generating knockout females for this experiment in a timely manner. __

Minor Points:

All figures need some sort of reformatting. Several of the conclusions are made based on a limited number of replicates (often n=3) which is not a robust sample size to make a rigorous conclusion. Many figures have text that is stretched. Histology and whole mount images are missing scale bar. IHC quantifications are obscure - what is an optical density? how many animals were analyzed and how many fields of vision were captured? Figure 2F is absolutely impossible to understand. Neither figures nor legends disclose the number of animals or samples analyzed. The statistical test utilized across all figures is not appropriated. Fig5B GSEA plots are missing statistical significance, and without this information one cannot properly access the relevance of the findings. Fig5C - how were co-expressed genes defined? is this just random genes that are expressed in cells that have higher levels of DEK? The term co-expressed suggests a specific type of analysis that would investigate linkage of expression between genes, which i dont think is the case here.

__As the reviewer already mentioned in major comment #1, there was a concern with sample size, which we addressed above in the planned revisions. We believe this concern about sample size was the rationale for the minor comment about “The statistical test utilized across all figures is not appropriate.” We have consulted with a biostatistician, Adam Lane PhD, who has confirmed that our statistical approaches were correct but were limited by our sample size. Thus, we do not agree with the reviewer’s view of statistical analyses. We have revised the text to include sample size information in figure legends and statistical significance information for GSEA plots in Fig 5, With regards to figure text being stretched, it does not look like that in our version of the document and reviewer 2 did not comment on this, so we would like the reviewer to identify a specific instance of this. We plan to capture images with size bars for IHC while we are performing the additional sample size collection. The reviewer asked about the number of fields of view for IHC quantification and we would like to note that our methods section already had that information in the first submission, “at least 3 fields of view from at least 3 different mice per group.” Our methods section also already had information regarding the identification of co-expressed genes in scRNA-Seq data and quantifying IHC with Image J. However, we have revised the text to add some clarifying sentences that we hope helps the reviewer better understand our methods. Finally, we are not sure what is “absolutely impossible to understand” about Fig 2F, which is a network visualization of functional enrichment analyses for differentially expressed genes in our RNA-Seq data. Is the text too small, or does the reviewer not understand the network? We would appreciate it if the reviewer could clarify this concern in their next review. __

Minor Point 1: Throughout, it would be better to indicate the genotype of the "Control" animals on each figure so as the rigor the experiment can be evaluated fully.

It appears that the reviewer was not aware that all controls were the same genotype and were the bitransgenic mice on dox chow. We have revised the manuscript to better clarify that “controls” = “+dox chow” bitransgenics and have added text on page 5 to directly state this. We have also revised Fig 1C to specify that the mouse with no luciferase signal is the “+dox” control.

Minor Point 2: Standard nomenclature for gene names and protein names should be corrected throughout the text.

__We have revised the text to confirm gene and protein names are correct. We have followed convention in using italics for gene names, non-italics for protein names, all capital letters for human genes/proteins (i.e.: DEK) and only first letter capitalization for non-human gene names (i.e.: Dek). __

Minor Point 3: Similar to the point above, the use of Dek-OE to either refer to the mouse model or function as an acronym for "Dek overexpression" is inconsistent throughout the text.

We thank the reviewer for pointing out this inconsistency and we have revised the text so that the “-OE” notation is only used when discussing the mice and have changed to writing out “over-expression” for function.

Minor Point 4: In the main text for Figure 4I-J, the authors state that DEK was previously published as an Erα target gene, however there is no citation to support this.

We have revised the text to include this citation, which is:

16. Privette Vinnedge, L.M., et al., The DEK Oncogene Is a Target of Steroid Hormone Receptor Signaling in Breast Cancer. PLoS One, 2012. 7(10): p. e46985.

Minor Point 5: It is unclear what the conclusion drawn from the experiments shown in Figure 4G-H and Figure 4I-J mean with respect to the goal of Figure 4, which was to show that Dek-OE mice have an expanded luminal alveolar compartment.

We have revised the text to better explain that we were investigating the impact of ovarian hormones and pregnancy on endogenous Dek expression in wild-type mice, since this information has not been previously reported and adds context to our study.

Minor Point 6: Optical density was used to quantify IHC experiments, which was performed using color deconvolution in ImageJ. Something that is unclear is whether the authors are measuring density in the entire field of view, or if the authors are measuring optical density per cell. This has implications whether there are more cell expressing the protein of interest, or if the existing cells are expressing a higher level of the protein of interest.

We have revised the text to include more information in the methods. The Methods now states: “____Image J color deconvolution was utilized to measure the staining intensity only within mammary epithelial cells from at least 3 fields of view from at least 3 different mice per group. Specifically, cross-sections of similarly sized ducts were outlined such that only the collective epithelial cells within that cross section were measured, removing background signal from the stromal cells. Only single cross-sections of ducts were analyzed to minimize the impact of epithelial hyperplasia in experimental mice compared to controls fed dox chow.”

Minor Point 7: In the main text for Figure 6D, the system being used to overexpress DEK protein is not described. It is not the same genetic system as is used in the Dek-OE mice, as doxycycline is inducing Dek expression.

We have revised the figure 6 legend to specify “____DEK over-expression was accomplished with a dox-inducible pTRIPZ vector while DEK knockdown was accomplished with a pLKO.1 shRNA vector” and we kindly point the reviewer to the Methods section (“human cell lines” subsection) as written in the first submission which included detailed information for the subcloning of DEK cDNA into the pTRIPZ vector.

Reviewer 2

_All comments_

1. Comment 1: This study would be improved by sharing important data including virgin mammary gland development in the DEK-OE and DEK-KO models (ductal growth and branching) and the expression of markers including ESR1, PGR, and ERBB2 (data not shown, page 8). Although there may be no differences, this is important data to share regarding the goal of this study. For example, in the DEK-OE model, data are only evaluated in the aged/multiparous stage and in the DEK-KO model, data are only evaluated during lactation. Furthermore, the DEK-KO model resembles germline DEK loss (under control of the CMV promoter), and there is limited validation of a MEC-intrinsic function.

We have revised the manuscript to include data on Esr1/ERa and Erbb2/Her2 by western blot in new Fig S4 as well as the bulk RNA-Seq mRNA levels (by FPKM) for select basal and hormone sensing cell populations. The concern regarding parity was also mentioned by Reviewer 1 (major comments 3&4 above). Briefly we have clarified that ____nearly all data in the manuscript is from nulliparous (virgin) females and have revised the text throughout to more clearly state this fact. We have also revised the text to address the limitation of the CMV promoter. The Discussion section now states “____However, it is noted that one weakness of this CMV-Cre knockout model, is that there is a constitutive loss of Dek, which limits the interpretation for mammary epithelial cell-specific Dek functions.”

Comment 2: Another major concern with this manuscript is the use of immunohistochemistry (IHC) and bulk mammary gland lysate western blots. IHC is non-quantitative, and the images are low resolution. For example, using IHC DEK expression is observed in all MECs (control and DEK-OE mice, Figure 1F), however, in the scRNAseq data DEK expression is confined to basal cells and a subset of stem/progenitor cells (Figure 5A). Furthermore, the hyperplasia in the DEK-OE model will bias bulk analysis (such as western blot and RNAseq) towards increased expression of MEC markers.

1. __We have revised the text to point out that IHC images for Dek in control tissues show some cells have higher expression than others, which is what would be predicted by scRNA-Seq. The text now states on page 16 “____The scRNA-Seq data suggests that Dek is more highly expressed in specific subpopulations of cells, and the variable intensity of immunohistochemical staining for Dek in epithelial cells within control mouse tissue supports this (see Fig 3I, 4I, 4K, and 7H).” Furthermore, on page 10 in the Result section we have revised the text to state “The mammary gland undergoes substantial hormone-induced remodeling across the murine lifespan. We show that Dek is highest during pregnancy and minimally expressed during lactation and involution (Fig 4K), and that Dek protein expression is not uniform across all epithelial cells in wild-type glands (Fig 3I, 4I-K). This suggests that certain epithelial subpopulations express more Dek than others.” __
2. __We acknowledge that IHC and western blots are only semi-quantitative, which is why we attempt to perform both as orthogonal approaches or find additional ways to support our findings throughout the manuscript (i.e.: co-expression at the RNA level from other sources, small molecule inhibitor treatment, etc). We also note that these methods are used to validate the quantitative method of RNA-Seq, and (often) validation of differentially expressed genes can be limited by antibody availability and the applications those antibodies are suitable for. __
3. We also have revised the text to acknowledge that we knew the bulk RNA-Seq would be biased towards the hyperplastic cells. We wanted to take advantage of that bias to identify a gene signature that could be used to determine which cell type was leading to the hyperplasia phenotype. We used the differentially expressed genes to identify biomarkers for specific cell populations. On pages 6-7 the text now reads “____We performed bulk RNA sequencing on whole mammary tissue from two +dox control and two Dek-OE adult virgin females at 15 months of age to discover molecular targets regulated by Dek over-expression and to reveal a gene signature that could help identify the expanded cell population(s) in hyperplastic glands.” And “DEGs were plotted as a heatmap and ontologies for biomarkers of cell populations were defined to help identify the expanded cell population driving Dek-induced hyperplasia.”

Comment 3: A third major concern is the mechanistic link between DEK and H3K27me3. Most of the data are correlative and rely on bulk analysis or IHC. For example, in the DEK-OE organoid model, is there an increase in H3K27me3. Additionally, in the DEK-OE organoids, can loss of EZH2 block the increased cell proliferation?

__We plan to revise the manuscript to include an experiment in which we treat primary mammary epithelial cell organoids from Dek-OE mice with EZH2 inhibitor, GSK-126, +/- doxycycline for a mechanistic or functional link between DEK and H3K27me3 levels. We will then determine organoid size and attempt molecular characterization with IF. This will support the biochemical studies in Fig 6 showing DEK interacts with the PRC2 complex. __

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

In this manuscript, the authors recorded cerebellar unipolar brush cells (UBCs) in acute brain slices. They confirmed that mossy fiber (MF) inputs generate a continuum of UBC responses. Using systematic and physiological trains of MF electrical stimulation, they demonstrated that MF inputs either increased or decreased UBC firing rates (UBC ON vs. OFF) or induced complex, long-lasting modulation of their discharges. The MF influence on UBC firing was directly associated with a specific combination of metabotropic glutamate receptors, mGluR2/3 (inhibitory) and mGluR1 (excitatory). Ultimately, the amount and ratio of these two receptors controlled the time course of the effect, yielding specific temporal transformations such as phase shifts.

Overall, the topic is compelling, as it broadens our understanding of temporal processing in the cerebellar cortex. The experiments are well-executed and properly analyzed.

Strengths:

(1) A wide range of MF stimulation patterns was explored, including burst duration and frequency dependency, which could serve as a valuable foundation for explicit modeling of temporal transformations in the granule cell layer.

(2) The pharmacological blockade of mGluR2/3, mGluR1, AMPA, and NMDA receptors helped identify the specific roles of these glutamate receptors.

(3) The experiments convincingly demonstrate the key role of mGluR1 receptors in temporal information processing by UBCs.

Weaknesses:

(1) This study is largely descriptive and represents only a modest incremental advance from the previous work (Guo et al., Nat. Commun., 2021). 

We feel that the present study is a major advance.  It builds on (Guo et al., Nat. Commun., 2021) in which we examined the effects of bursts of 20 stimuli at 100 spk/s.  In that study we found that differential expression of mGluR1 and mGluR2 let to a continuum of temporal responses in UBCs, but AMPARs make a minimal contribution for such bursts. It was not known how UBCs transform realistic mossy fiber input patterns. Here we provide a comprehensive evaluation of a wide range of input patterns that include a range of bursts comprised of 1-20 stimuli, sustained stimulation with stimulation of 1 spk/s to 60 spk/s. This more thorough assessment of UBC transformations combined with a pharmacological assessment of the contributions of different glutamate receptor subtypes provided many new insights: 

• We found that UBC transformations are comprised of two different components: a slow temporally filtered component controlled by an interplay of mGluR1 and mGluR2, and a second component mediated by AMPARs that can convey spike timing information. NMDARs do not make a major contribution to UBC firing. The finding that UBCs simultaneously convey two types of signals, a slow filtered response and responses to single stimuli, has important implications for the computational potential of UBCs and fundamentally changes the way we think about UBCs.  

• We found that with regard to the slow filtered component mediated by mGluR1 and mGluR2, we could extend the concept of a continuum of responses evoked by 20 stimuli at 100 spk/s (Guo et al., Nat. Commun., 2021) to a wide range of stimuli. It was not a given that this would be the case.   

• The contributions of AMPARs was surprising. Even though snRNAseq data did not reveal a gradient of AMPAR expression across the population of UBCs (Guo et al., Nat. Commun., 2021), we found that there was a gradient of AMPA-mediated responses, and that the AMPA component was also most prominent in cells with a large mGluR1 component. Our finding that AMPAR accessory proteins exhibit a gradient across the population, which could account for the gradient of AMPAR responses, will prompt additional studies to test their involvement. 

(2) The MF activity used to mimic natural stimulation was previously collected in primates, while the recordings were conducted in mice.

Our first task was to determine the firing properties of mossy fibers under physiological conditions in UBC rich cerebellar regions. Previous studies have estimated this in anesthetized mice using whole cell granule cell recordings (Arenz et al., 2008; Witter & De Zeeuw 2015). However, for assessing firing patterns during awake behavior, we felt that the most comprehensive data set available in a UBC rich cerebellar region was for mossy fibers involved in smooth pursuit in monkeys (David J. Herzfeld and Stephen G. Lisberger). This revealed the general features of mossy fiber firing that helped us design stimulus patterns to thoroughly probe the properties of MF to UBC transformations. The firing patterns are designed to investigate the transformations for a wide range of activity patterns and have important general implications for UBC transformations that are likely applicable to UBCs in different species that are activated in different ways.   

(3) Inhibition was blocked throughout the study, reducing its physiological relevance.

The reviewer correctly brings up the very important issue of inhibition in shaping UBC responses.  It is well established that UBCs are inhibited by Golgi cells (Rousseau et al., 2012), and we recently showed that some UBCs are also inhibited by PCs (Guo et al., eLife, 2021). This will undoubtedly influence the firing of UBCs in vivo. We considered examining this issue, but felt that brain slice experiments are not well suited to this. In contrast to MF inputs that can be activated with a realistic activity pattern, it is exceedingly difficult to know how Golgi cells and Purkinje cells are activated under physiological conditions. Each UBC is activated by a single mossy fiber, but inhibition is provided by Golgi cells that are activated by many mossy fibers and granule cells, and PCs that are controlled by many granule cells and many other PCs. In addition, we found that many Golgi cells do not survive very well in slices, and the axons of many PCs are severed in brain slice. Although limitations of the slice preparation prevent us from determining the role of inhibition in shaping UBC responses, we have added a section to the discussion in which we address the important issue of inhibition and UBC responses.   

Reviewer #2 (Public review):

This study addresses the question of how UBCs transform synaptic input patterns into spiking output patterns and how different glutamate receptors contribute to their transformations. The first figure utilizes recorded patterns of mossy fiber firing during eye movements in the flocculus of rhesus monkeys obtained from another laboratory. In the first figure, these patterns are used to stimulate mossy fibers in the mouse cerebellum during extracellular recordings of UBCs in acute mouse brain slices. The remaining experiments stimulate mossy fiber inputs at different rates or burst durations, which is described as 'mossy-fiber like', although they are quite simpler than those recorded in vivo. As expected from previous work, AMPA mediates the fast responses, and mGluR1 and mGluR2/3 mediate the majority of longer-duration and delayed responses. The manuscript is well organized and the discussion contextualizes the results effectively.

The authors use extracellular recordings because the washout of intracellular molecules necessary for metabotropic signaling may occur during whole-cell recordings. These cell-attached recordings do not allow one to confirm that electrical stimulation produces a postsynaptic current on every stimulus. Moreover, it is not clear that the synaptic input is monosynaptic, as UBCs synapse on one another. This leaves open the possibility that delays in firing could be due to disynaptic stimulation. Additionally, the result that AMPAmediated responses were surprisingly small in many UBCs, despite apparent mRNA expression, suggests the possibility that spillover from other nearby synapses activated the higher affinity extrasynaptic mGluRs and that that main mossy fiber input to the UBC was not being stimulated. For these reasons, some whole-cell recordings (or perforated patch) would show that when stimulation is confirmed to be monosynaptic and reliable it can produce the same range of spiking responses seen extracellularly and that AMPA receptormediated currents are indeed small or absent in some UBCs.

We appreciate the reviewer’s concerns regarding the reliability of mossy fiber activation, the possibility of glutamate spillover from other synapses, and the possibility of disynaptic activation involving stimulation of MFàUBCàUBC connections. We examined these issues in a previous study (Guo et al., Nat. Commun., 2021).  We did on-cell recordings and followed that up with whole cell voltage clamp recordings from the same cell (Guo et al., Nat. Commun., 2021, Fig. 5), and there was good agreement with the amplitude and timing of spiking and the time course and amplitudes of the synaptic currents.  We also compared responses evoked by focal glutamate uncaging over the brush and MF stimulation (Guo et al., Nat. Commun., 2021, Fig. 4). We found that the time courses and amplitudes of the responses were remarkably similar. This strongly suggests that the responses we observe do not reflect disynaptic activation (MFàUBCàUBC connections). We also showed that the responses were all-or-none: at low intensities no response was evoked, as the intensity of extracellular stimulation was increased a large response was suddenly evoked at a threshold intensity and further increases in intensity did not increase the amplitude of the response (Guo et al., Nat. Commun., 2021, Extended data Fig. 1).  We can be well above threshold and still excite the same response, and as a result we do not see stereotyped indications of an inability to stimulate during prolonged high frequency activation.  We recognize the importance of these issues, so we have  added a section dealing explicitly with these issues (pp. 15-16).  

A discussion of whether the tested glutamate receptors affected the spontaneous firing rates of these cells would be informative as standing currents have been reported in UBCs. It is unclear whether the firing rate was normalized for each stimulation, each drug application, or each cell. It would also be informative to report whether UBCs characterized as responding with Fast, Mid-range, Slow, and OFF responses have different spontaneous firing rates or spontaneous firing patterns (regular vs irregular).

The spontaneous firing of UBCs is indeed an interesting issue that is deserving of further investigation. It is not currently known how spontaneous firing at rest is regulated in UBCs, however, in previous work we have shown that there is great diversity in the rates across the population of UBCs in the dorsal cochlear nucleus (Huson & Regehr, JNeurosci, 2023, Fig. 4). Unfortunately, during the kind of sustained high-frequency stimulation protocols (as used in this study) spontaneous firing rates tend to increase. This is likely an effect of residual receptor activation. As such, our current dataset is not suitable to performing in depth analysis of the effects of the different glutamate receptors on spontaneous firing rates. As this study aims to explore UBC responses to MF inputs we feel that specific experiments to address the issue of spontaneous firing rates are outside of the scope.

As the reviewers points out there are indeed different ways the firing rates can be normalized for display in the heatmaps, and different normalizations have been used in different figures. We have made sure that the method for normalization is clearly indicated in the figure legends for each of the heatmaps on display, specifying the protocol and drug application used for normalization.

Figure 1 shows examples of how Fast, Mid-range, Slow, and OFF UBCs respond to in vivo MF firing patterns, but lacks a summary of how the input is transformed across a population of UBCs. In panel d, it looks as if the phase of firing becomes more delayed across the examples from Fast to OFF UBCs. Quantifying this input/output relationship more thoroughly would strengthen these results.

The UBC responses to in vivo MF firing patterns are intriguing and we agree that there appears to be increasing delays for slower UBCs visible in Figure 1. However, we feel that the true in vivo MF firing patterns are too complex and irregular for rigorous interpretation. Therefore, we only tested simplified burst and smooth pursuit-like input patterns on the full population of UBCs. Here we indeed do see increasingly delayed responses as UBCs get slower (Fig. 4).

Inhibition was pharmacologically blocked in these studies. Golgi cells and other inhibitory interneurons likely contribute to how UBCs transform input signals. Speculation of how GABAergic and glycinergic synaptic inhibition may contribute additional context to help readers understand how a circuit with intact inhibition may behave. 

As indicated in our response to reviewer 1, we have added a section discussing the very important issue of inhibition and UBC responses in vivo.   

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Including recordings without inhibition blocked would strengthen the study and provide a more comprehensive view of the transformations made by UBCs at the input stage of the cerebellar cortex.

See response to public comments.   

(2) The authors claim that a continuum of temporal responses was observed in UBCs, but they also distinguish between fast, mid-range, slow, and OFF UBCs. While some UBCs fire spontaneously, others are activated by MF inputs. A more thorough classification effort would clarify the various response profiles observed under specific MF stimulation regimes. Have the authors considered using machine learning algorithms to aid in classification? 

We fundamentally feel that these response properties do not conform to rigid categories. In our previous work we have shown that UBC population constitutes a continuum in terms of gene expression, and in terms of spontaneous and evoked firing patterns. While in order to answer some questions empirically it may still be useful to apply advanced algorithms to enforce separate groups to be compared, in this work we aimed to present the full range of UBC responses without introducing any additional biases that such methods would produce.

(3) A robust classification could assist in quantifying the temporal shifts observed during smooth pursuit-like MF stimulation, a critical outcome of the study.

As stated above, we prefer to present an unbiased overview of the continuous nature of the UBC population, as we believe that this is fundamentally the most accurate representation. While it is true that this prevents us from providing a quantification in the different temporal shifts, we believe that the range of shifts across the population is sufficiently large and continuously varying the be convincing (see Figure 4d).  

(4) In Figure 5, contrary to what is described on page 10, Cells 10 and 11 (OFF UBCs) appear to behave differently, as mGluR1 does not seem to affect their firing rates. A specific case should be made for OFF UBCs. 

Indeed, cells 10 and 11 do not show clear increases in firing and are not strongly affected by blocking of mGluR1. However, as discussed above and explored in our previous work, we feel that the range of UBC increases in firing is best described as a continuum, including the extreme where increases in firing are no longer clearly observable. As the aim in this work is to describe this continuum of responses for physiologically relevant inputs, we do not feel there is a benefit to creating a specific case for OFF UBCs here. It should be pointed out that the number of “pure” OFF UBCs completely lacking an mGluR1 component is very small.  

(5) A summary diagram should be added at the end of the manuscript to highlight the key temporal features observed in this study. 

This is a great suggestion and we have prepared such a summary diagram (Figure 6).

Reviewer #2 (Recommendations for the authors):

(1) Page 3- "Assed" should be "assessed"

(2) Page 19- "by integrating" is repeated twice

(3) It was not noted whether the data would be made available. It could be useful for those interested in implementing UBCs in models of the cerebellar cortex.

We agree that this data set is invaluable to those interested in implementing UBCs in models of the cerebellar cortex.  We will make the dataset available as described in the text.

Author response:

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

Reviewer #2 (Public review):

Summary:

Yamawaki et al., conducted a series of neuroanatomical tracing and whole cell recording experiments to elucidate and characterise a relatively unknown pathway between the endopiriform (EN) and CA1 of the ventral hippocampus (vCA1) and to assess its functional role in social and object recognition using fibre photometry and dual vector chemogenetics. The main findings were that the EN sends robust projections to the vCA1 that collateralise to the prefrontal cortex, lateral entorhinal cortex and piriform cortex, and these EN projection neurons terminate in the stratum lacunosum-moleculare (SLM) layer of distal vCA1, synapsing onto GABAergic neurons that span across the Pyramidal-Stratum Radiatum (SR) and SR-SML borders. It was also demonstrated that EN input disynaptically inhibits vCA1 pyramidal neurons. vCA1 projecting EN neurons receive afferent input from piriform cortex, and from within EN. Finally, fibre photometry experiments revealed that vCA1 projecting EN neurons are most active when mice explore novel objects or conspecifics, and pathway-specific chemogenetic inhibition led to an impairment in the ability to discriminate between novel vs. familiar objects and conspecifics.

The authors have addressed most of my concerns, but a few weaknesses remain :<br /> (1) I expected to see the addition of raw interaction times with objects and conspecifics for each phase of social testing (pre-test, sociability test, social discrimination), as per my comment on including raw data. However, the authors only provided total distance traveled and velocity, and total interaction time in Figure S9, which is less informative.

We apologies for missing the request. We have added the raw interaction times in Fig. S9G.

(2) The authors observed increased activity in vCA1-projecting EN neurons tracking with the preferred object during the pre-test (object-object exploration) phase of the social tests, and the summary schematic (Figure 9A) depicts animals as showing a preference for one object over the other (although they are identical) in both the social and object recognition tests. However, in the chemogenetic experiment, the data (Fig S9B) indicate that animals did not show this preference for one object over another, making the expected baseline for this task unclear. This also raises an important question of whether the lack of effect from chemogenetic inhibition of vCA1-projecting EN neurons could be attributed to the absence of this baseline preference.

We appreciate the comments. In Fig. S9B, although the group median at baseline (pretest) showed no preference for one object, individual subjects displayed a preference for one object (i.e., each data point deviated positively or negatively from 0.5) in saline condition. Therefore, we do not think that a lack of baseline preference accounts for the absence of the inhibition effect in the pretest.

Additionally, the finding that vCA1-projecting EN activity is associated with the preferred object exploration appears to counter the authors' argument that novelty engages this circuit (since both objects are novel in this instance). This discrepancy warrants further discussion.

This is an interesting point. One possibility is that during the pretest, EN activity simply "reports" or "represents" the interaction time without driving exploratory preference. This aligns with our DREADD experiment data, which show that inhibition of EN neurons produced no overall behavioral effect. Innate exploratory behavior has been attributed to various circuits, including the medial preoptic area → PAG circuit (Ryoo et al., 2021, Front. Neuro.) and the Septal → VTA circuit (Mocellin et al., 2024, Neuron). We found no direct projection from these areas to EN (Fig. 6), but such connections could be established di- or polysynaptically. Moreover, these circuits could be driven by common inputs, such as the locus coeruleus or the cholinergic system for arousal, with only specific downstream targets, excluding EN, playing a key role in driving innate exploration and preference.

We have inserted the following sentence in discussion (line 253-255):

“The correlation of ENvCA1-proj. activity with novel object preference in the pretest nevertheless suggests that these neurons 'represent' the innate preference without driving it.”

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

Line 209: Please remove the reference to neural activity 'predicting' behavior, as correlation analysis does not imply predictive power.

We now have changed the phrase to “Although EN^vCA1-proj. activity was correlated with the behavior…”

Line 236: It is unclear what is meant by: 'This circuit motif may predict the predominant role of ENvCA1-proj. neurons in social recognition memory'

We have changed the sentence to the following for the clarity:

“Since social odor information is crucial for discriminating conspecifics in rodents, this circuit motif may predict the predominant role of ENvCA1-proj. neurons in social recognition memory, given that social odor can engage multiple olfactory pathways innervating the piriform cortex.”

Fig 7 title: insert 'with' after correlates: 'Activity of ENvCA1-proj. neurons correlates social/object discrimination performance'

Corrected.

Fig S1 title: 'Projecing' typo.

Corrected.

Fig S8: Please rephrase for clarity: 'In pretest, the object was aligned by longer interaction time (preferred object is plotted in right side)'

We now have rephrased the sentence to:

“In the pretest plot, the object that the mice interacted with more is placed on the right side.”

References:

A septal-ventral tegmental area circuit drives exploratory behavior. Mocellin, Petra et al. Neuron, Volume 112, Issue 6, 1020-1032.e7

An inhibitory medial preoptic circuit mediates innate exploration. Ryoo, Jia et al. Front. Neurosci., 23 August 221. Volume 15- 2021

Author response:

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

eLife Assessment

This study presents valuable findings on the potential of short-movie viewing fMRI protocol to explore the functional and topographical organization of the visual system in awake infants and toddlers. Although the data are compelling given the difficulty of studying this population, the evidence presented is incomplete and would be strengthened by additional analyses to support the authors' claims. This study will be of interest to cognitive neuroscientists and developmental psychologists, especially those interested in using fMRI to investigate brain organisation in pediatric and clinical populations with limited fMRI tolerance.

We are grateful for the thorough and thoughtful reviews. We have provided point-bypoint responses to the reviewers’ comments, but first, we summarize the major revisions here. We believe these revisions have substantially improved the clarity of the writing and impact of the results.

Regarding the framing of the paper, we have made the following major changes in response to the reviews:

(1) We have clarified that our goal in this paper was to show that movie data contains topographic, fine-grained details of the infant visual cortex. In the revision, we now state clearly that our results should not be taken as evidence that movies could replace retinotopy and have reworded parts of the manuscript that could mislead the reader in this regard.

(2) We have added extensive details to the (admittedly) complex methods to make them more approachable. An example of this change is that we have reorganized the figure explaining the Shared Response Modelling methods to divide the analytic steps more clearly.

(3) We have clarified the intermediate products contributing to the results by adding 6 supplementary figures that show the gradients for each IC or SRM movie and each infant participant.

In response to the reviews, we have conducted several major analyses to support our findings further:

(1) To verify that our analyses can identify fine-grained organization, we have manually traced and labeled adult data, and then performed the same analyses on them. The results from this additional dataset validate that these analyses can recover fine-grained organization of the visual cortex from movie data.

(2) To further explore how visual maps derived from movies compare to alternative methods, we performed an anatomical alignment control analysis. We show that high-quality maps can be predicted from other participants using anatomical alignment.

(3) To test the contribution of motion to the homotopy analyses, we regressed out the motion effects in these analyses. We found qualitatively similar results to our main analyses, suggesting motion did not play a substantial role.

(4) To test the contribution of data quantity to the homotopy analyses, we correlated the amount of movie data collected from each participant with the homotopy results. We did not find a relationship between data quantity and the homotopy results. 

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Ellis et al. investigated the functional and topographical organization of the visual cortex in infants and toddlers, as evidenced by movie-viewing data. They build directly on prior research that revealed topographic maps in infants who completed a retinotopy task, claiming that even a limited amount of rich, naturalistic movie-viewing data is sufficient to reveal this organization, within and across participants. Generating this evidence required methodological innovations to acquire high-quality fMRI data from awake infants (which have been described by this group, and elsewhere) and analytical creativity. The authors provide evidence for structured functional responses in infant visual cortex at multiple levels of analyses; homotopic brain regions (defined based on a retinotopy task) responded more similarly to one another than to other brain regions in visual cortex during movie-viewing; ICA applied to movie-viewing data revealed components that were identifiable as spatial frequency, and to a lesser degree, meridian maps, and shared response modeling analyses suggested that visual cortex responses were similar across infants/toddlers, as well as across infants/toddlers and adults. These results are suggestive of fairly mature functional response profiles in the visual cortex in infants/toddlers and highlight the potential of movie-viewing data for studying finer-grained aspects of functional brain responses, but further evidence is necessary to support their claims and the study motivation needs refining, in light of prior research.

Strengths:

- This study links the authors' prior evidence for retinotopic organization of visual cortex in human infants (Ellis et al., 2021) and research by others using movie-viewing fMRI experiments with adults to reveal retinotopic organization (Knapen, 2021).

- Awake infant fMRI data are rare, time-consuming, and expensive to collect; they are therefore of high value to the community. The raw and preprocessed fMRI and anatomical data analyzed will be made publicly available.

We are grateful to the reviewer for their clear and thoughtful description of the strengths of the paper, as well as their helpful outlining of areas we could improve.

Weaknesses:

- The Methods are at times difficult to understand and in some cases seem inappropriate for the conclusions drawn. For example, I believe that the movie-defined ICA components were validated using independent data from the retinotopy task, but this was a point of confusion among reviewers. 

We acknowledge the complexity of the methods and wish to clarify them as best as possible for the reviewers and the readers. We have extensively revised the methods and results sections to help avoid potential misunderstandings. For instance, we have revamped the figure and caption describing the SRM pipeline (Figure 5).

To answer the stated confusion directly, the ICA components were derived from the movie data and validated on the (completely independent) retinotopy data. There were no additional tasks. The following text in the paper explains this point:

“To assess the selected component maps, we correlated the gradients (described above) of the task-evoked and component maps. This test uses independent data: the components were defined based on movie data and validated against task-evoked retinotopic maps.” Pg. 11

In either case: more analyses should be done to support the conclusion that the components identified from the movie reproduce retinotopic maps (for example, by comparing the performance of movie-viewing maps to available alternatives (anatomical ROIs, group-defined ROIs). 

Before addressing this suggestion, we want to restate our conclusions: features of the retinotopic organization of infant visual cortex could be predicted from movie data. We did not conclude that movie data could ‘reproduce’ retinotopic maps in the sense that they would be a replacement. We recognize that this was not clear in our original manuscript and have clarified this point throughout, including in this section of the discussion:

“To be clear, we are not suggesting that movies work well enough to replace a retinotopy task when accurate maps are needed. For instance, even though ICA found components that were highly correlated with the spatial frequency map, we also selected some components that turned out to have lower correlations. Without knowing the ground truth from a retinotopy task, there would be no way to weed these out. Additionally, anatomical alignment (i.e., averaging the maps from other participants and anatomically aligning them to a held-out participant) resulted in maps that were highly similar to the ground truth. Indeed, we previously[23] found that adult-defined visual areas were moderately similar to infants. While functional alignment with adults can outperform anatomical alignment methods in similar analyses[27], here we find that functional alignment is inferior to anatomical alignment. Thus, if the goal is to define visual areas in an infant that lacks task-based retinotopy, anatomical alignment of other participants’ retinotopic maps is superior to using movie-based analyses, at least as we tested it.” Pg. 21

As per the reviewer’s suggestion and alluded to in the paragraph above, we have created anatomically aligned visual maps, providing an analogous test to the betweenparticipant analyses like SRM. We find that these maps are highly similar to the ground truth. We describe this result in a new section of the results:

“We performed an anatomical alignment analog of the functional alignment (SRM) approach. This analysis serves as a benchmark for predicting visual maps using taskbased data, rather than movie data, from other participants. For each infant participant, we aggregated all other infant or adult participants as a reference. The retinotopic maps from these reference participants were anatomically aligned to the standard surface template, and then averaged. These averages served as predictions of the maps in the test participant, akin to SRM, and were analyzed equivalently (i.e., correlating the gradients in the predicted map with the gradients in the task-based map). These correlations (Table S4) are significantly higher than for functional alignment (using infants to predict spatial frequency, anatomical alignment > functional alignment: ∆_{Fisher Z} M=0.44, CI=[0.32–0.58], p<.001; using infants to predict meridians, anatomical alignment > functional alignment: ∆_{Fisher Z} M=0.61, CI=[0.47–0.74], p<.001; using adults to predict spatial frequency, anatomical alignment > functional alignment: ∆_{Fisher Z} M=0.31, CI=[0.21–0.42], p<.001; using adults to predict meridians, anatomical alignment > functional alignment: ∆_{Fisher Z} M=0.49, CI=[0.39–0.60], p<.001). This suggests that even if SRM shows that movies can be used to produce retinotopic maps that are significantly similar to a participant, these maps are not as good as those that can be produced by anatomical alignment of the maps from other participants without any movie data.” Pg. 16–17

Also, the ROIs used for the homotopy analyses were defined based on the retinotopic task rather than based on movie-viewing data alone - leaving it unclear whether movie-viewing data alone can be used to recover functionally distinct regions within the visual cortex.

We agree with the reviewer that our approach does not test whether movie-viewing data alone can be used to recover functionally distinct regions. The goal of the homotopy analyses was to identify whether there was functional differentiation of visual areas in the infant brain while they watch movies. This was a novel question that provides positive evidence that these regions are functionally distinct. In subsequent analyses, we show that when these areas are defined anatomically, rather than functionally, they also show differentiated function (e.g., Figure 2). Nonetheless, our intention was not to use the homotopy analyses to define the regions. We have added text to clarify the goal and novelty of this analysis.

“Although these analyses cannot define visual maps, they test whether visual areas have different functional signatures.” Pg. 6

Additionally, even if the goal were to define areas based on homotopy, we believe the power of that analysis would be questionable. We would need to use a large amount of the movie data to define the areas, leaving a low-powered dataset to test whether their function is differentiated by these movie-based areas.

- The authors previously reported on retinotopic organization of the visual cortex in human infants (Ellis et al., 2021) and suggest that the feasibility of using movie-viewing experiments to recover these topographic maps is still in question. They point out that movies may not fully sample the stimulus parameters necessary for revealing topographic maps/areas in the visual cortex, or the time-resolution constraints of fMRI might limit the use of movie stimuli, or the rich, uncontrolled nature of movies might make them inferior to stimuli that are designed for retinotopic mapping, or might lead to variable attention between participants that makes measuring the structure of visual responses across individuals challenging. This motivation doesn't sufficiently highlight the importance or value of testing this question in infants. Further, it's unclear if/how this motivation takes into account prior research using movie-viewing fMRI experiments to reveal retinotopic organization in adults (e.g., Knapen, 2021). Given the evidence for retinotopic organization in infants and evidence for the use of movie-viewing experiments in adults, an alternative framing of the novel contribution of this study is that it tests whether retinotopic organization is measurable using a limited amount of movie-viewing data (i.e., a methodological stress test). The study motivation and discussion could be strengthened by more attention to relevant work with adults and/or more explanation of the importance of testing this question in infants (is the reason to test this question in infants purely methodological - i.e., as a way to negate the need for retinotopic tasks in subsequent research, given the time constraints of scanning human infants?).

We are grateful to the reviewer for giving us the opportunity to clarify the innovations of this research. We believe that this research contributes to our understanding of how infants process dynamic stimuli, demonstrates the viability and utility of movie experiments in infants, and highlights the potential for new movie-based analyses (e.g., SRM). We have now consolidated these motivations in the introduction to more clearly motivate this work:

“The primary goal of the current study is to investigate whether movie-watching data recapitulates the organization of visual cortex. Movies drive strong and naturalistic responses in sensory regions while minimizing task demands[12, 13, 24] and thus are a proxy for typical experience. In adults, movies and resting-state data have been used to characterize the visual cortex in a data-driven fashion[25–27]. Movies have been useful in awake infant fMRI for studying event segmentation[28], functional alignment[29], and brain networks[30]. However, this past work did not address the granularity and specificity of cortical organization that movies evoke. For example, movies evoke similar activity in infants in anatomically aligned visual areas[28], but it remains unclear whether responses to movie content differ between visual areas (e.g., is there more similarity of function within visual areas than between31). Moreover, it is unknown whether structure within visual areas, namely visual maps, contributes substantially to visual evoked activity. Additionally, we wish to test whether methods for functional alignment can be used with infants. Functional alignment finds a mapping between participants using functional activity – rather than anatomy – and in adults can improve signal-to-noise, enhance across participant prediction, and enable unique analyses[27, 32–34].” Pg. 3-4

Furthermore, the introduction culminates in the following statement on what the analyses will tell us about the nature of movie-driven activity in infants:

“These three analyses assess key indicators of the mature visual system: functional specialization between areas, organization within areas, and consistency between individuals.” Pg. 5

Furthermore, in the discussion we revisit these motivations and elaborate on them further:

[Regarding homotopy:] “This suggests that visual areas are functionally differentiated in infancy and that this function is shared across hemispheres[31].” Pg. 19

[Regarding ICA:] “This means that the retinotopic organization of the infant brain accounts for a detectable amount of variance in visual activity, otherwise components resembling these maps would not be discoverable.” Pg. 19–20

[Regarding SRM:] “This is initial evidence that functional alignment may be useful for enhancing signal quality, like it has in adults[27,32,33], or revealing changing function over development[45].” Pg. 21

Additionally, we have expanded our discussion of relevant work that uses similar methods such as the excellent research from Knapen (2021) and others:

“In adults, movies and resting-state data have been used to characterize the visual cortex in a data-driven fashion[25-27].” Pg. 4

“We next explored whether movies can reveal fine-grained organization within visual areas by using independent components analysis (ICA) to propose visual maps in individual infant brains[25,26,35,42,43].” Pg. 9

Reviewer #2 (Public Review):

Summary:

This manuscript shows evidence from a dataset with awake movie-watching in infants, that the infant brain contains areas with distinct functions, consistent with previous studies using resting state and awake task-based infant fMRI. However, substantial new analyses would be required to support the novel claim that movie-watching data in infants can be used to identify retinotopic areas or to capture within-area functional organization.

Strengths:

The authors have collected a unique dataset: the same individual infants both watched naturalistic animations and a specific retinotopy task. These data position the authors to test their novel claim, that movie-watching data in infants can be used to identify retinotopic areas.

Weaknesses:

To claim that movie-watching data can identify retinotopic regions, the authors should provide evidence for two claims:

- Retinotopic areas defined based only on movie-watching data, predict retinotopic responses in independent retinotopy-task-driven data.

- Defining retinotopic areas based on the infant's own movie-watching response is more accurate than alternative approaches that don't require any movie-watching data, like anatomical parcellations or shared response activation from independent groups of participants.

We thank the reviewer for their comments. Before addressing their suggestions, we wish to clarify that we do not claim that movie data can be used to identify retinotopic areas, but instead that movie data captures components of the within and between visual area organization as defined by retinotopic mapping. We recognize that this was not clear in our original manuscript and have clarified this point throughout, including in this section of the discussion:

“To be clear, we are not suggesting that movies work well enough to replace a retinotopy task when accurate maps are needed. For instance, even though ICA found components that were highly correlated with the spatial frequency map, we also selected some components that turned out to have lower correlations. Without knowing the ground truth from a retinotopy task, there would be no way to weed these out. Additionally, anatomical alignment (i.e., averaging the maps from other participants and anatomically aligning them to a held-out participant) resulted in maps that were highly similar to the ground truth. Indeed, we previously[23] found that adult-defined visual areas were moderately similar to infants. While functional alignment with adults can outperform anatomical alignment methods in similar analyses[27], here we find that functional alignment with infants is inferior to anatomical alignment. Thus, if the goal is to define visual areas in an infant that lacks task-based retinotopy, anatomical alignment of other participants’ retinotopic maps is superior to using movie-based analyses, at least as we tested it.” Pg. 21

In response to the reviewer’s suggestion, we compare the maps identified by SRM to the averaged, anatomically aligned maps from infants. We find that these maps are highly similar to the task-based ground truth and we describe this result in a new section:

“We performed an anatomical alignment analog of the functional alignment (SRM) approach. This analysis serves as a benchmark for predicting visual maps using taskbased data, rather than movie data, from other participants. For each infant participant, we aggregated all other infant or adult participants as a reference. The retinotopic maps from these reference participants were anatomically aligned to the standard surface template, and then averaged. These averages served as predictions of the maps in the test participant, akin to SRM, and were analyzed equivalently (i.e., correlating the gradients in the predicted map with the gradients in the task-based map). These correlations (Table S4) are significantly higher than for functional alignment (using infants to predict spatial frequency, anatomical alignment < functional alignment: ∆_{Fisher Z} M=0.44, CI=[0.32–0.58], p<.001; using infants to predict meridians, anatomical alignment < functional alignment: ∆_{Fisher Z} M=0.61, CI=[0.47–0.74], p<.001; using adults to predict spatial frequency, anatomical alignment < functional alignment: ∆_{Fisher Z} M=0.31, CI=[0.21–0.42], p<.001; using adults to predict meridians, anatomical alignment < functional alignment: ∆_{Fisher Z} M=0.49, CI=[0.39–0.60], p<.001). This suggests that even if SRM shows that movies can be used to produce retinotopic maps that are significantly similar to a participant, these maps are not as good as those that can be produced by anatomical alignment of the maps from other participants without any movie data.” Pg. 16–17

Note that we do not compare the anatomically aligned maps with the ICA maps statistically. This is because these analyses are not comparable: ICA is run withinparticipant whereas anatomical alignment is necessarily between-participant — either infant or adults. Nonetheless, an interested reader can refer to the Table where we report the results of anatomical alignment and see that anatomical alignment outperforms ICA in terms of the correlation between the predicted and task-based maps.

Both of these analyses are possible, using the (valuable!) data that these authors have collected, but these are not the analyses that the authors have done so far. Instead, the authors report the inverse of (1): regions identified by the retinotopy task can be used to predict responses in the movies. The authors report one part of (2), shared responses from other participants can be used to predict individual infants' responses in the movies, but they do not test whether movie data from the same individual infant can be used to make better predictions of the retinotopy task data, than the shared response maps.

So to be clear, to support the claims of this paper, I recommend that the authors use the retinotopic task responses in each individual infant as the independent "Test" data, and compare the accuracy in predicting those responses, based on:

-  The same infant's movie-watching data, analysed with MELODIC, when blind experimenters select components for the SF and meridian boundaries with no access to the ground-truth retinotopy data.

-  Anatomical parcellations in the same infant.

-  Shared response maps from groups of other infants or adults.

-  (If possible, ICA of resting state data, in the same infant, or from independent groups of infants).

Or, possibly, combinations of these techniques.

If the infant's own movie-watching data leads to improved predictions of the infant's retinotopic task-driven response, relative to these existing alternatives that don't require movie-watching data from the same infant, then the authors' main claim will be supported.

These are excellent suggestions for additional analyses to test the suitability for moviebased maps to replace task-based maps. We hope it is now clear that it was never our intention to claim that movie-based data could replace task-based methods. We want to emphasize that the discoveries made in this paper — that movies evoke fine-grained organization in infant visual cortex — do not rely on movie-based maps being better than alternative methods for producing maps, such as the newly added anatomical alignment.

The proposed analysis above solves a critical problem with the analyses presented in the current manuscript: the data used to generate maps is identical to the data used to validate those maps. For the task-evoked maps, the same data are used to draw the lines along gradients and then test for gradient organization. For the component maps, the maps are manually selected to show the clearest gradients among many noisy options, and then the same data are tested for gradient organization. This is a double-dipping error. To fix this problem, the data must be split into independent train and test subsets.

We appreciate the reviewer’s concern; however, we believe it is a result of a miscommunication in our analytic strategy. We have now provided more details on the analyses to clarify how double-dipping was avoided. 

To summarize, a retinotopy task produced visual maps that were used to trace both area boundaries and gradients across the areas. These data were then fixed and unchanged, and we make no claims about the nature of these maps in this paper, other than to treat them as the ground truth to be used as a benchmark in our analyses. The movie data, which are collected independently from the same infant in the session, used the boundaries from the retinotopy task (in the case of homotopy) or were compared with the maps from the retinotopy task (in the case of ICA and SRM). In other words, the statement that “the data used to generate maps is identical to the data used to validate those maps” is incorrect because we generated the maps with a retinotopy task and validated the maps with the movie data. This means no double dipping occurred.

Perhaps a cause of the reviewer’s interpretation is that the gradients used in the analysis are not clearly described. We now provide this additional description:  “Using the same manually traced lines from the retinotopy task, we measured the intensity gradients in each component from the movie-watching data. We can then use the gradients of intensity in the retinotopy task-defined maps as a benchmark for comparison with the ICA-derived maps.” Pg. 10

Regarding the SRM analyses, we take great pains to avoid the possibility of data contamination. To emphasize how independent the SRM analysis is, the prediction of the retinotopic map from the test participant does not use their retinotopy data at all; in fact, the predicted maps could be made before that participant’s retinotopy data were ever collected. To make this prediction for a test participant, we need to learn the inversion of the SRM, but this only uses the movie data of the test participant. Hence, there is no double-dipping in the SRM analyses. We have elaborated on this point in the revision, and we remade the figure and its caption to clarify this point:

We also have updated the description of these results to emphasize how double-dipping was avoided:

“We then mapped the held-out participant's movie data into the learned shared space without changing the shared space (Figure 5c). In other words, the shared response model was learned and frozen before the held-out participant’s data was considered.

This approach has been used and validated in prior SRM studies[45].” Pg. 14

The reviewer suggests that manually choosing components from ICA is double-dipping. Although the reviewer is correct that the manual selection of components in ICA means that the components chosen ought to be good candidates, we are testing whether those choices were good by evaluating those components against the task-based maps that were not used for the ICA. Our statistical analyses evaluate whether the components chosen were better than the components that would have been chosen by random chance. Critically: all decisions about selecting the components happen before the components are compared to the retinotopic maps. Hence there is no double-dipping in the selection of components, as the choice of candidate ICA maps is not informed by the ground-truth retinotopic maps. We now clarify what the goal of this process is in the results:

“Success in this process requires that 1) retinotopic organization accounts for sufficient variance in visual activity to be identified by ICA and 2) experimenters can accurately identify these components.” Pg. 10

The reviewer also alludes to a concern that the researcher selecting the maps was not blind to the ground-truth retinotopic maps from participants and this could have influenced the results. In such a scenario, the researcher could have selected components that have the gradients of activity in the places that the infant has as ground truth. The researcher who made the selection of components (CTE) is one of the researchers who originally traced the areas in the participants approximately a year prior to the identification of ICs. The researcher selecting the components didn’t use the ground-truth retinotopic maps as reference, nor did they pay attention to the participant IDs when sorting the IC components. Indeed, they weren’t trying to find participant specific maps per se, but rather aimed to find good candidate retinotopic maps in general. In the case of the newly added adult analyses, the ICs were selected before the retinotopic mapping was reviewed or traced; hence, no knowledge about the participant-specific ground truth could have influenced the selection of ICs. Even with this process from adults, we find results of comparable strength as we found in infants, as shown below. Nonetheless, there is a possibility that this researcher’s previous experience of tracing the infant maps could have influenced their choice of components at the participant-specific level. If so, it was a small effect since the components the researcher selected were far from the best possible options (i.e., rankings of the selected components averaged in the 64th percentile for spatial frequency maps and the 68th percentile for meridian maps). We believe all reasonable steps were taken to mitigate bias in the selection of ICs.

Reviewer #3 (Public Review):

The manuscript reports data collected in awake toddlers recording BOLD while watching videos. The authors analyse the BOLD time series using two different statistical approaches, both very complex but do not require any a priori determination of the movie features or contents to be associated with regressors. The two main messages are that 1) toddlers have occipital visual areas very similar to adults, given that an SRM model derived from adult BOLD is consistent with the infant brains as well; 2) the retinotopic organization and the spatial frequency selectivity of the occipital maps derived by applying correlation analysis are consistent with the maps obtained by standard and conventional mapping.

Clearly, the data are important, and the author has achieved important and original results. However, the manuscript is totally unclear and very difficult to follow; the figures are not informative; the reader needs to trust the authors because no data to verify the output of the statistical analysis are presented (localization maps with proper statistics) nor so any validation of the statistical analysis provided. Indeed what I think that manuscript means, or better what I understood, may be very far from what the authors want to present, given how obscure the methods and the result presentation are.

In the present form, this reviewer considers that the manuscript needs to be totally rewritten, the results presented each technique with appropriate validation or comparison that the reader can evaluate.

We are grateful to the reviewer for the chance to improve the paper. We have broken their review into three parts: clarification of the methods, validation of the analyses, and enhancing the visualization.

Clarification of the methods

We acknowledge that the methods we employed are complex and uncommon in many fields of neuroimaging. That said, numerous papers have conducted these analyses on adults (Beckman et al., 2005; Butt et al., 2015; Guntupalli et al., 2016; Haak & Beckman, 2018; Knapen, 2021; Lu et al., 2017) and non-human primates (Arcaro & Livingstone, 2017; Moeller et al., 2009). We have redoubled our efforts in the revision to make the methods as clear as possible, expanding on the original text and providing intuitions where possible. These changes have been added throughout and are too vast in number to repeat here, especially without context, but we hope that readers will have an easier time following the analyses now. 

Additionally, we updated Figures 3 and 5 in which the main ICA and SRM analyses are described. For instance, in Figure 3’s caption we now add details about how the gradient analyses were performed on the components: 

“We used the same lines that were manually traced on the task-evoked map to assess the change in the component’s response. We found a monotonic trend within area from medial to lateral, just like we see in the ground truth.” Pg. 11

Regarding Figure 5, we reconsidered the best way to explain the SRM analyses and decided it would be helpful to partition the diagram into steps, reflecting the analytic process. These updates have been added to Figure 5, and the caption has been updated accordingly.

We hope that these changes have improved the clarity of the methods. For readers interested in learning more, we encourage them to either read the methods-focused papers that debut the analyses (e.g., Chen et al., 2015), read the papers applying the methods (e.g., Guntupalli et al., 2016), or read the annotated code we publicly release which implements these pipelines and can be used to replicate the findings.

Validation of the analyses

One of the requests the reviewer makes is to validate our analyses. Our initial approach was to lean on papers that have used these methods in adults or primates (e.g., Arcaro, & Livingstone, 2017; Beckman et al., 2005; Butt et al., 2015; Guntupalli et al., 2016; Haak & Beckman, 2018; Knapen, 2021; Moeller et al., 2009) where the underlying organization and neurophysiology is established. However, we have made changes to these methods that differ from their original usage (e.g., we used SRM rather than hyperalignment, we use meridian mapping rather than traveling wave retinotopy, we use movie-watching data rather than rest). Hence, the specifics of our design and pipeline warrant validation. 

To add further validation, we have rerun the main analyses on an adult sample. We collected 8 adult participants who completed the same retinotopy task and a large subset of the movies that infants saw. These participants were run under maximally similar conditions to infants (i.e., scanned using the same parameters and without the top of the head-coil) and were preprocessed using the same pipeline. Given that the relationship between adult visual maps and movie-driven (or resting-state) analyses has been shown in many studies (Beckman et al., 2005; Butt et al., 2015; Guntupalli et al., 2016; Haak & Beckman, 2018; Knapen, 2021; Lu et al., 2017), these adult data serve as a validation of our analysis pipeline. These adult participants were included in the original manuscript; however, they were previously only used to support the SRM analyses (i.e., can adults be used to predict infant visual maps). The adult results are described before any results with infants, as a way to engender confidence. Moreover, we have provided new supplementary figures of the adult results that we hope will be integrated with the article when viewing it online, such that it will be easy to compare infant and adult results, as per the reviewer’s request. 

As per the figures and captions below, the analyses were all successful with the adult participants: 1) Homotopic correlations are higher than correlations between comparable areas in other streams or areas that are more distant within stream. 2) A multidimensional scaling depiction of the data shows that areas in the dorsal and ventral stream are dissimilar. 3) Using independent components analysis on the movie data, we identified components that are highly correlated with the retinotopy task-based spatial frequency and meridian maps. 4) Using shared response modeling on the movie data, we predicted maps that are highly correlated with the retinotopy task-based spatial frequency and meridian maps.

These supplementary analyses are underpowered for between-group comparisons, so we do not statistically compare the results between infants and adults. Nonetheless, the pattern of adult results is comparable overall to the infant results. 

We believe these adult results provide a useful validation that the infant analyses we performed can recover fine-grained organization.

Enhancing the visualization

The reviewer raises an additional concern about the lack of visualization of the results. We recognize that the plots of the summary statistics do not provide information about the intermediate analyses. Indeed, we think the summary statistics can understate the degree of similarity between the components or predicted visual maps and the ground truth. Hence, we have added 6 new supplementary figures showing the intensity gradients for the following analyses: 1. spatial frequency prediction using ICA, 2. meridian prediction using ICA, 3. spatial frequency prediction using infant SRM, 4. meridian prediction using infant SRM, 5. spatial frequency prediction using adult SRM, and 6. meridian prediction using adult SRM.

We hope that these visualizations are helpful. It is possible that the reviewer wishes us to also visually present the raw maps from the ICA and SRM, akin to what we show in Figure 3A and 3B. We believe this is out of scope of this paper: of the 1140 components that were identified by ICA, we selected 36 for spatial frequency and 17 for meridian maps. We also created 20 predicted maps for spatial frequency and 20 predicted meridian maps using SRM. This would result in the depiction of 93 subfigures, requiring at least 15 new full-page supplementary figures to display with adequate resolution. Instead, we encourage the reader to access this content themselves: we have made the code to recreate the analyses publicly available, as well as both the raw and preprocessed data for these analyses, including the data for each of these selected maps.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) As mentioned in the public review, the authors should consider incorporating relevant adult fMRI research into the Introduction and explain the importance of testing this question in infants.

Our public response describes the several citations to relevant adult research we have added, and have provided further motivation for the project.

(2) The authors should conduct additional analyses to support their conclusion that movie data alone can generate accurate retinotopic maps (i.e., by comparing this approach to other available alternatives).

We have clarified in our public response that we did not wish to conclude that movie data alone can generate accurate retinotopic maps, and have made substantial edits to the text to emphasize this. Thus, because this claim is already not supported by our analyses, we do not think it is necessary to test it further.

(3) The authors should re-do the homotopy analyses using movie-defined ROIs (i.e., by splitting the movie-viewing data into independent folds for functional ROI definition and analyses).

As stated above, defining ROIs based on the movie content is not the intended goal of this project. Even if that were the general goal, we do not believe that it would be appropriate to run this specific analysis with the data we collected. Firstly, halving the data for ROI definition (e.g., using half the movie data to identify and trace areas, and then use those areas in the homotopy analysis to run on the other half of data) would qualitatively change the power of the analyses described here. Secondly, we would be unable to define areas beyond hV4/V3AB with confidence, since our retinotopic mapping only affords specification of early visual cortex. Thus we could not conduct the MDS analyses shown in Figure 2.

(4) If the authors agree that a primary contribution of this study and paper is to showcase what is possible to do with a limited amount of movie-viewing data, then they should make it clearer, sooner, how much usable movie data they have from infants. They could also consider conducting additional analyses to determine the minimum amount of fMRI data necessary to reveal the same detailed characteristics of functional responses in the visual cortex.

We agree it would be good to highlight the amount of movie data used. When the infant data is first introduced in the results section, we now state the durations:

“All available movies from each session were included (Table S2), with an average duration of 540.7s (range: 186--1116s).” Pg. 5

Additionally, we have added a homotopy analysis that describes the contribution of data quantity to the results observed. We compare the amount of data collected with the magnitude of same vs. different stream effect (Figure 1B) and within stream distance effect (Figure 1C). We find no effect of movie duration in the sample we tested, as reported below:

“We found no evidence that the variability in movie duration per participant correlated with this difference [of same stream vs. different stream] (r=0.08, p=.700).” Pg. 6-7

“There was no correlation between movie duration and the effect (Same > Adjacent: r=-0.01, p=.965, Adjacent > Distal: r=-0.09, p=.740).” Pg. 7

(5) If any of the methodological approaches are novel, the authors should make this clear. In particular, has the approach of visually inspecting and categorizing components generated from ICA and movie data been done before, in adults/other contexts?

The methods we employed are similar to others, as described in the public review.

However, changes were necessary to apply them to infant samples. For instance, Guntupalli et al. (2016) used hyperalignment to predict the visual maps of adult participants, whereas we use SRM. SRM and hyperalignment have the same goal — find a maximally aligned representation between participants based on brain function — but their implementation is different. The application of functional alignment to infants is novel, as is their use in movie data that is relatively short by comparison to standard adult data. Indeed, this is the most thorough demonstration that SRM — or any functional alignment procedure — can be usefully applied to infant data, awake or sleeping. We have clarified this point in the discussion.

“This is initial evidence that functional alignment may be useful for enhancing signal quality, like it has in adults[27,32,33], or revealing changing function over development[45], which may prove especially useful for infant fMRI[52].” Pg. 21

(6) The authors found that meridian maps were less identifiable from ICA and movie data and suggest that this may be because these maps are more susceptible to noise or gaze variability. If this is the case, you might predict that these maps are more identifiable in adult data. The authors could consider running additional analyses with their adult participants to better understand this result.

As described in the manuscript, we hypothesize that meridian maps are more difficult to identify than spatial frequency maps because meridian maps are a less smooth, more fine-grained map than spatial frequency. Indeed, it has previously been reported (Moeller et al., 2009) that similar procedures can result in meridian maps that are constituted by multiple independent components (e.g., a component sensitive to horizontal orientations, and a separate component sensitive to vertical components). Nonetheless, we have now conducted the ICA procedure on adult participants and again find it is easier to identify spatial frequency components compared to meridian maps, as reported in the public review.

Minor corrections:

(1) Typo: Figure 3 title: "Example retintopic task vs. ICA-based spatial frequency maps.".

Fixed

(2) Given the age range of the participants, consider using "infants and toddlers"? (Not to diminish the results at all; on the contrary, I think it is perhaps even more impressive to obtain awake fMRI data from ~1-2-year-olds). Example: Figure 3 legend: "A) Spatial frequency map of a 17.1-monthold infant.".

We agree with the reviewer that there is disagreement about the age range at which a child starts being considered a toddler. We have changed the terms in places where we refer to a toddler in particular (e.g., the figure caption the reviewer highlights) and added the phrase “infants and toddlers” in places where appropriate. Nonetheless, we have kept “infants” in some places, particularly those where we are comparing the sample to adults. Adding “and toddlers” could imply three samples being compared which would confuse the reader.

(3) Figure 6 legend: The following text should be omitted as there is no bar plot in this figure: "The bar plot is the average across participants. The error bar is the standard error across participants.".

Fixed

(4) Table S1 legend: Missing first single quote: Runs'.

Fixed

Reviewer #2 (Recommendations For The Authors):

I request that this paper cite more of the existing literature on the fMRI of human infants and toddlers using task-driven and resting-state data. For example, early studies by (first authors) Biagi, Dehaene-Lambertz, Cusack, and Fransson, and more recent studies by Chen, Cabral, Truzzi, Deen, and Kosakowski.

We have added several new citations of recent task-based and resting state studies to the second sentence of the main text:

“Despite the recent growth in infant fMRI[1-6], one of the most important obstacles facing this research is that infants are unable to maintain focus for long periods of time and struggle to complete traditional cognitive tasks[7].”

Reviewer #3 (Recommendations For The Authors):

In the following, I report some of my main perplexities, but many more may arise when the material is presented more clearly.

The age of the children varies from 5 months to about 2 years. While the developmental literature suggests that between 1 and 2 years children have a visual system nearly adult-like, below that age some areas may be very immature. I would split the sample and perhaps attempt to validate the adult SRM model with the youngest children (and those can be called infants).

We recognize the substantial age variability in our sample, which is why we report participant-specific data in our figures. While splitting up the data into age bins might reveal age effects, we do not think we can perform adequately powered null hypothesis testing of the age trend. In order to investigate the contribution of age, larger samples will be needed. That said, we can see from the data that we have reported that any effect of age is likely small. To elaborate: Figures 4 and 6 report the participant-specific data points and order the participants by age. There are no clear linear trends in these plots, thus there are no strong age effects.

More broadly, we do not think there is a principled way to divide the participants by age. The reviewer suggests that the visual system is immature before the first year of life and mature afterward; however, such claims are the exact motivation for the type of work we are doing here, and the verdict is still out. Indeed, the conclusion of our earlier work reporting retinotopy in infants (Ellis et al., 2021) suggests that the organization of the early visual cortex in infants as young as 5 months — the youngest infant in our sample — is surprisingly adult-like.

The title cannot refer to infants given the age span.

There is disagreement in the field about the age at which it is appropriate to refer to children as infants. In this paper, and in our prior work, we followed the practice of the most attended infant cognition conference and society, the International Congress of Infant Studies (ICIS), which considers infants as those aged between 0-3 years old, for the purposes of their conference. Indeed, we have never received this concern across dozens of prior reviews for previous papers covering a similar age range. That said, we understand the spirit of the reviewer’s comment and now refer to the sample as “infants and toddlers” and to older individuals in our sample as “toddlers” wherever it is appropriate (the younger individuals would fairly be considered “infants” under any definition).

Figure 1 is clear and an interesting approach. Please also show the average correlation maps on the cortical surface.

While we would like to create a figure as requested, we are unsure how to depict an area-by-area correlation map on the cortical surface. One option would be to generate a seed-based map in which we take an area and depict the correlation of that seed (e.g., vV1) with all other voxels. This approach would result in 8 maps for just the task-defined areas, and 17 maps for anatomically-defined areas. Hence, we believe this is out of scope of this paper, but an interested reader could easily generate these maps from the data we have released.

Figure 2 results are not easily interpretable. Ventral and dorsal V1-V3 areas represent upper or lower VF respectively. Higher dorsal and ventral areas represent both upper and lower VF, so we should predict an equal distance between the two streams. Again, how can we verify that it is not a result of some artifacts?

In adults, visual areas differ in their functional response properties along multiple dimensions, including spatial coding. The dorsal/ventral stream hypothesis is derived from the idea that areas in each stream support different functions, independent of spatial coding. The MDS analysis did not attempt to isolate the specific contribution of spatial representations of each area but instead tested the similarity of function that is evoked in naturalistic viewing. Other covariance-based analyses specifically isolate the contribution of spatial representations (Haak et al., 2013); however, they use a much more constrained analysis than what was implemented here. The fact that we find broad differentiation of dorsal and ventral visual areas in infants is consistent with adults (Haak & Beckman, 2018) and neonate non-human primates (Arcaro & Livingstone, 2017). 

Nonetheless, we recognize that we did not mention the differences in visual field properties across areas and what that means. If visual field properties alone drove the functional response then we would expect to see a clustering of areas based on the visual field they represent (e.g., hV4 and V3AB should have similar representations). Since we did not see that, and instead saw organization by visual stream, the result is interesting and thus warrants reporting. We now mention this difference in visual fields in the manuscript to highlight the surprising nature of the result.

“This separation between streams is striking when considering that it happens despite differences in visual field representations across areas: while dorsal V1 and ventral V1 represent the lower and upper visual field, respectively, V3A/B and hV4 both have full visual field maps. These visual field representations can be detected in adults[41]; however, they are often not the primary driver of function[39]. We see that in infants too: hV4 and V3A/B represent the same visual space yet have distinct functional profiles.” Pg. 8

The reviewer raises a concern that the MDS result may be spurious and caused by noise. Below, we present three reasons why we believe these results are not accounted for by artifacts but instead reflect real functional differentiation in the visual cortex. 

(1) Figure 2 is a visualization of the similarity matrix presented in Figure S1. In Figure S1, we report the significance testing we performed to confirm that the patterns differentiating dorsal and ventral streams — as well as adjacent areas from distal areas — are statistically reliable across participants. If an artifact accounted for the result then it would have to be a kind of systematic noise that is consistent across participants.

(2) One of the main sources of noise (both systematic and non-systematic) with infant fMRI is motion. Homotopy is a within-participant analysis that could be biased by motion. To assess whether motion accounts for the results, we took a conservative approach of regressing out the framewise motion (i.e., how much movement there is between fMRI volumes) from the comparisons of the functional activity in regions. Although the correlations numerically decreased with this procedure, they were qualitatively similar to the analysis that does not regress out motion:

“Additionally, if we control for motion in the correlation between areas --- in case motion transients drive consistent activity across areas --- then the effects described here are negligibly different (Figure S5).” Pg. 7

(3) We recognize that despite these analyses, it would be helpful to see what this pattern looks like in adults where we know more about the visual field properties and the function of dorsal and ventral streams. This has been done previously (e.g., Haak & Beckman, 2018), but we have now run those analyses on adults in our sample, as described in the public review. As with infants, there are reliable differences in the homotopy between streams (Figure S1). The MDS results show that the adult data was more complex than the infant data, since it was best described by 3 dimensions rather than 2. Nonetheless, there is a rotation of the MDS such that the structure of the ventral and dorsal streams is also dissociable. 

Figure 3 also raises several alternative interpretations. The spatial frequency component in B has strong activity ONLY at the extreme border of the VF and this is probably the origin of the strong correlation. I understand that it is only one subject, but this brings the need to show all subjects and to report the correlation. Also, it is important to show the putative average ICA for retinotopy and spatial frequencies across subjects and for adults. All methods should be validated on adults where we have clear data for retinotopy and spatial frequency.

The reviewer notes that the component in Figure 3 shows strong negative response in the periphery. It is often the case, as reported elsewhere (Moeller et al., 2009), that ICA extracts portions of visual maps. To make a full visual map would require combining components into a composite (e.g., a component that has a high response in the periphery and another component that has a high response in the fovea). If we were to claim that this component, or others like it, could replace the need for retinotopic mapping, then we would want to produce these composite maps; however, our conclusion in this project is that the topographic information of retinotopic maps manifest in individual components of ICA. For this purpose, the analysis we perform adequately assesses this topography.

Regarding the request to show the results for all subjects, we address this in the public response and repeat it here briefly: we have added 6 new figures to show results akin to Figure 3C and D. It is impractical to show the equivalent of Figure 3A and B for all participants, yet we do release the data necessary to see to visualize these maps easily.

Finally, the reviewer suggests that we validate the analyses on adult participants. As shown in Figure S3 and reported in the public response, we now run these analyses on adult participants and observe qualitatively similar results to infants.

How much was the variation in the presumed spatial frequency map? Is it consistent with the acuity range? 5-month-old infants should have an acuity of around 10c/deg, depending on the mean luminance of the scene.

The reviewer highlights an important weakness of conducting ICA: we cannot put units on the degree of variation we see in components. We now highlight this weakness in the discussion:

“Another limitation is that ICA does not provide a scale to the variation: although we find a correlation between gradients of spatial frequency in the ground truth and the selected component, we cannot use the component alone to infer the spatial frequency selectivity of any part of cortex. In other words, we cannot infer units of spatial frequency sensitivity from the components alone.” Pg. 20

Figure 5 pipeline is totally obscure. I presumed that I understood, but as it is it is useless. All methods should be clearly described, and the intermediate results should be illustrated in figures and appropriately discussed. Using such blind analyses in infants in principle may not be appropriate and this needs to be verified. Overall all these techniques rely on correlation activities that are all biased by head movement, eye movement, and probably the dummy sucking. All those movements need to be estimated and correlated with the variability of the results. It is a strong assumption that the techniques should work in infants, given the presence of movements.

We recognize that the SRM methods are complex. Given this feedback, we remade Figure 5 with explicit steps for the process and updated the caption (as reported in the public review).

Regarding the validation of these methods, we have added SRM analyses from adults and find comparable results. This means that using these methods on adults with comparable amounts of data as what we collected from infants can predict maps that are highly similar to the real maps. Even so, it is not a given that these methods are valid in infants. We present two considerations in this regard. 

First, as part of the SRM analyses reported in the manuscript, we show that control analyses are significantly worse than the real analyses (indicated by the lines on Figure 6). To clarify the control analysis: we break the mapping (i.e., flip the order of the data so that it is backwards) between the test participant and the training participants used to create the SRM. The fact that this control analysis is significantly worse indicates that SRM is learning meaningful representations that matter for retinotopy. 

Second, we believe that this paper is a validation of SRM for infants. Infant fMRI is a nascent field and SRM has the potential to increase the signal quality in this population. We hope that readers will see these analyses as a proof of concept that SRM can be used in their work with infants. We have stated this contribution in the paper now.

“Additionally, we wish to test whether methods for functional alignment can be used with infants. Functional alignment finds a mapping between participants using functional activity -- rather than anatomy -- and in adults can improve signal-to-noise, enhance across participant prediction, and enable unique analyses[27,32-34].” Pg. 4

“This is initial evidence that functional alignment may be useful for enhancing signal quality, like it has in adults[27,32,33], or revealing changing function over development[45].” Pg. 21

Regarding the reviewer’s concern that motion may bias the results, we wish to emphasize the nature of the analyses being conducted here: we are using data from a group of participants to predict the neural responses in a held-out participant. For motion to explain consistency between participants, the motion would need to be timelocked across participants. Even if motion was time-locked during movie watching, motion will impair the formation of an adequate model that can contain retinotopic information. Thus, motion should only hurt the ability for a shared response to be found that can be used for predicting retinotopic maps. Hence, the results we observed are despite motion and other sources of noise.

What is M??? is it simply the mean value??? If not, how it is estimated?

M is an abbreviation for mean. We have now expanded the abbreviation the first time we use it.

Figure 6 should be integrated with map activity where the individual area correlation should be illustrated. Probably fitting SMR adult works well for early cortical areas, but not for more ventral and associative, and the correlation should be evaluated for the different masks.

With the addition of plots showing the gradients for each participant and each movie (Figures S10–S13) we hope we have addressed this concern. We additionally want to clarify that the regions we tested in the analysis in Figure 6 are only the early visual areas V1, V2, V3, V3A/B, and hV4. The adult validation analyses show that SRM works well for predicting the visual maps in these areas. Nonetheless, it is an interesting question for future research with more extensive retinotopic mapping in infants to see if SRM can predict maps beyond extrastriate cortex.

Occipital masks have never been described or shown.

The occipital mask is from the MNI probabilistic structural atlas (Mazziotta et al., 2001), as reported in the original version and is shared with the public data release. We have added the additional detail that the probabilistic atlas is thresholded at 0% in order to be liberally inclusive. 

“We used the occipital mask from the MNI structural atlas[63] in standard space -- defined liberally to include any voxel with an above zero probability of being labelled as the occipital lobe -- and used the inverted transform to put it into native functional space.” Pg. 27–28

Methods lack the main explanation of the procedures and software description.

We hope that the additions we have made to address this reviewer’s concerns have provided better explanations for our procedures. Additionally, as part of the data and code release, we thoroughly explain all of the software needed to recreate the results we have observed here.

I think this is one important crux of the study, and could lead to resources useful for the field.

Author response:

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

Reviewer #1:

(1) All analyses were performed on trial-averaged neural responses that were pooled across mice. Owing to differences between subjects in behavior, experimental preparation quality, and biological variability, it seems important to perform at least some analyses on individual analyses to assess how behavioral training might differently affect each animal.

In order to image at a relatively fast rate (30Hz) appropriate to the experimental conditions, we restricted our imaging to a relatively small field of view (412x412um with 512x512 pixels). This entails a smaller number of ROIs per animal, which can lead to an unbalanced distribution of cells responsive to different stimuli for individual fields-of-view. We used the common approach of pooling across animals (Homann et al., 2021; Kim et al., 2019) to overcome limitations imposed by sampling a smaller number of cells per animal. In response to this comment, we included supplemental analyses (Sup.Fig. 6) showing that representational drift (which was not performed on trial-averaged data) looks substantially the same (albeit nosier) for individual animals as at the population level. Additional analyses (PE ratio, etc.) were difficult since the distribution of cells selective for individual stimuli is unbalanced between individual animals and few mice have multiple cells representing all of the different stimuli.

(2) The correlation analyses presented in Figure 3 (labeled the second Figure 2 in the text) should be conducted on a single-animal basis. Studying population codes constructed by pooling across mice, particularly when there is no behavioral readout to assess whether learning has had similar effects on all animals, appears inappropriate to me. If the results in Figure 3 hold up on single animals, I think that is definitely an interesting result.

We repeated the correlation analysis performed on mice individually and included them in the supplement (Supp. Fig. 6). The overall result generally mirrors the result found by pooling across animals.

(3) On Day 0 and Day 5, the reordered stimuli are presented in trial blocks where each image sequence is shown 100 times. Why wasn't the trial ordering randomized as was done in previous studies (e.g. Gavornik and Bear 2014)? Given this lack of reordering, did neurons show reduced predictive responses because the unexpected sequence was shown so many times in quick succession? This might change the results seen in Figure 2, as well as the decoder results where there is a neural encoding of sequence order (Figure 4). It would be interesting if the Figure 4 decoder stopped working when the higher-order block structure of the task was disrupted.

Our work builds primarily on previous studies (Gavornik & Bear, 2014; Price et al., 2023) that demonstrated clear changes in neural responses over days while employing a similar block structure. Notably, Price et al. found that trial number (within a block) was not a significant factor in the generation of prediction-error responses which strongly suggests short-term plasticity does not play a significant role in shaping responses within the block structure. This finding is consistent with our previous LFP recordings which have not revealed any significant plasticity occurring within a training session, a conclusion bolstered by a collaborative work currently in press (Hosmane et al. 2024, Sleep) revealing the requirement for sleep in sequence plasticity expression.

It is possible that layer 2/3 adapts to sequences more rapidly than layer 4/5. While manual inspection does not reveal an obvious difference between early and late blocks in this dataset, the n for this subset is too small to draw firm conclusions. It is our view that the block structure provides the strongest comparison to previous work, but agree it would be interesting to randomize or fully interleave sequences in future studies to determine what effect, if any, short-term changes might have. 

(4) A primary advantage of using two-photon calcium imaging over other techniques like extracellular electrophysiology is that the same neurons can be tracked over many days. This is a standard approach that can be accomplished by using many software packages-including Suite2P (Pachitariu et al. 2017), which is what the authors already used for the rest of their data preprocessing. The authors of this paper did not appear to do this. Instead, it appears that different neurons were imaged on Day 0 (baseline) and Day 5 (test). This is a significant weakness of the current dataset.

The hypothesis being tested was whether expectation violations, as described in Keller & Mrsic-Flogel 2018, exist under a multi-day sequence learning paradigm. For this, tracking cells across days is not necessary as our PE metric compared responses of individual neurons to multiple stimuli within a single session. Given the speed/FOV tradeoff discussed above, we wanted to consider all cells irrespective of whether they were visible/active or trackable across days, especially since we would expect cells that learn to signal prediction errors to be inactive on day 0 and not selected by our segmentation algorithm. Though we did not compare the responses of single cells before/after training, we did analyze cells from the same field of view on days 0 and 5 (see Supp.Fig. 1) and not distinct populations.

Reviewer #2:

(1) There appears to be some confusion regarding the conceptual framing of predictive coding.

Assuming the mouse learns to expect the sequence ABCD, then ABBD does not probe just for negative prediction errors, and ACBD is not just for positive prediction errors. With ABBD, there is a combination of a negative prediction error for the missing C in the 3rd position, and a positive prediction error for B in the 3rd. Likewise, with ACBD, there is a negative prediction error for the missing B at 2nd and missing C at 3rd, and a positive prediction error for the C in 2nd and B in 3rd. Thus, the authors' experimental design does not have the power to isolate either negative or positive prediction errors. Moreover, looking at the raw data in Figure 2C, this does not look like an "omission" response to C, but more like a stronger response to a longer B. The pitch of the paper as investigating prediction error responses is probably not warranted - we see no way to align the authors' results with this interpretation.

The reviewer has identified a real problem with the framing of “positive” and “negative” prediction errors in context of sensory stimuli where substitution simultaneously introduces unexpected “positive” violation and “negative” omission. Simply put, even if there are separate mechanisms to represent positive and negative errors, there may be no way to isolate the positive response experimentally since an unexpected input always replaces the unseen expected input. For example, had a cell fired solely to ACBD (and not during either ABCD or ABCD), then whether it was signaling the unexpected occurrence of C or the unexpected absence of B would be inherently ambiguous. In either case, such a cell would have been labeled as C-responsive, and its activity would have been elevated compared with ABCD and would have been included in our substitution-type analysis of prediction errors. We accept that there is some ambiguity regarding the description in this particular case, but overall, this cell’s activity pattern would have informed the PE analysis for which the result was essentially null for the substitution-type violation ACBD.

Omission, in which the sensory input does not change, may experimentally isolate the negative response though this is only true if there is a temporal expectation of when the change should have occurred. If A is predicting B in an ordinal sense but there is no expectation of when B will occur with respect to A, changing the duration of A would not be expected to produce an error signal since at any point in time B might still be coming and the expectation is not broken until something other than B occurs. With respect specifically to ABBD in our experiments, it is correct that the learned error responses take the form of stronger, sustained responses to B during the time C was expected. This is still in contrast to day 0 in which activation decays after a transient response to ABBD. The data shows that responses during an omitted element are altered with training and take the form of elevated responses to ABBD on day 5.As we say in our discussion, this is somewhat ambiguous evidence of prediction errors since it does emerges only with training and is generally consistent with the hypothesis being tested though it takes a different form than we expected it to.

(2) Related to the interpretation of the findings, just because something can be described as a prediction error does not mean it is computed in (or even is relevant to) the visual cortex. To the best of our knowledge, it is still unclear where in the visual stream the responses described here are computed. It is possible that this type of computation happens before the signals reach the visual cortex, similar to mechanisms predicting moving stimuli already in the retina (https://pubmed.ncbi.nlm.nih.gov/10192333/). This would also be consistent with the authors' finding (in previous work) that single-cell recordings in V1 exhibit weaker sequence violation responses than the author's earlier work using LFP recordings.

Our work was aimed at testing the specific hypothesis that PE responses, at the very least, exist in L2/3—a hypothesis that is well-supported under different experimental paradigms (often multisensory mismatch). Our aim was to test this idea under a sequence learning paradigm and connect it with previously found PE responses in L4. We don’t claim that it is the only place in which prediction errors may be computed or useful, especially since (as you mentioned), there is evidence for such responses in layer 4. But it is fundamentally important to predictive processing that we determine whether PE responses can be found in layer 2/3 under this passive sequence learning paradigm, whether or not they reflect upstream processes, feedback from higher areas, or entirely local computations. Our aim was to establish some baseline evidence for or against predictive processing accounts of L2/3 activity during passive exposure to visual sequences.

(3) Recording from the same neurons over the course of this paradigm is well within the technical standards of the field, and there is no reason not to do this. Given that the authors chose to record from different neurons, it is difficult to distinguish representational drift from drift in the population of neurons recorded.

Our discussion of drift refers to changes occurring within a population of neurons over the course of a single imaging session. We have added clarifying language to the manuscript to make this clear. Changes to the population-level encoding of stimuli over days are treated separately and with different analytical tools. Re. tracking single across days, please see the response to Reviewer #1, comment 4.

(4) The block paradigm to test for prediction errors appears ill-chosen. Why not interleave oddball stimuli randomly in a sequence of normal stimuli? The concern is related to the question of how many repetitions it takes to learn a sequence. Can the mice not learn ACBD over 100x repetitions? The authors should definitely look at early vs. late responses in the oddball block. Also, the first few presentations after the block transition might be potentially interesting. The authors' analysis in the paper already strongly suggests that the mice learn rather rapidly. The authors conclude: "we expected ABCD would be more-or-less indistinguishable from ABBD and ACBD since A occurs first in each sequence and always preceded by a long (800 ms) gray period.

This was not the case. Most often, the decoder correctly identified which sequence stimulus A came from." This would suggest that whatever learning/drift could happen within one block did indeed happen and responses to different sequences are harder to interpret.

This work builds on previous studies that used a block structure to drive plasticity across days. We previously tested whether there are intra-block effects and found no indication of changes occurring within a block or withing a session (please see the response to Reviewer #1, comment 3 for further discussion). Observed drift does complicate comparison between blocks. There is no indication in our data that this is a learned effect, though future experiments could test this directly.

(5) Throughout the manuscript, many of the claims are not statistically tested, and where they are the tests do not appear to be hierarchical (https://pubmed.ncbi.nlm.nih.gov/24671065/), even though the data are likely nested.

We have modified language throughout the manuscript to be more precise about our claims. We used pooled data between mice and common parametric statistics in line with published literature. The referenced paper offers a broad critique of this approach, arguing that it increases the possibility of type 1 errors, though it is not clear to us that our experimental design carries this risk particularly since most of our results were negative. To address the specific concern, however we performed a non-parametric hierarchical bootstrap analysis (https://pmc.ncbi.nlm.nih.gov/articles/PMC7906290/) that re-confirmed the statistical significance of our positive results, see Supplemental Figure 8.

(6) The manuscript would greatly benefit from thorough proofreading (not just in regard to figure references).

We apologize for the errors in the manuscript. We caught the issue and passed on a corrected draft, but apparently the uncorrected draft was sent for review. The re-written manuscript addresses all identified issues.

(7) With a sequence of stimuli that are 250ms in length each, the use of GCaMP6s appears like a very poor choice.

We started our experiments using GCaMP6f but ultimately switched to GCaMP6s due to its improved sensitivity, brightness, and accuracy in spike detection (Huang et al., 2021). When combined with deconvolution (Pachitariu et al., 2018; Pnevmatikakis et al., 2016), we found GCaMP6s provides the most complete and accurate view of spiking within 40ms time bins. The inherent limitations of calcium imaging are more likely to be addressed using electrophysiology rather than a faster sensor in future studies.

(8) The data shown are unnecessarily selective. E.g. it would probably be interesting to see how the average population response evolves with days. The relevant question for most prediction error interpretations would be whether there are subpopulations of neurons that selectively respond to any of the oddballs. E.g. while the authors state they "did" not identify a separate population of omission-responsive neurons, they provide no evidence for this. However, it is unclear whether the block structure of the experiments allows the authors to analyze this.

We concluded that there is no clear dedicated subpopulation of omission-responding cells by inspecting cells with large PE responses (i.e., ABBD, see supplemental figure 3). Out of the 107 B-responsive cells on day 5, only one appeared to fire exclusively during the omitted stimulus. Average traces for all B-responsive cells are included in the supplement and we have updated the manuscript accordingly. Similarly, a single C-responsive cell was found with an apparently unique substitution error profile (ABCD and ACBD , supplemental figure 4).

Our primary concern was to make sure that days 0 and 5 had the highest quality fields-of-view. In work leading up to this study, there were concerns that imaging on all intermediate days resulted in a degradation of quality due to photobleaching. We agree that an analysis of intermediate days would be interesting, but it was excluded due to these concerns. 

Reviewer #3:

(1) Experimental design using a block structure. The use of a block structure on test days (0 and 5) in which sequences were presented in 100 repetition blocks leads to several potential confounds. First, there is the potential for plasticity within blocks, which could alter the responses and induce learned expectations. The ability of the authors to clearly distinguish blocks 1 and 2 on Day 0 with a decoder suggests this change over time may be meaningful.

Repeating the experiments with fully interleaved sequences on test days would alleviate this concern. With the existing data, the authors should compare responses from the first trials in a block to the last trials in a block.

This block design likely also accounts for the ability of a decoder to readily distinguish stimulus A in ABCD from A in ABBD. As all ABCD sequences were run in a contiguous block separate from ABBD, the recent history of experience is different for A stimuli in ABCD versus ABBD. Running fully interleaved sequences would also address this point, and would also potentially mitigate the impact of drift over blocks (discussed below).

As described in other responses, the block structure was chosen to align more closely with previous studies. We take the overall point though, and future studies will employ the suggested randomized or interleaved structure in addition to block structures to investigate the effects of short-term plasticity.

(2) The computation of prediction error differs significantly for omission as opposed to substitutions, in meaningful ways the authors do not address. For omission errors, PE compares the responses of B1 and B2 within ABBD blocks. These responses are measured from the same trial, within tens of milliseconds of each other. In contrast, substitution PE is computed by comparing C in ABCD to C in ACBD. As noted above, the block structure means that these C responses were recorded in different blocks, when the state of the brain could be different. This may account for the authors' detection of prediction error for omission but not substitution. To address this, the authors should calculate PE for omission using B responses from ABCD.

We performed the suggested analysis (i.e., ABBD vs ABCD) prior to submission but omitted it from the draft for brevity (the effect was the same as with ABBD vs ABBD). We have added the results of standardizing with ABCD as supplementary figure 3.

(3) The behavior of responses to B and C within the trained sequence ABCD differs considerably, yet is not addressed. Responses to B in ABCD potentiate from d0-> d5, yet responses to C in the same sequence go down. This suggests there may be some difference in either the representation of B vs C or position 2 vs 3 in the sequence that may also be contributing to the appearance of prediction errors in ABBD but not ACBD. The authors do not appear to consider this point, which could potentially impact their results. Presenting different stimuli for A,B,C,D across mice would help (in the current paper B is 75 deg and C is 165 deg in all cases). Additionally, other omissions or substitutions at different sequence positions should be tested (eg ABCC or ABDC).

We appreciate the suggestion. Ideally, we could test many different variants, but practical concerns regarding the duration of the imaging sessions prevented us from testing other interesting variations (such as ABCC) in the current study. We are uncertain as to how we should interpret the overall depressed response to element C seen on day 5, but since the effect is shared in both ABCD and ACBD, we don’t think it affected our PE calculations. 

(4) The authors' interpretation of their PCA results is flawed. The authors write "Experience simplifies activity in principal component space". This is untrue based on their data. The variance explained by the first set of PCs does not change with training, indicating that the data is not residing in a lower dimensional ("simpler") space. Instead, the authors show that the first 5 PCs better align with their a priori expectations of the stimulus structure, but that does not mean these PCs necessarily represent more information about the stimulus (and the fact that the authors fail to see an improvement in decoding performance argues against this case). Addressing such a question would be highly interesting, but is lacking in the current manuscript. Without such analysis, referring to the PCs after training as "highly discretized" and "untangled" are largely meaningless descriptions that lack analytical support.

We meant the terms “simpler”, “highly-discretized”, and “untangled” as qualitative descriptions of changes in covariance structure that occurred despite the maintenance of overall dimensionality. As the reviewer notes, the obvious changes in PC space appear to have had practically no effect on decodability or dimensionality, and we found this surprising and worth describing.

(5) The authors report that activity sparsifies, yet provide only the fraction of stimulus-selective cells. Given that cell detection was automated in a manner that takes into account neural activity (using Suite2p), it is difficult to interpret these results as presented. If the authors wish to claim sparsification, they need to provide evidence that the total number of ROIs drawn on each day (the denominator for sparseness in their calculation) is unbiased. Including more (or less) ROIs can dramatically change the calculated sparseness.

The authors mention sparsification as contributing to coding efficiency but do not test this. Training a decoder on variously sized subsets of their data on days 0 and 5 would test whether redundant information is being eliminated in the network over training.

First, we provide evidence for sparseness using a visual responsiveness metric in addition to stimulus-selectivity. Second, it is true that Suite2p’s segmentation is informed by activity and therefore may possibly omit cells with very minimal activity. However, we detected a comparable number of cells on day 5 (n=1500) to day 0 (1368). We reportedly roughly half as many cells are stimulus-selective on day 5 compared with day 0. In order for that to have been a result of biased ROI segmentation, we would have needed to have detected closer to 2600 cells on day 5 rather than 1500.  Therefore, we consider any bias in the segmentation to have had little effect on the main findings.

(6) The authors claim their results show representational drift, but this isn't supported in the data. Rather they show that there is some information in the structure of activity that allows a decoder to learn block ID. But this does not show whether the actual stimulus representations change, and could instead reflect an unrelated artifact that changes over time (responsivity, alertness, bleaching, etc). To actually assess representational drift, the authors should directly compare representations across blocks (one could train a decoder on block 1 and test on blocks 2-5). In the absence of this or other tests of representational drift over blocks, the authors should remove the statement that "These findings suggest that there is a measurable amount of representational drift".

“To actually assess representational drift, the authors should directly compare representations across blocks (one could train a decoder on block 1 and test on blocks 25)”: This is the exact analysis that was performed. Additionally, our analysis of pairwise correlations directly measures representational drift.

“But this does not show whether the actual stimulus representations change, and could instead reflect an unrelated artifact that changes over time (responsivity, alertness, bleaching, etc)”: We have repeated the decoder analysis using normalized population vectors (Supplementary Figure 5) which we believe directly addresses whether the observed drift is due to photobleaching or alertness that would affect the overall magnitudes of response vectors.

Our analysis of block decoding reflects decoders trained on individual stimulus elements, and we show the average over all such decodings (we have clarified this in the text). For example, we trained a decoder on ABCD presentations from block 1 and tested only against ABCD from other blocks, which I believe is the test being suggested by the reviewer. Furthermore, we do show that representational similarity for all stimulus elements reduces gradually and more-or-less monotonically as the time between presentations increases. We believe this is a fairly straightforward test of representational drift as has been reported and used elsewhere (Deitch et al., 2021).

(7) The authors allude to "temporal echoes" in a subheading. This term is never defined, or substantiated with analysis, and should be removed.

We hoped the term ‘temporal echo’ would be understood in the context of rebounding activity during gray periods as supported by analysis in figure 6a. We have eliminated the wording in the updated manuscript.

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

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Reply to the reviewers

1. General Statements [optional]

We thank the reviewers for their insightful comments regarding our study and for appreciating the range of experiments used, the depth of our study and the significance of our work. We also thank reviewers with expertise in evolutionary biology for highlighting the need for precise wrong of some parts of the manuscript and the need for balancing the various viewpoints on the current understanding of early metazoan evolution. A point-by-point response to each reviewer comment is given below. We believe that we can effectively address most reviewer comments in a revised version. The revised improved manuscript will be the first insightful study of intracellular signalling pathways in the context of early animal evolution. We thank the reviewer for noting that this study is highly impactful and can have a broader influence on the scientific community.

2. Description of the planned revisions

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

__ Summary: The researchers identified PIP4K (phosphatidylinositol 5 phosphate 4-kinase) as a lipid kinase that is specific to metazoans. In order to determine its conserved function across metazoans, they compared PIP4K activity in both early-branching metazoans and bilaterian animals. Biochemical assays demonstrated a conserved catalytic activity between the sponge Amphimedon queenslandica (AqPIP4K) and human PIP4K. In in-vivo experiments, AqPIP4K was found to rescue the reduced cell size, growth, and development phenotype in larvae of null mutant in Drosophila PIP4K. Based on these findings, the authors suggest that the function of PIP4K was established in early metazoans to facilitate intercellular communication. The experiments were well designed, and a range of biochemical, in vitro, and in vivo experiments were conducted.__

__ That being said, there are some questions that require further discussion before we can fully accept the author's conclusion of an evolutionarily conserved function of PIP4K across metazoans.__

Major comments:

• The authors mentioned that PIP4K is metazoan-specific and involved in intercellular communication. How can we explain the presence of PIP4K in choanoflagellate genomes? Despite its high similarity with conserved domains and functionally important residues, experimental results with the PIP4K from Choanoflagellate (Monosiga brevicollis, MbPIP4K) such as Mass spectrometry-based kinase assay and mutant Drosophila PIP4K didn't show similar activity to sponge AqPIP4K. The authors suggested that "In the context of other ancient PIP4K it is possible that since choanoflagellates exist as both single-cell and a transient multicellular state and do not have the characteristics of metazoans, PIP4K does not play any important functional role in these." However, this explanation is not well justified; they need to provide a more detailed discussion on this. Response: PIP4K is found in the genome of the choanoflagellate, M.brevicollis. MbPIP4K has the requisite kinase domain and the critical residue in the activation loop (A381) required for PIP4K activity is also conserved with the Amphimedon enzyme. Despite this, MbPIP4K was unable to rescue the growth and cell size phenotype of dPIP4K mutants (dPIP4K29) unlike AqPIP4K.

We have previously published a comparison of the in vitro activity versus in vivo function for the three PIP4K enzymes in the human genome (Mathre et.al PMID: __30718367). While all three human PIP4K isoforms can functionally rescue the Drosophila dPIP4K mutant, there is a nearly 104-fold difference for in vitro activity between them with PIP4K2C showing almost no in vitro activity. __The difference in in vitro enzyme activity between MbPIP4K and AqPIP4K is similarly notable. We would however highlight that this is more likely a reflection of the limitations of the in vitro PIP4K activity.

However, while AqPIP4K can rescue function in vivo (rescue of fly mutant phenotypes) MbPIP4K could not when expressed in fly cells. This must imply that there are differences in the polypeptide sequences of AqPIP4K and MbPIP4K that allow the former but not the latter to couple to the Insulin PI3K signalling pathway in fly cells. Given that Amphimedon and Choanoflagellates are separated by 100-150 Mya in evolution, this is possible. Our data on expression of AqPIP4K and MbPIP4K in fly S2 cells shows that they do not have equivalent localization (Fig 2C). What are the differences in the two polypeptides that lead to this? We will perform a multiple sequence alignment using PIP4K sequences from multiple choanoflagellates and sponges to identify these differences.

We will include the results of this analysis and an appropriate discussion in the revised manuscript.

• Likewise, the PIP4K gene has been identified in cnidarians, which are a sister group to bilaterian animals. However, the Cnidaria HvPIP4K showed no activity in biochemical or functional assays. In comparison to sponges, cnidarians are relatively complex organisms, and I believe that PIP4K is highly important for intercellular communication, as it is in bilaterians. The authors attempted to explain this by suggesting that "Based on theories of parallel evolution between cnidarians and sponges during early metazoan evolution, it is possible that the PIP4K gene was retained functional in one lineage and not in other." However, I am not convinced by this statement.

Response: This is a really interesting and challenging question from the reviewer. We are aware that both sponges (Porifera) and Cnidaria are examples of primitive metazoans separated by 80-90 Mya of evolution, yet while AqPIP4K shows activity and can functionally rescue dPIP4K mutants, HvPIP4K cannot. What does this mean?

A key difference between sponges and cnidarians is that while cnidarians have a simple “nerve-net” like nervous system, sponges do not have such a mode of communication. Therefore, it is possible that PIP4K, which we propose works in the context of hormone-based communication, is functionally important in sponges.

We are of course aware and acknowledge that in a like for like experimental system (Drosophila cells) our data shows that the two proteins behave differently, be it in terms of in vitro activity or in vivo function. This must imply inherent differences in the two polypeptides.

What we propose to do is to compare available PIP4K sequences from multiple Porifera and Cnidaria genomes and try and understand differences in the protein sequence that might explain differences in function. These results and their implications will be included in the revised manuscript.

• Please provide details of the databases (Uniprot-KB, NCBI sequence database, Pfam) versions. After identifying the specific PIP4K protein in each species (e.g. AqPIP4K and HvPIP4K), have you considered performing a reciprocal blast against the human genome to see if you have a top hit to PIP4K? Hence, the main focus of the project is on PIP4K as a metazoan-specific protein. We need to include a wider representation of non-bilaterian animals, including multiple species from sponges, ctenophores, placozoans, and cnidarians. Additionally, please check if homologues of PIP4K are present in other unicellular holozoans besides choanoflagellates. Response: We will add the NCBI IDs for all the sequences. We have carried out reciprocal blast to human proteome and then classified the selected sequences as PIP4K, we will add the results in the supplementary for the same. We will add more species of sponges, ctenophores, placozoans, and cnidarians in our analysis of PIP4K sequences. We will also include an analysis of other unicellular holozoans where genome sequence is available.

• Authors suggested the identification of other components of the PI signaling pathway along with PIP4k in the sponge. What is the status of these PI signaling pathway genes in other non-bilaterians and choanoflagellates? Response: We will add the details of the same in the revised manuscript and agree that this will help enhance the interpretation of our results.

• Phylogenetic tree of all PIP4K sequences (Figure 1C): How authors can be certain that the identified PIP4K sequences (e.g. AqPIP4K, HvPIP4K, and MbPIP4K) are indeed PIP4K, especially when there are several closely related proteins? It is important to conduct phylogenetic analysis alongside other PIP sequences (such as PI3K, PI4K, PIP5K, and PIP4K). If this analysis is carried out, the identified AqPIP4K, HvPIP4K, and MbPIP4K should be grouped together with human PIP4K in the same cluster. Response: As described in the methods, we have searched all the individual genomes analyzed for all PIK and PIPK enzyme sequences. We have marked the domains (using Pfam and Interpro) on these sequences and eliminated other PIK and PIPK sequences (such as PI3K, PI4K, PIP5K) and selected only PIP4K. To additionally confirm the distinction between PIP5K and PIP4K, we have manually inspected each sequence to establish the identity of the A381 amino acid residue in the activation loop. The identity of the amino acid at this position in the activation loop has been experimentally demonstrated to be an essential feature of PIP4K (Kunze et.al PMID: 11733501) and we have also confirmed this independently in a recent study (Ghosh et.al PMID: 37316298).

We will perform the phylogenetic analysis of the phosphoinositide kinases in the format suggested by the reviewer and add it in the revision as a supporting evidence.

Minor comments:

• Line 157: Phylogenetic conservation of PIP4Ks: Please provide details about bootstrap analysis. Response: Will be added

• Line 230: symbol correction 30{degree sign}C Response: Will be done

• Line 429-430: "from early metazoans like Sponges, Cnidaria and Nematodes." Nematodes are not considered early metazoans. Response: Apologies for the typo. This will be corrected. We agree that nematodes are not early metazoans.

• Line 477-478: "However, interestingly, MbPIP4K::GFP localizes only at the plasma membrane in S2 cells (Figure 2C)." This part was not further discussed. Can you please elaborate on why MbPIP4K::GFP localizes only at the plasma membrane in S2 cells? Response: We have discussed this point specifically in response to major comment by the reviewer and it will be addressed as described.

• Line 598: "the earliest examples of metazoa, namely the coral A. queenslandica" A. queenslandica is a sponge, not coral. Response: Apologies for the error. We will correct it.

• Line 602: "Amphimedon and human enzyme, although separated by 50Mya years of evolution" I think it's 500 million years ago, not 50 million years ago. Response: This typo will be corrected.

• Line 612: "coordinated communication between the cells is the most likely function" the cell. Response: Will change the sentence accordingly

• Line 614: "intracellular phosphoinositide signalling the identity of the hormone" missing full stop punctuation. Response: Will change the sentence accordingly

• Line 802 - 804: "other by way of difference in colour. The sub clusters have been numbered (1- early metazoans, 2- Nematodes, 3- Arthropods, 4- Molluscs, 5- Vertebrates (isoform PIP4K2C), 6- Vertebrates (isoform PIP4K2A), 7- Vertebrates (isoform PIP4K2B)." In the Figure, I can't find numbers on the subclusters. Response: Will add the numbers in the figure.

• Line 805- 807: "Phylogenetic analysis of selected PIP4K sequences from model organisms of interest. PIP4K from A. queenslandica has been marked in rectangular box." The rectangular box is missing in the figure. Response: Will change the figure accordingly

• Figure 1C: full forms of species names are missing. Response: Will change the figure accordingly

Reviewer #1 (Significance (Required):

The data is presented well, and the authors used a wide range of assays to support their conclusion. The study is highly impactful and can have a broader influence on the scientific community, particularly in evolutionary molecular biology, development, and biochemistry.

The study provides interesting findings; however, the reasons for PIP4K not being functional in cnidarians as in sponges and why PIP4K is present in unicellular holozoans but not functional are unclear.

We thank the reviewer for appreciating the significance and impact of our study. The very helpful questions raised by the reviewer will help enhance the quality of our study even further. We will make every effort to address these queries.

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

The manuscript by Krishnan et al. uses molecular phylogenetics, in vitro kinase assays, heterologous expression assays in Drosophila S2 cells and mutant complementation assays in yeast to study the evolution and function of putative PIP4 kinase genes from a sponge, a cnidarian and a choanoflagellate. Based on these experiments, the authors conclude that PIP4K is metazoan-specific and that the sponge PIP4K has conserved functions in selectively phosphorylating PI5P.

The study is in principle of interest and it could all be valid data, but the large number of flaws in the data presentation and/or analysis just makes it hard to assess the quality and thus validity of the data and conclusions.

We thank the reviewer for appreciating the potential interest in our findings of PIP4K function in early metazoans. We thank them for noting the need for correcting data presentation and these will be done in the revision.

__ Major comments:__

Overall, the manuscript lacks scientific rigor in the analysis and representation of the results, and the validity of many of the conclusions is therefore difficult to assess.

Major problems are:

(i) The authors base their study on the evolution of PIP4K genes on a deeply flawed concept of animal evolution. On multiple occasions, including the title, the authors refer to extant species (e.g. Amphimedon) as 'early metazoan', 'regarded as the earliest evolved metazoan' (l. 46-7) or 'the earliest examples of metazoans' just to name a few. This reflects a 'ladder-like' view on evolution that suggests that extant sponges are identical to early 'steps' of animal evolution.

We thank the reviewer who is clearly vastly more experienced in the field of evolutionary biology for the possible imprecise/incorrect usage of the word “ancient metazoan”. As new entrants to this area of evolutionary biology, we have of course referred to the existing literature such as PMID: 20686567 to guide us. This paper describes the sequencing of the A. queenslandica genome. It is clear that there is perceived value in studying this sponge in the context of early animal evolution although we are aware of there are a multitude of sponges and not all of them may be of value in the study of early animal evolution. We will peruse the literature more carefully and revise the manuscript to provide a more balanced view of this very interesting but unresolved area.

Also, the author's interpretation that one cluster of genes 'contained the sequences from early metazoans like sponges, cnidaria and nematodes' is referring to an outdated idea of animal phylogeny where nematodes were thought to be ancestrally simple organisms grouped as 'Acoelomata'. This idea of animal phylogeny was however disproven by molecular phylogenetics since the 1990ies.

Response: We are aware that the field of animal classification is undergoing continuous evolution. While earlier classifications may have been based of the presence or otherwise of a coelom and/or other anatomical features, we are aware of the use of molecular phylogenetics.

The phylogeny presented in Fig 1C is based on the sequence relationships between the PIP4K sequences from various animal genomes. Any errors in the labelling of groups such as that highlighted by the reviewer will be revised or corrected after a careful consideration of extant views in the field, which are somewhat varied.

(ii) The description of taxa in the phylogenetic tree in Fig. 1B lacks any understanding of phylogenetic relationships between animals and other eukaryotic groups. What kind of taxa are 'invertebrates' or 'parasites'? And why would 'invertebrates' exclude cnidarians and sponges? Also, why is the outgroup of opisthokonts named 'Eukaryota'?? Are not all organisms represented on the tree eukaryotes?

Response: We apologize for this imprecision in labelling taxa. This will be corrected.

(iii) The methods part lacks any information about the type of analysis (ML, Bayesian, Parsimony?) used to perform the phylogenetic analysis shown in Fig. 1C. Also, the authors mention three distinct clusters (l.428) that are not labelled in the figure.

Response: We will update the methods to include the additional details requested by the reviewer. Fig 1C will be re-labelled.

(iv) The validity of the Western Blot is difficult to assess as the authors have cut away the MW markers. Without, it is for example difficult to assess the size differences visible between Hydra and Monosiga PIP4K-GFP proteins on Fig. 2B. Also, it has become standard practice to show the whole Western blot as supplementary data in order to assess the correct size of the bands and the specificity of the antibody. This is also missing from this manuscript.

Response: Cropped Western blots have been shown to facilitate figure preparation in the main manuscript. The complete uncropped Western blots, in all cases, will be shared as Source data as is the standard practice for multiple journals in the review Commons portfolio.

(v) The authors claim that AqPIP4K was able to convert PI3P into PI with very low efficiency (Figure 2E), but without further label in the figure or explanation, it remains unclear how the authors come to this conclusion.

Response: We regret the typo in line 500 of the manuscript we have stated that “Further,……… was able to convert PI3P into PI with very low efficiency (Figure 2E).” What we intended to write was “Further,……… was able to convert PI3P into PI (3,4) P2 with very low efficiency (Figure 2E).” The efficiency with which this reaction takes place is very low and has been reported by us (Ghosh et.al PMID: 31652444) and others (Zhang et.al PMID: 9211928). At the exposure of the TLC shown in Fig 2E the PI(3,4)P2 spot cannot been seen. Much longer exposures of the TLC plate will be needed to see the PI(3,4)P2 spot. This will be corrected in a revised version of the manuscript.

(vi) The box plots in Fig. 3C and D lack error bars and thus seem to be consisting of only single data points without replicates. Also, Fig. 3C is a quantification of Fig. 3B but it remains unclear what has been quantified and how. It is also unclear how %PIP2 was determined.

Response: For Fig 3C, the colony count has been done from three replicates and the average has been considered to calculate the % growth for each genotype. We will include error bars and clarify this in the revised figure legend. For Fig 3D, the PIP2/PIP ratio has been calculated from biological replicates and average has been represented in the graphs. The individual values can be provided as supplementary data.

(vii) Throughout Fig. 4, I do not understand the genotypes indicated on the x-axis of the plots and below the images. I read the figure legends and manuscript describing these results at least 3 times, but cannot figure out what it all means. On Fig. 4C, what is the wild-type situation?

Response: We apologize for the lack of precision in labelling the figures versus the figure legends. This will be corrected in the revision:

The genotypes are as follows

• w1118 (control) * Act-GAL4. This has been referred to as wild type in the figure legend and called Act-Gal4 in Fig4 panels A-E
• dPIP4K29 – This refers to the protein null strain of dPIP4K. This strain is the background in which all reconstitutions of PIP4K genes have been done.
• PIP4K transgene from A. queenslandica.
• AqPIP4KKD Kinase dead PIP4K transgene from * queenslandica. In panels A, B, D and E, Act-GAL4: dPIP4K29* indicates the genetic background in which either AqPIP4K or AqPIP4KKD has been reconstituted.

Reviewer #2 (Significance (Required)):

If validated and put in the right phylogenetic context, the study is potentially contributing to expanding our knowledge on the evolution of metazoan-specific features, especially the evolution of proteins involved in cell-cell signalling and growth control. My field of expertise is broadly in evo-devo, molecular phylogentics, developmental genetics and cell biology. The in vitro lipid analysis seems interesting and potentially valid but I do not have sufficient expertise to evaluate its validity.

We thank the reviewer for appreciating the novelty of our contribution and its potential to contribute to understanding the evolution of metazoan specific signalling systems, once appropriate corrections have been made. We also appreciate their positive comment on our in vitro experimental analysis. This paper is a big effort to not only perform phylogenetic analysis but address the emerging interpretations experimentally as much as possible.

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

Summary In this manuscript, the authors investigate the evolutionary origins of metazoan Phosphatidylinositol phosphates (PIPs) signaling by elucidating the sequence and function of the PIP4K enzyme, which is crucial for converting PI5P to PI(4,5)P2 through phosphorylation. The authors have described PIP4K-like sequences distributed throughout metazoans and choanoflagellates through an extensive sequence screening. With in vitro and in vivo functional assays, the authors have shown that the sponge A. queenslandica PIP4K (AqPIP4K) is functionally similar to its human counterpart and highlight the major discovery of this study - that PIP4K protein function dates back to as early as sponges.

We thank the reviewer for noting the major finding of our study and our efforts to experimentally validate, using multiple approaches, the findings of our detailed bioinformatics analysis of PIP4K gene distribution across the tree of life.

Major comments

There are two key limitations to this paper. Like the sponges, ctenophores are one of the earliest branching metazoans. They are not well addressed in the paper. Secondly, despite finding PIP4 homologs in choanoflagellates, the authors claim that PIP4 is metazoan-specific.

We thank the reviewer for highlighting these two points; we recognize that both of these are important to address, to the extent that it is possible to do so. These will be addressed using the approaches detailed in the response to reviewer 1 comments.

1. Line 46: A. queenslandica is the earliest branching metazoan. The phylogeny of sponges and ctenophores is not conclusively defined and hence, the statement must be rephrased. Despite the brief description of the evolution of metazoan lineage in the discussion section, ctenophores are missing from the phylogenetic tree. At least a sequence-level information PIP4K in ctenophores would strongly back the claims of the manuscript. Here is the link to the Mnemiopsis database. Response: We thank the reviewer for highlighting this point and pointing us to the Mnemiopsis database. We will most certainly analyse ctenophore genome sequences and add the ctenophore PIP4K sequence to the phylogeny, post analysis and the discussion will be modified to reflect the findings.

Mentioning that choanoflagellates contain homologs of PIP4K contradicts the statement that PIP4K is metazoan-specific. As per Fig 1E., the domain organization of PIP4K is conserved among choanoflagellates and metazoans. What is the percent sequence similarity to the query? This could answer why it doesn't show activity in Drosophila rescues - the system might simply not be compatible with the choanoflagellate homolog. The same may apply to the cnidarian homolog HvPIP4K. Further evidence is needed before concluding that MbPIP4K doesn't phosphorylate PIP5. It is additionally fascinating that MbPIP4K localizes at the plasma membrane unlike other homologs - this function might be choano-specific. Overall, PIP4K's possible origin in the choanoflagellate-metazoan common ancestor backs the current research that choanoflagellates indeed hold clues to understanding metazoan evolution. Further research is necessary before concluding (as in line 648) in the discussions section, where it is mentioned that "PIP4K does not play any important functional role in choanos".

Response: We thank the reviewer for highlighting the very interesting but incompletely understood facets of our study vis-à-vis choanoflagellates versus metazoans. The proposal for additional analysis is indeed interesting and we will carry out these analysis and revise the text accordingly.

__ Minor Comments__

1. A detailed comparison of the sequence of the hydra PIP4K might help understand why it may not have worked like the sponge PIP4K. The discussion on the cnidarian PIP4K evolution is not convincing. It may not have worked because of it being expressed in a non-natural system. Structure prediction and comparison of proteins from different early branching animals should be used. Response: Thank you for these suggestions to understand why the cnidarian PIP4K may not have been functional. We will perform the suggested analysis and incorporate the data into the revision.

78 - Multicellularity evolved many times. Maybe say 'first evolved metazoans'

Response: Thank you for the suggestion.

Line 598 A. queenslandica is not a coral, it's a sponge.

Response: Text will be changed accordingly

Line 612 'thcells' à 'the cells'

Response: Text will be changed.

Line 623 - full stop missing after metazoans.

Response: Text will be changed

Figure 1B - Classification should be consistent - C. elegans is a species name, whereas ctenophores and vertebrates belong to a different classification. Invertebrates is not a scientific group. The edges of the lines of the phylogenetic tree don't join and they need to be arranged correctly.

Response: The names in the phylogeny will be changed to maintain uniformity. The representation of the phylogeny will be changed as mentioned.

Figure 2B The full blot could be shown in the supplement.

Response: Full blot will be provided as source data on resubmission or included as supplementary based on the destination journal’s specification.

Optional

1. Heterologous overexpression does not always provide the full picture of the gene functionality. To make claims on the evolution of function, testing gene functions homologous systems can give a better picture. For example, performing in vitro kinase activity assays of MbPIP4K after overexpressing PIP4K in Monosiga brevicollis. would be a great. Data is missing also about the presence and function of ctenophore PIP4K. Overexpression of ctenophore-PIP4K in Drosophila for functional analyses could help in understanding the distribution/diversity of function of PIP4K in early animals. Response: We agree with the reviewer that heterologous expression may sometimes not replicate the biochemical environment of cells in the organism from which the gene being expressed was originally derived. Yet, heterologous expression experiments do sometimes provide an insight into properties solely dependent on the polypeptide with limited or no contribution from the cellular environment. In principle expressing PIP4K in M.brevicollis cells and then performing kinase assays would be a very good idea. However, we would like to highlight that till date there has been only one study where septins have been transfected in Choanoflagellates and their localization being observed. We are not set up to culture M. brevicollis and will be unable to do this for a revision of the current manuscript. However, we appreciate the importance of this experiment and will do this in collaboration with a choanoflagellate lab in a follow up study to this one.

Ctenophores like cnidarians have two main layers of cells that sandwich a middle layer of jelly-like material, while, more complex animals have three main cell layers and no intermediate jelly-like layer. Hence ctenophores and cnidarians have traditionally been labelled diploblastic. Studies have shown that ctenophores and unicellular eukaryotes share ancestral metazoan patterns of chromosomal arrangements, whereas sponges, bilaterians, and cnidarians share derived chromosomal rearrangements. Conserved syntenic characters unite sponges with bilaterians, cnidarians, and placozoans in a monophyletic clade while ctenophores are excluded from this clustering, placing ctenophores as the sister group to all other animals. Ctenophore PIP4K sequence can be identified and compared as discussed before to other PIP4K sequences used in this study.

Reviewer #3 (Significance (Required)):

Significance: This is the first study that addresses PIP signaling pathway in early metazoans. The findings of this manuscript contribute to the understanding of second-messenger signaling and its link with the origin and evolution of metazoan multicellularity. PIP signaling is crucial in different metazoan aspects such as cytoskeletal dynamics, neurotransmission, and vesicle trafficking, and hence, plays a critical role in metazoan multicellularity. Through this study, it was interesting to see that some components of the PIP signaling pathway are conserved in yeast, but some, such as the PIP4K protein evolved at the brink of metazoan evolution, highlighting the need for complexity in metazoans and their close relatives - the facultatively multicellular choanoflagellates. Since this is a crucial pathway in human biology and has medical significance due to its role in tumorigenesis and cancer cell migration, this study serves the audience in basic research such as evolutionary biology, and applied research such as human medicine. My field of expertise is molecular biology, cell biology and microbiology, with specific expertise on choanoflagellates. Therefore, it is exciting to see the homologs of PIP4K present in choanoflagellates.

__ Evidence, Reproducibility, and clarity:__

The authors have made a clear case of why PIP4K needs to be studied. They have thoroughly mapped PIP4K throughout the tree of life. The results are clear and reproducible. With the findings of this study, they have linked the PIP signalling cascade and metazoan evolution. Using the heterologous expression of sponge A. queensladica PIP4K, they have made compelling evidence that AqPIP4K functions in PIP5 phosphorylation, as seen in humans and Drosophila. However, it was not convincing why the hydra PIP4K was not functional. It was also not convincing why the PIP4K is metazoan-only when there is a conserved sequence (with conserved domain structure) present in choanoflagellates.

We thank the reviewer for appreciating the novelty and importance of our findings in multiple areas of basic biology related to early metazoans and basic biomedical sciences. We also note their comments on the clear and reproducible results presented. Points raised related to the lack of functionality of PIP4K from Hydra and choanoflagellates are noted and will be addressed as indicated in response to other reviewer comments.

Experiments/Analysis to be done

1. We will perform a multiple sequence alignment using PIP4K sequences from multiple choanoflagellates and sponges to identify these differences.
2. What we propose to do is to compare available PIP4K sequences from multiple Porifera and Cnidaria genomes and try and understand differences in the protein sequence that might explain differences in function.
3. We will add more species of sponges, ctenophores, placozoans, and cnidarians in our analysis of PIP4K sequences. We will also include an analysis of other unicellular holozoans where genome sequence is available.
4. We will perform the phylogenetic analysis of the phosphoinositide kinases in the format suggested by the reviewer and add it in the revision as a supporting evidence.
5. Structure prediction and comparison of proteins from different early branching animals should be used.
6. Uniformity of terminology and alignment with conventions in the field of animal taxonomy
7. NCBI ID of sequences to be added and include more non-bilaterian animals sequences in phylogeny- redo the phylogeny.
8. Check for PI signalling genes in choanoflagellates
9. More detailed description of phylogenetic analysis.
10. Add complete Western blot as source data.
11. *

3. Description of the revisions that have already been incorporated in the transferred manuscript

Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. If no revisions have been carried out yet, please leave this section empty.

• *

4. Description of analyses that authors prefer not to carry out

• Expression of PIP4K in choanoflagellates and in vitro kinase assays with lysates. It is beyond our technical ability to perform these experiments at this stage.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This work aims to understand the role of thalamus POm in dorsal lateral striatum (DLS) projection in learning a sensorimotor associative task. The authors first confirm that POm forms "en passant" synapses with some of the DLS neuronal subtypes. They then perform a go/no-go associative task that consists of the mouse learning to discriminate between two different textures and to associate one of them with an action. During this task, they either record the activity of the POm to DLS axons using endoscopy or silence their activity. They report that POm axons in the DLS are activated around the sensory stimulus but that the activity is not modulated by the reward. Last, they showed that silencing the POm axons at the level of DLS slows down learning the task.

The authors show convincing evidence of projections from POm to DLS and that POm inputs to DLS code for whisking whatever the outcome of the task is. However, their results do not allow us to conclude if more neurons are recruited during the learning process or if the already activated fibres get activated more strongly. Last, because POm fibres in the DLS are also projecting to S1, silencing the POm fibres in the DLS could have affected inputs in S1 as well and therefore, the slowdown in acquiring the task is not necessarily specific to the POm to DLS pathway.

We thank the reviewer for these constructive comments. The points are addressed below.  

Strengths:

One of the main strengths of the paper is to go from slice electrophysiology to behaviour to get an in-depth characterization of one pathway. The authors did a comprehensive description of the POm projections to the DLS using transgenic mice to unambiguously identify the DLS neuronal population. They also used a carefully designed sensorimotor association task, and they exploited the results in depth.

It is a very nice effort to have measured the activity of the axons in the DLS not only after the mice have learned the task but throughout the learning process. It shows the progressive increase of activity of POm axons in the DLS, which could imply that there is a progressive strengthening of the pathway. The results show convincingly that POm axons in the DLS are not activated by the outcome of the task but by the whisker activity, and that this activity on average increases with learning.

Weaknesses:

One of the main targets of the striatum from thalamic input are the cholinergic neurons that weren't investigated here, is there information that could be provided?

This is true of the parafascicular (Pf) thalamic nucleus, which has been well studied in this context. However, there is much less known about the striatal projections of other thalamic nuclei, including POm, and their inputs to cholinergic neurons. Anatomical tracing evidence from Klug et al. (2018), which mapped brain-wide inputs to striatal cholinergic (ChAT) interneurons, suggests that Pf provides the majority of thalamic innervation of striatal ChAT neurons compared to other thalamic nuclei. Many other thalamic nuclei, including POm, showed very little of no labeling, suggesting weak innervation of ChAT interneurons. However, it is possible that these thalamic nuclei, including POm, do provide functional innervation of ChAT interneurons that is not sufficiently assessed by anatomical tracing. Understanding the innervation patterns of POm-striatal projections beyond the three cell types we have studied here would be an important area of further study.

It is interesting to know that the POm projects to all neuronal types in the DLS, but this information is not used further down the manuscript so the only take-home message of Figure 1 is that the axons that they image or silence in the DLS are indeed connected to DLS neurons and not just passing fibres. In this line, are these axons the same as the ones projecting to S1? If this is the case, why would we expect a different behaviour of the axon activity at the DLS level compared to S1?

Tracing of single POm axons by Ohno et al. (2012) indicated that POm axons form a branched collateral that innervates striatum, while the main axon continues in the rostral-dorsal direction to innervate cortex. We think it is reasonable, based on the morphology, that our optogenetic suppression experiment restricted the suppression of glutamate release to this branch and avoided the other branches of the axon that project to cortex. However, testing this would require monitoring S1 activity during the POm-striatal axon suppression, which we did not do in this study.

It is a very interesting question whether there could be different axon activity behavior in striatum versus S1. There is surprising evidence that POm synaptic terminals are different sizes in S1 and M1 and show different synaptic physiological properties depending on these cortical projection targets (Casas-Torremocha et al., 2022). Based on this, it is possible that POm-striatal synapses show distinct properties compared to cortex; however, this will need to be tested in future work.

The authors used endoscopy to measure the POm axons in the DLS activity, which makes it impossible to know if the progressive increase of POm response is due to an increase of activity from each individual neuron or if new neurons are progressively recruited in the process.

This is a good point. It would be necessary to perform chronic two-photon imaging of POm neurons (or chronic electrophysiological recordings) to determine whether the activity of individual neurons increased versus whether individual neuron activity levels remained similar but new neurons became active with learning. Even under baseline conditions, it is not known in detail what fraction of the population of POm neurons is active during sensory processing or behavior, highlighting how much is still to be discovered in this exciting area of neuroscience.

The picture presented in Figure 4 of the stimulation site is slightly concerning as there are hardly any fibres in neocortical layer 1 while there seems to be quite a lot of them in layer 4, suggesting that the animal here was injected in the VB. This is especially striking as the implantation and projection sites presented in Figures 1 and 2 are very clean and consistent with POm injection.

Although this image was selected to demonstrate the position of the POm injection site and optical fiber implant above striatal axons, the reviewer is correct that there appears to be mixed labeling of axons in L4 and L5a. In some cases, there was expression slightly outside the border of POm (see Fig. 1B, right), which might explain the cortical innervation pattern in this figure. While cortically bound VPM axons pass through the striatum, they do not form synaptic terminals until reaching the cortex (Hunnicutt et al., 2016). If, as may be the case, inhibitory opsins suppress release of neurotransmitter at synaptic terminals more effectively than action potential propagation in axons, it may be likely that optogenetic suppression of POm-striatal terminals is more effective than suppression of action potentials in off-target-labelled VPM axons of passage. Ideally, we could compare effects of suppression of POm-striatal synapses with POm-cortical synapses and VPM-cortical synapses, but this was outside the bandwidth of the present study.

Reviewer #2 (Public Review):

Summary:

Yonk and colleagues show that the posterior medial thalamus (POm), which is interconnected with sensory and motor systems, projects directly to major categories of neurons in the striatum, including direct and indirect pathway MSNs, and PV interneurons. Activity in POm-striatal neurons during a sensory-based learning task indicates a relationship between reward expectation and arousal. Inhibition of these neurons slows reaction to stimuli and overall learning. This circuit is positioned to feed salient event activation to the striatum to set the stage for effective learning and action selection.

Strengths:

The results are well presented and offer interesting insight into an understudied thalamostriatal circuit. In general, this work is important as part of a general need for an increased understanding of thalamostriatal circuits in complex learning and action selection processes, which have generally received less attention than corticostriatal systems.

Weaknesses:

There could be a stronger connection between the connectivity part of the data - showing that POm neurons context D1, D2, and PV neurons in the striatum but with some different properties - and the functional side of the project. One wonders whether the POm neurons projecting to these subtypes or striatal neurons have unique signaling properties related to learning, or if there is a uniform, bulk signal sent to the striatum. This is not a weakness per se, as it's reasonable for these questions to be answered in future papers.

We are very interested to understand the potentially distinct learning-related synaptic and circuit changes that potentially occur at the POm synapses with D1- and D2-SPNs and PV interneurons, and other striatal cell types. We agree that this would be an important topic for further investigation.

All the in vivo activity-related conclusions stem from data from just 5 mice, which is a relatively small sample set. Optogenetic groups are also on the small side.

We appreciate this point and agree that higher N can be important for observing robust effects. A factor of our experiments that helped reduce the number of animals used was the longitudinal design, with repeated measures in the same subjects. This allowed for the internal control of comparing learning effects in the same subject from naïve to expert stages and therefore increased robustness. Even with relatively small group sizes, results were statistically significant, suggesting that the use of more mice was unnecessary, which we considered consistent with best practice in the use of animals in research. We also note that our group sizes were consistent with other studies in the field.  

Reviewer #3 (Public Review):

Yonk and colleagues investigate the role of the thalamostriatal pathway. Specifically, they studied the interaction of the posterior thalamic nucleus (PO) and the dorsolateral striatum in the mouse. First, they characterize connectivity by recording DLS neurons in in-vitro slices and optogenetically activating PO terminals. PO is observed to establish depressing synapses onto D1 and D2 spiny neurons as well as PV neurons. Second, the image PO axons are imaged by fiber photometry in mice trained to discriminate textures. Initially, no trial-locked activity is observed, but as the mice learn PO develops responses timed to the audio cue that marks the start of the trial and precedes touch. PO does appear to encode the tactile stimulus type or outcome. Optogenetic suppression of PO terminals in striatum slow task acquisition. The authors conclude that PO provides a "behaviorally relevant arousal-related signal" and that this signal "primes" striatal circuitry for sensory processing.

A great strength of this paper is its timeliness. Thalamostriatal processing has received almost no attention in the past, and the field has become very interested in the possible functions of PO. Additionally, the experiments exploit multiple cutting-edge techniques.

There seem to be some technical/analytical weaknesses. The in vitro experiments appear to have some contamination of nearby thalamic nuclei by the virus delivering the opsin, which could change the interpretation. Some of the statistical analyses of these data also appear inappropriate. The correlative analysis of Pom activity in vivo, licking, and pupil could be more convincingly done.

The bigger weakness is conceptual - why should striatal circuitry need "priming" by the thalamus in order to process sensory stimuli? Why would such circuitry even be necessary? Why is a sensory signal from the cortex insufficient? Why should the animal more slowly learn the task? How does this fit with existing ideas of striatal plasticity? It is unclear from the experiments that the thalamostriatal pathway exists for priming sensory processing. In fact, the optogenetic suppression of the thalamostriatal pathway seems to speak against that idea.

We thank the reviewer for these constructive comments. The points are addressed below.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

Do POm neurons innervate CINs also? The connection between the PF thalamus and CINs is mentioned in a couple of places - one question is how unique are the input patterns for the POm versus adjacent sensorimotor thalamic regions, including the PF? This isn't a weakness per se but knowing the answer to that question would help in forming a more complete picture of how these different thalamostriatal circuits do or do not contribute uniquely to learning and action selection.

Anatomical tracing evidence from Klug et al. (2018), which mapped brain-wide inputs to striatal cholinergic (ChAT) interneurons, suggests that Pf provides the majority of thalamic innervation of striatal ChAT neurons compared to other thalamic nuclei. Many other thalamic nuclei, including POm, showed very little or no labeling, suggesting weak innervation of ChAT interneurons. However, it is possible that these thalamic nuclei, including POm, do provide functional innervation of ChAT interneurons that is not sufficiently assessed by anatomical tracing.

Another difference between Pf and other thalamic nuclei (likely including POm) comes from anatomical tracing evidence (Smith et al., 2014; PMID: 24523677) which indicates that Pf inputs form the majority of their synapses onto dendritic shafts of SPNs, while other thalamic nuclei form synapses onto dendritic spines. Understanding the innervation patterns of POm-striatal projections beyond the three cell types we have studied here, including ChAT neurons and subcellular localization, would be an important area of further study.

It would be useful to know to what extent these POm-striatum neurons are activated generally during movement, versus this discrimination task specifically.

We agree that distinguishing general movement-related activity from task-specific activity would be very useful. Earlier work (Petty et al., 2021) showed a close relationship between POm neuron activity, spontaneous (task-free) whisker movements, and pupil-indexed arousal in head-restrained mice. Oram et al. (2024; PMID: 39003286) recently recorded VPM and POm in freely moving mice during natural movements, finding that activity of both nuclei correlated with head and whisker movements. These studies indicate that POm is generally coactive with exploratory head and whisker movements.

During task performance, the situation may change with training and attentional effects. For example, Petty and Bruno (2024) (https://elifesciences.org/reviewed-preprints/97188) showed that POm activity correlates more closely with task demands than tactile or visual stimulus modality. Our data indicate that POm axonal signals are increased at trial start during anticipation of tactile stimulus delivery and through the sensory discrimination period, then decrease to baseline levels during licking and water reward collection (Fig. 3). Results of Petty and Bruno (2024) together with ours suggest that POm is particularly active during the context of behaviorally relevant task performance. Thus, we think it is likely that, while pupil dilation indexes general movement and arousal, POm activity is more specific to movement and arousal associated with task engagement and behavioral performance. We have strengthened this point in the Discussion.

Many of the data panels and text for legends/axes are quite small, and the stroke on line art is quite faint - overall figures could be improved from a readability standpoint.

We thank the reviewer for their careful attention to the figures. 

Reviewer #3 (Recommendations For The Authors):

Major

(1) Page 4, the Results regarding PSP and distance from injection site. The r-squared is the wrong thing to look at to test for a relationship. One should look at the p-value on the coefficient corresponding to the slope. The p-value is probably significant given the figures, in which case there may be a relationship contrary to what is stated. All the low r-squared value says is that, if there is a relationship, it does not explain a lot of the PSP variability.

We thank the reviewer for alerting us this oversight. We have included the p value (p = 0.0293) in the figure and legend, and indicated that the relationship is “small but significant”.

(2) Figure 1B suggests that the virus injections extend beyond POm and into other thalamic structures. Do any of the results change if the injections contaminating other nuclei are excluded from the analysis? I am not suggesting the authors change the figures/analyses. I am simply suggesting they double-check.

We selected for injections that were predominantly expressing in POm as determined by post-hoc histological analysis (see Fig. 1, right). As above, we think that axons of passage that do not form striatal synapses are less likely to be suppressed than axons with terminals; however, this would need to be determined in further experiments. Because the preponderance of expression is within POm, we think the results would be similar even with a stricter selection criterion. 

(3) The authors conclude that POm and licking are not correlated (bottom of page 6 pertaining to Figures 3A-F). The danger of these analyses is that they assume that GCaMP8 is a perfect linear reporter of POm spikes. The reliability of GCaMP8 has been quantified in some cell types, but not thalamic neurons, which have relatively higher firing rates.

The reviewer is correct that the relationship between GCaMP8 fluorescence changes and spiking has not been sufficiently characterized in thalamic neurons, and that this would be important to do.

What if the indicator is simply saturated late into the trial (after the average reaction time)? It would look like there is no response and one would conclude no correlation, but there could be a very strong correlation.

While saturation is worthy of concern, the signal dynamics here argue against this possibility. The reason is that the signal increased in the early part of the trial and decreased by the end. If saturation was an issue, this would have been apparent during the initial increase. When the signal decreased in amplitude at the end of the trial, this indicates that the signal is not saturated because it is returning from a point closer to its maximum (and is becoming less saturated).

Also, what happens between trials? Are the correlations the same, stronger, weaker? Ideally, the authors would analyze the data during and between trials.

Between trials the signal did not show further changes in baseline beyond what was displayed at the start and end of behavioral trials. There were no consistent increases or decreases in signals between trials, except perhaps during strong whisking bouts. This is anecdotal because we did not analyze between-trial data. However, it is interesting and important to note that signals increased dramatically in amplitude from naïve, early learning to expert behavioral performance (Fig. 3), highlighting that POm-axonal signals relate to behavioral engagement and performance rather than spontaneous behaviors.  

(4) Axonal activity could also appear more correlated with the pupil than licking because pupil dynamics are slow like the dynamics of calcium indicators. These kernels could artificially inflate the correlation. Ideally, the authors could consider these temporal effects. Perhaps they could deconvolve the temporal profiles of calcium and pupil before correlating? Or equivalently incorporate the profiles into their analysis?

We analyzed the lick probability histograms, which had a temporal profile similar to the calcium signals (Fig. 3D,E), ruling out concerns about effects of temporal effects on correlations. It is also worth noting that we observed changes in correlations between calcium signals and pupil with learning stage (Fig. 3I), even though the temporal profiles (signal dynamics) are not changing. Thus, temporal effects of the signals themselves are not the driver of correlations, but rather the changes in relative timing between calcium signals and pupil, as occur with learning.

(5) The authors conclude that PO provides a "behaviorally relevant arousal-related signal" and that this signal "primes" striatal circuitry for sensory processing. The data here support the first part. It is not clear that the data support the second part, largely because it is vague what "priming" of sensory processing or "a key role in the initial stages of action selection (p.9) even means here. Why would such circuitry even be necessary? Why is a sensory signal from the cortex insufficient? Why should the animal more slowly learn the task? How does this fit with existing ideas of striatal plasticity? Some conceptual proposals from the authors, even if speculative and not offered as a conclusion, would be helpful.

We appreciate these good points and have added further consideration and revision of the concept of priming and potential roles in an extensively revised Discussion section.

(6) The photometry shows that PO turns on about 2 seconds before the texture presentation. PO's activity seems locked to the auditory cue, not the texture (Figure 2). This means that the attempt to suppress the thalamostriatal pathway with JAWS (Figure 4) is rather late, isn't it? Some PO signals surely go through. This seems to contradict the idea of priming above. It would be good if the authors could factor this into their narrative. Perhaps labelling the time of the auditory cue in Figure 4C would also be helpful.

The start of texture presentation (movement of the texture panel toward the mouse) and auditory cue occur at the same time. To clarify this, we added a label “start tone” in Figure 4C and also in Figure 2C.

For optogenetic (JAWS) suppression, we intentionally chose a time window between start tone onset and texture presentation, because our photometry experiments showed that this was when the preponderance of the signal occurred. However, the reviewer is correct that our chosen optogenetic suppression (JAWS) onset occurs shortly after the photometry signal has already started, potentially leaving the early photometry signal un-suppressed. Our motivation for choosing a restricted time window surrounding the texture presentation time was 1) to minimize illumination and potential heating of brain tissue; 2) to target a time window that avoids the auditory cue but covers stimulus presentation. We did not want to extend the duration of the suppression to before the trial started, because this could produce task-non-specific effects, such as distraction or loss of attention before the start of the trial.

Even if some signal were getting through before suppression, we don’t think this contradicts the possibility of ‘priming’, because the process underlying priming would still be disrupted even if not totally suppressed. This would alter the temporal relationship between POm-striatal inputs and further corticostriatal inputs (from S1 and M1 cortex, for example). We have included further consideration of these points and possible relation to the priming concept in the Discussion.

Minor

(1) Page 5, "the sensitivity metric is artificially increased". What do you mean "artificially"? The mice are discriminating better. It is true that either a change in HR or FAR can cause the sensitivity metric to change, but there is nothing artificial or misleading about this.

We removed the word artificial and clarified our definition of behaviorally Expert in this context:

“Mice were considered Expert once they had reached ≥ 0.80 Hit Rate and ≤ 0.30 FA Rate for two consecutive sessions in lieu of a strict sensitivity (d’) threshold; we found this definition more intuitive because d’ is enhanced as Hit Rate and FA Rate approach their extremes (0 or 1)”

(2) Page 7, "Upon segmentation (Figure S4G-J)". Do you mean "segregation by trial outcome"?

Corrected.

(3) Page 9, "POm projections may have discrete target-specific functions, such that POm-striatal inputs may play a distinct role in sensorimotor behavior compared to POm-cortical inputs". Would POm-cortical inputs not also be sensorimotor? The somatosensory cortex contains a lot of corticostriatal cells. It also has various direct and indirect links to the motor cortex as well.

We have clarified the wording here to convey the possibility that POm signals could be received and processed differently by striatal versus cortical circuitry, and have moved this statement to later in the discussion for better elaboration.

(4) The Methods state that male and female mice were used. Why not say how many of each and whether or not there are any sex-specific differences?

We added the following information to the Methods:

The number of male and female mice were as follows, by experiment type: 6 male, 4 female (electrophysiology); 3 male, 2 female (fiber photometry); 4 male, 5 female (optogenetics). Data were not analyzed for sex differences.

Reviewer #1 (Public review):

Summary:

In this series of studies, Locantore et al. investigated the role of SST-expressing neurons in the entopeduncular nucleus (EPNSst+) in probabilistic switching tasks, a paradigm that requires continued learning to guide future actions. In prior work, this group had demonstrated EPNSst+ neurons co-release both glutamate and GABA and project to the lateral habenula (LHb), and LHb activity is also necessary for outcome evaluation necessary for performance in probabilistic decision-making tasks. Previous slice physiology works have shown that the balance of glutamate/GABA co-release is plastic, altering the net effect of EPN on downstream brain areas and neural circuit function. The authors used a combination of in vivo calcium monitoring with fiber photometry and computational modelling to demonstrate that EPNSst+ neural activity represents movement, choice direction and reward outcomes in their behavioral task. However, viral-genetic manipulations to synaptically silence these neurons or selectively eliminate glutamate release had no effect on behavioral performance in well-trained animals. The authors conclude that despite their representation of task variables, EPN Sst+ neuron synaptic output is dispensable for task performance.

Strengths and Weaknesses:

Overall, the manuscript is exceptionally scholarly, with a clear articulation of the scientific question and a discussion of the findings and their limitations. The analyses and interpretations are careful and rigorous. This review appreciates the thorough explanation of the behavioral modelling and GLM for deconvolving the photometry signal around behavioral events, and the transparency and thoroughness of the analyses in the supplemental figures. This extra care has the result of increasing the accessibility for non-experts, and bolsters confidence in the results. To bolster a reader's understanding of results, we suggest it would be interesting to see the same mouse represented across panels (i.e. Fig 1 F-J, Supp 1 F,K etc i.e via inclusion of faint hash lines connecting individual data points across variables. Additionally, Fig 3E demonstrates that eliminating the 'reward' and 'choice and reward' terms from the GLM significantly worsens model performance; to demonstrate the magnitude of this effect, it would be interesting to include a reconstruction of the photometry signal after holding out of both or one of these terms, alongside the 'original' and 'reconstructed' photometry traces in panel D. This would help give context for how the model performance degrades by exclusion of those key terms. Finally, the authors claimed calcium activity increased following ipsilateral movements. However, figure 3C clearly shows that both SXcontra and SXisi increase beta coefficients. Instead, the choice direction may be represented in these neurons, given that beta coefficients increase following CXipsi and before SEipsi, presumably when animals make executive decisions. Could the authors clarify their interpretation on this point? Also, it is not clear if there is a photometry response related to motor parameters (i.e. head direction or locomotion, licking), which could change the interpretation of the reward outcome if it is related to a motor response; could the authors show photometry signal from representative 'high licking' or 'low licking' reward trials, or from spontaneous periods of high. Vs low locomotor speeds (if the sessions are recorded) to otherwise clarify this point?

There are a few limitations with the design and timing of the synaptic manipulations that would improve the manuscript if discussed or clarified. The authors take care to validate the intersectional genetic strategies: Tetanus Toxin virus (which eliminates synaptic vesicle fusion) or CRISPR editing of Slc17a6, which prevents glutamate loading into synaptic vesicles. The magnitude of effect in the slice physiology results are striking. However, this relies on co-infection of a second AAV to express channelrhodopsin for the purposes of validation, and it is surely the case that there will not be 100% overlap between the proportion of cells infected. Alternative means of glutamate packaging (other VGluT isoforms, other transporters etc) could also compensate for the partial absence of VGluT2, which should be discussed. The authors do not perform a complimentary experiment to delete GABA release (i.e. via VGAT editing), which is understandable, given the absence of an effect with the pan-synaptic manipulation. A more significant concern is the timing of these manipulations as the authors acknowledge. The manipulations are all done in well-trained animals, who continue to perform during the length of viral expression. Moreover, after carefully showing that mice use different strategies on the 70/30 version vs the 90/10 version of the task, only performance on the 90/10 version is assessed after the manipulation. Together, the observation that EPNsst activity does not alter performance on a well learned, 90/10 switching task decreases the impact of the findings, as this population may play a larger role during task acquisition or under more dynamic task conditions. Additional experiments could be done to strengthen the current evidence, although the limitations is transparently discussed by the authors.

Finally, intersectional strategies target LHb-projecting neurons, although in the original characterization it is not entirely clear that the LHb is the only projection target of EPNsst neurons. A projection map would help clarify this point.

Overall, the authors used a pertinent experimental paradigm and common cell-specific approaches to address a major gap in the field, which is the functional role of glutamate/GABA co-release from the major basal ganglia output nucleus in action selection and evaluation. The study is carefully conducted, their analyses are thorough, and the data are often convincing and thought-provoking. However, the limitations of their synaptic manipulations with respect to the behavioral assays reduces generalizability and to some extent the impact of their findings.

Comments on the latest version:

Specifically, they have included more thorough analyses to address several concerns related to interpreting activity patterns of EPSst+ neurons. The authors clearly point out that calcium activity increased during ipsilateral movements, and the increase was statistically larger during the choice phase (Figure 2 supplement 1F-G), indicating that these neurons may represent movement and additional factors (e.g. executive decision-making). Correspondingly, we appreciate the thorough explanation of using a GLM model to determine which behavioural variables contribute to observed physiological signals and adding the example reconstructed signal with direction and reward variables omitted in Figure 3 supplements 1 and 2.

Although no new manipulation experiment is added to the manuscript, the authors respond to common critiques related to testing the behavioural effect after the manipulations in well-trained mice. The discussion related to technical limitations, possible compensatory mechanisms and alternative interpretations is thorough and overall satisfying. Based on the behaviour modeling results, the authors speculate that animals need to integrate more evidence from the past to guide choice in a more uncertain environment (70/30 version), instead of adopting a 'win-stay, lose-shift' strategy in the more deterministic 90/10 version. The authors expand the discussion, but the possibility that EPNSst+ neurons contribute to task performance in well-trained animals under uncertainty is not directly tested. Along with other alternative explanations discussed in the manuscript, we think the paper is valuable literature for future studies to understand the basal ganglia circuits in learning and decision-making.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this series of studies, Locantore et al. investigated the role of SST-expressing neurons in the entopeduncular nucleus (EPNSst+) in probabilistic switching tasks, a paradigm that requires continued learning to guide future actions. In prior work, this group had demonstrated EPNSst+ neurons co-release both glutamate and GABA and project to the lateral habenula (LHb), and LHb activity is also necessary for outcome evaluation necessary for performance in probabilistic decision-making tasks. Previous slice physiology works have shown that the balance of glutamate/GABA co-release is plastic, altering the net effect of EPN on downstream brain areas and neural circuit function. The authors used a combination of in vivo calcium monitoring with fiber photometry and computational modeling to demonstrate that EPNSst+ neural activity represents movement, choice direction, and reward outcomes in their behavioral task. However, viral-genetic manipulations to synaptically silence these neurons or selectively eliminate glutamate release had no effect on behavioral performance in well-trained animals. The authors conclude that despite their representation of task variables, EPN Sst+ neuron synaptic output is dispensable for task performance.

Strengths and Weaknesses:

Overall, the manuscript is exceptionally scholarly, with a clear articulation of the scientific question and a discussion of the findings and their limitations. The analyses and interpretations are careful and rigorous. This review appreciates the thorough explanation of the behavioral modeling and GLM for deconvolving the photometry signal around behavioral events, and the transparency and thoroughness of the analyses in the supplemental figures. This extra care has the result of increasing the accessibility for non-experts, and bolsters confidence in the results.

(1) To bolster a reader's understanding of results, we suggest it would be interesting to see the same mouse represented across panels (i.e. Figures 1 F-J, Supplementary Figures 1 F, K, etc i.e via the inclusion of faint hash lines connecting individual data points across variables.

Thank you for the suggestion. The same mouse is now represented in Fig 1 and Fig 1—Figure Supplement 1 as a darkened circle so it can be followed across different panels. Photometry from this mouse was used as sample date in Figure 2b and Figure 2—figure supplement 1a-b.

(2) Additionally, Figure 3E demonstrates that eliminating the 'reward' and 'choice and reward' terms from the GLM significantly worsens model performance; to demonstrate the magnitude of this effect, it would be interesting to include a reconstruction of the photometry signal after holding out of both or one of these terms, alongside the 'original' and 'reconstructed' photometry traces in panel D. This would help give context for how the model performance degrades by exclusion of those key terms.

We have now added analyses and reconstructed photometry signals from GLMs excluding important predictors in Figure 3—figure supplement 1 and 2. We use the model where both “Direction and reward” were omitted as predictors for the GLM and showed photometry reconstructions aligned to behavioral events used for the full model (Figure 3—figure supplement 1) and partial model (Figure 3—figure supplement 2) to compare model performance.  

(3) Finally, the authors claimed calcium activity increased following ipsilateral movements. However, Figure 3C clearly shows that both SXcontra and SXipsi increase beta coefficients. Instead, the choice direction may be represented in these neurons, given that beta coefficients increase following CXipsi and before SEipsi, presumably when animals make executive decisions. Could the authors clarify their interpretation on this point?

We observe that calcium activity increases during ipsilateral choices as the animal moves toward the ipsilateral side port (e.g. CX_ipsi to SE_ipsi; Fig 2C and Fig 3C). The animal also makes other ipsiversive movements not during the “choice” phase of a trial such as when it is returning to the center port following a contralateral choice (e.g. SX_Contra to CE; Fig 2—figure supplement 1F and Fig 3C). We also observe an increase in calcium activity during these ipsiversive movements (e.g. SX_Contra to CE), but they are not as large as those observed during the choice phase (Fig 2—figure supplement 1G). Therefore, during the choice phase of a trial, activity contains signals related to ipsilateral movement and additional factors (e.g. executive decision making).    

(4) Also, it is not clear if there is a photometry response related to motor parameters (i.e. head direction or locomotion, licking), which could change the interpretation of the reward outcome if it is related to a motor response; could the authors show photometry signal from representative 'high licking' or 'low licking' reward trials, or from spontaneous periods of high vs. low locomotor speeds (if the sessions are recorded) to otherwise clarify this point?

Unfortunately, neither licks nor locomotion were recorded during the behavioral sessions when photometry was recorded. In Figure 2—figure supplement 1a we now show individual trials sorted by trial duration (time elapsed between CE and SE) to illustrate the dynamics of the photometry signal on fast vs slow trials within a session.  

(5) There are a few limitations with the design and timing of the synaptic manipulations that would improve the manuscript if discussed or clarified. The authors take care to validate the intersectional genetic strategies: Tetanus Toxin virus (which eliminates synaptic vesicle fusion) or CRISPR editing of Slc17a6, which prevents glutamate loading into synaptic vesicles. The magnitude of effect in the slice physiology results is striking. However, this relies on the co-infection of a second AAV to express channelrhodopsin for the purposes of validation, and it is surely the case that there will not be 100% overlap between the proportion of cells infected.

For the Tet-tox experiments in Figure 4 we estimate approximately 70±15% of EP^Sst+ neurons expressed Tet-tox based on our histological counts and published stereological counts in EP (Miyamoto and Fukuda, 2015). It is true that channelrhodopsin expression will not overlap 100% with cells infected by the other virus, indeed our in vitro synaptic physiology shows small residual postsynaptic currents following optogenetic stimulation either from incomplete blockade of synaptic release or neurons that expressed channelrhodopsin but not Tettx (Figure 4—figure supplement 1J-K). The same is shown for CRISPR mediated deletion of Slc17a6 (Fig 5 – Fig supplement 1J-K).  

(6) Alternative means of glutamate packaging (other VGluT isoforms, other transporters, etc) could also compensate for the partial absence of VGluT2, which should be discussed.

While single cell sequencing (Wallace et al, 2017) has shown EP^Sst+ neurons do not express Slc17a7/8 (vGlut1 or vGlut3) it is possible that these genes could be upregulated following CRISPR mediated deletion of Slc17a6, however we do not see evidence of this with our in vitro synaptic physiology (EPSCs are significant suppressed, Figure 5 – Fig supplement 1J-K) and therefore can conclude it is highly unlikely to occur to a significant degree in our experiments. This is now included in the Discussion.

(7) The authors do not perform a complimentary experiment to delete GABA release (i.e. via VGAT editing), which is understandable, given the absence of an effect with the pan-synaptic manipulation. A more significant concern is the timing of these manipulations as the authors acknowledge. The manipulations are all done in well-trained animals, who continue to perform during the length of viral expression. Moreover, after carefully showing that mice use different strategies on the 70/30 version vs the 90/10 version of the task, only performance on the 90/10 version is assessed after the manipulation. Together, the observation that EPNsst activity does not alter performance on a well-learned, 90/10 switching task decreases the impact of the findings, as this population may play a larger role during task acquisition or under more dynamic task conditions. Additional experiments could be done to strengthen the current evidence, although the limitation is transparently discussed by the authors.

As mentioned above, it is possible that a requirement for EP^Sst+ neurons could be revealed if the experiment was conducted with different parameters (either different reward probabilities, fluctuating reward probabilities within a session, or withholding additional training during viral expression). It is difficult to predict which version of the task, if any, would be most likely to reveal a requirement for EP^Sst+ neurons based on our results. We favor testing for EP^Sst+ function using a new behavioral paradigm that allows us to carefully examine task learning following EP manipulations in an independent study.

(8) Finally, intersectional strategies target LHb-projecting neurons, although in the original characterization, it is not entirely clear that the LHb is the only projection target of EPNsst neurons. A projection map would help clarify this point.

In a previous study we confirmed that EP^Sst+ neurons project exclusively to the LHb using cell-type specific rabies infection and examining all reported downstream regions for axon collaterals (Wallace et al 2017, Suppl. Fig 6F-G). When EP^Sst+ neurons were labeled we did not observe axon collaterals in known targets of EP such as ventro-antero lateral thalamus, red nucleus, parafasicular nucleus of the thalamus, or the pedunculopontine tegmental nucleus, only in the LHb. Additionally, using single cell tracing techniques, others have shown EP neurons that exclusively project to the LHb (Parent et al, 2001).

Overall, the authors used a pertinent experimental paradigm and common cell-specific approaches to address a major gap in the field, which is the functional role of glutamate/GABA co-release from the major basal ganglia output nucleus in action selection and evaluation. The study is carefully conducted, their analyses are thorough, and the data are often convincing and thought-provoking. However, the limitations of their synaptic manipulations with respect to the behavioral assays reduce generalizability and to some extent the impact of their findings.

Reviewer #2 (Public Review):

Summary:

This paper aimed to determine the role EP sst+ neurons play in a probabilistic switching task.

Strengths:

The in vivo recording of the EP sst+ neuron activity in the task is one of the strongest parts of this paper. Previous work had recorded from the EP-LHb population in rodents and primates in head-fixed configurations, the recordings of this population in a freely moving context is a valuable addition to these studies and has highlighted more clearly that these neurons respond both at the time of choice and outcome.

The use of a refined intersectional technique to record specifically the EP sst+ neurons is also an important strength of the paper. This is because previous work has shown that there are two genetically different types of glutamatergic EP neurons that project to the LHb. Previous work had not distinguished between these types in their recordings so the current results showing that the bidirectional value signaling is present in the EP sst+ population is valuable.

Weaknesses:

(1) One of the main weaknesses of the paper is to do with how the effect of the EP sst+ neurons on the behavior was assessed.

(a) All the manipulations (blocking synaptic release and blocking glutamatergic transmission) are chronic and more importantly the mice are given weeks of training after the manipulation before the behavioral effect is assessed. This means that as the authors point out in their discussion the mice will have time to adjust to the behavioral manipulation and compensate for the manipulations. The results do show that mice can adapt to these chronic manipulations and that the EP sst+ are not required to perform the task. What is unclear is whether the mice have compensated for the loss of EP sst+ neurons and whether they play a role in the task under normal conditions. Acute manipulations or chronic manipulations without additional training would be needed to assess this.

Unfortunately, when mice are given a three week break from behavioral training (the time required to allow for adequate viral expression) behavioral performance on the task (p(highport), p(switch), trial number, trial time, etc.) is significantly degraded. Animals do eventually recover to previous performance levels, but this takes place during a 4-5 day “relearning” period. Here we sought to examine if EP^Sst+ neurons are required for continued task performance and chose to continue to train the animals following viral injection to avoid the “relearning” period that occurs following an extended break from behavioral training which may have made it difficult to interpret changes in behavioral performance due to the viral manipulation vs relearning.  

Acute manipulations were not used because we planned to compare complete synaptic ablation (Tettx) and single neurotransmitter ablation (CRISPR Slc17a6) over similar time courses and we know of no acute manipulation that could achieve single neurotransmitter ablation. 

(b) Another weakness is that the effect of the manipulations was assessed in the 90/10 contingency version of the task. Under these contingencies, mice integrate past outcomes over fewer trials to determine their choice and animals act closer to a simple win-stay-lose switch strategy. Due to this, it is unclear if the EP sst+ neurons would play a role in the task when they must integrate over a larger number of conditions in the less deterministic 70/30 version of the task.

It is possible that a requirement for EP^Sst+ neurons could be revealed if the experiment was conducted with different parameters (either different reward probabilities, fluctuating reward probabilities within a session, or withholding additional training during viral expression). It is difficult to predict which version of the task, if any, would be most likely to reveal a requirement for EP^Sst+ neurons based on our results. We favor testing for EP^Sst+ function using a new behavioral paradigm that allows us to carefully examine task learning following EP manipulations in an independent study.

The authors show an intriguing result that the EP sst+ neurons are excited when mice make an ipsilateral movement in the task either toward or away from the center port. This is referred to as a choice response, but it could be a movement response or related to the predicted value of a specific action. Recordings while mice perform movement outside the task or well-controlled value manipulations within the session would be needed to really refine what these responses are related to.

If activity of EP^Sst+ neurons included a predicted value component, we would expect to see a change in activity during ipsilateral movements when the previous trial was rewarded vs unrewarded. This is examined in Fig 2—figure suppl. 2C, where we compare EP^Sst+ responses during ipsilateral trials when the previous trials were either rewarded (blue) or unrewarded (gray). We show that EP^Sst+ activity prior to side port entry (SE) is identical in these two trial types indicating that EP^Sst+ neurons do not show evidence of predicted value of an action in this context. Therefore, we conclude that increased EP^Sst+ activity during ipsilateral trials is primarily related to ipsilateral movement following CX (we call this the “choice” phase of the trial). We also show that other ipsiversive movements outside of the “choice” phase of a trial (such as the return to center port following a contralateral trial) show a smaller but significant increase in activity (Figure 2—figure supplement 1F-G). Therefore, whereas the activity observed during ipsilateral choice contains signals related to ipsilateral movement and additional factors, our data suggest that predicted value is not one of those factors. We will clarify this point and our definition of “choice” in the narrative.  

(2) The authors conclude that they do not see any evidence for bidirectional prediction errors. It is not possible to conclude this. First, they see a large response in the EP sst+ neurons to the omission of an expected reward. This is what would be expected of a negative reward prediction error. There are much more specific well-controlled tests for this that are commonplace in head-fixed and freely moving paradigms that could be tested to probe this. The authors do look at the effect of previous trials on the response and do not see strong consistent results, but this is not a strong formal test of what would be expected of a prediction error, either a positive or negative. The other way they assess this is by looking at the size of the responses in different recording sessions with different reward contingencies. They claim that the size of the reward expectation and prediction error should scale with the different reward probabilities. If all the reward probabilities were present in the same session this should be true as lots of others have shown for RPE. Because however this data was taken from different sessions it is not expected that the responses should scale, this is because reward prediction errors have been shown to adaptively scale to cover the range of values on offer (Tobler et al., Science 2005). A better test of positive prediction error would be to give a larger-than-expected reward on a subset of trials. Either way, there is already evidence that responses reflect a negative prediction error in their data and more specific tests would be needed to formally rule in or out prediction error coding especially as previous recordings have shown it is present in previous primate and rodent recordings.

We do not conclude that we see no evidence for RPE and the reviewer is correct in stating that a large increase in EP^Sst+ activity following omission of an expected reward would be expected of a negative reward prediction error. However, this observation alone is not strong enough evidence that EP^Sst+ neurons signal RPE. When we looked for additional evidence of RPE within our experiments we did not find consistent demonstrations of its existence in our data. When performing photometry measurements of dopamine release in the striatum, RPE signals are readily observed with a task identical to ours using trial history to as a modifier of reward prediction (Chantranupong, et al 2023). Of course, there could be a weaker more heterogeneous RPE signal in EP^Sst+ neurons that we cannot detect with our methods. As we state in the discussion, RPE signals may be present in a subset of individual neurons (as observed in Stephenson-Jones et al, 2016 and Hong and Hikosaka, 2008) which are below our detection threshold using fiber photometry. Additionally, Hong and Hikosaka, 2008 show that LHb-projecting GPi neurons show both positive and negative reward modulations which may obscure observation of RPE signals with photometry recordings that arise from population activity of genetically defined neurons.   

(3) There are a lot of variables in the GLM that occur extremely close in time such as the entry and exit of a port. If two variables occur closely in time and are always correlated it will be difficult if not impossible for a regression model to assign weights accurately to each event. This is not a large issue, but it is misleading to have regression kernels for port entry and exits unless the authors can show these are separable due to behavioral jitter or a lack of correlation under specific conditions, which does not seem to be the case.

It is true that two variables that are always correlated are redundant in a GLM. For example, center entry (CE) and center exit (CX) occur in quick succession in most trials and are highly correlated (Figure 1C). For this reason, when only one is removed as a predictor from the model but not the other there is a very small change in the MSE of the fit (Figure 3E, -CE or -CX). However, when both are removed model performance decreases further indicating that center-port nose-pokes do contribute to model performance (Figure 3E, -CE/CX). Due to the presence/absence of reward following side port entry there is substantial behavioral jitter (due to water consumption in rewarded trials) that the SE and SX are not always correlated, therefore the model performs worse when either are omitted alone, but even worse still when both SE/SX are omitted together (Figure 3E, -SE/SX). We will update Figure 3 and the narrative to make this more explicit.

Reviewer #3 (Public Review):

Summary:

The authors find that Sst-EPN neurons, which project to the lateral habenula, encode information about response directionality (left vs right) and outcome (rewarded vs unrewarded). Surprisingly, impairment of vesicular signaling in these neurons onto their LHb targets did not impair probabilistic choice behavior.

Strengths:

Strengths of the current work include extremely detailed and thorough analysis of data at all levels, not only of the physiological data but also an uncommonly thorough analysis of behavioral response patterns.

Weaknesses:

Overall, I saw very few weaknesses, with only two issues, both of which should be possible to address without new experiments:

(1) The authors note that the neural response difference between rewarded and unrewarded trials is not an RPE, as it is not affected by reward probability. However, the authors also show the neural difference is partly driven by the rapid motoric withdrawal from the port. Since there is also a response component that remains different apart from this motoric difference (Figure 2, Supplementary Figure 1E), it seems this is what needs to be analyzed with respect to reward probability, to truly determine whether there is no RPE component. Was this done?

We thank the reviewer for this comment, we believe this is particularly important for unrewarded trials as SE and SX occur in rapid succession. In Figure 2—figure supplement 2A-B we now show the photometry signal from Rewarded and Unrewarded ipsilateral trials aligned to SX for different reward probabilities. We quantify the signals for different reward probabilities during a 500ms window immediately prior to SX but find no differences between groups.  

(2) The current study reaches very different conclusions than a 2016 study by Stephenson-Jones and colleagues despite using a similar behavioral task to study the same Sst-EPN-LHb circuit. This is potentially very interesting, and the new findings likely shed important light on how this circuit really works. Hence, I would have liked to hear more of the authors' thoughts about possible explanations of the differences. I acknowledge that a full answer might not be possible, but in-depth elaboration would help the reader put the current findings in the context of the earlier work, and give a better sense of what work still needs to be done in the future to fully understand this circuit.

For example, the authors suggest that the Sst-EPN-LHb circuit might be involved in initial learning, but play less of a role in well-trained animals, thereby explaining the lack of observed behavioral effect. However, it is my understanding that the probabilistic switching task forces animals to continually update learned contingencies, rendering this explanation somewhat less persuasive, at least not without further elaboration (e.g. maybe the authors think it plays a role before the animals learn to switch?).

Also, as I understand it, the 2016 study used manipulations that likely impaired phasic activity patterns, e.g. precisely timed optogenetic activation/inhibition, and/or deletion of GABA/glutamate receptors. In contrast, the current study's manipulations - blockade of vesicle release using tetanus toxin or deletion of VGlut2, would likely have blocked both phasic and tonic activity patterns. Do the authors think this factor, or any others they are aware of, could be relevant?

We have added further discussion of the Stephenson-Jones, et al 2016 study as well as the Lazaridis, et al 2019 study which shows no effect of phasic stimulation of EP when specifically manipulating EP^Sst+ (vGat+/vGlut2+) neurons rather than vGlut2+ neurons as in the Stephenson-Jones study.  

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

In some places, there seems to be a mismatch between referenced figures and texts. For example:

(1) The authors described that 'This increase in activity was seen for all three reward probabilities tested (90/10, 80/20, and 70/30) and occurred while the animal was engaged in ipsiversive movements as similar increases were observed following side exit (SX) on contralateral trials as the animal was moving from the contralateral side port back to the center port (Figure 2-Figure Supplement 1c)', but supplement 1c is not about calcium dynamics around the SX event. I presume they mean Figure 2-Figure Supplement 1d.

Yes, this will be corrected in the revised manuscript.

(2) The authors explained that increased EPSst+ neuronal activity following an unrewarded outcome was partially due to the rapid withdrawal of the animal's snout following an unrewarded outcome however, differences in rewarded and unrewarded trials were still distinguishable when signals were aligned to side port exit indicating that these increases in EPSst+ neuronal activity on unrewarded trials were a combination of outcome evaluation (unrewarded) and side port withdrawal occurring in quick succession (SX, Figure 2 - Figure Supplement 1d). I presume that they mean Figure 2 - Figure Supplement 1e.

Yes, this will be corrected in the revised manuscript.

Minor suggestions related to specific figure presentation are below:

Figure 2 and supplement figures:

(1) Figure 2B: the authors may consider presenting outcome-related signals recorded from all trials, including both ipsilateral and contralateral events, and align signals to SE when reward consumption presumably begins, rather than aligning to CE.

We have added sample recordings from ipsilateral and contralateral trials and sorted them by trial duration to allow for clearer presentation of activity following CE and SE (Figure 2—figure supplement 1a-b).

(2) The authors described that 'This increase in activity was seen for all three reward probabilities tested (90/10, 80/20, and 70/30) and occurred while the animal was engaged in ipsiversive movements as similar increases were observed following side exit (SX) on contralateral trials as the animal was moving from the contralateral side port back to the center port (Figure 2-Figure Supplement 1c)', but supplement 1c is not about calcium dynamics around the SX event. I presume they mean Figure 2-Figure Supplement 1d.

Yes, this will be corrected in the revised manuscript.

(3) The authors explained that increased EPSst+ neuronal activity following an unrewarded outcome was partially due to the rapid withdrawal of the animal's snout following an unrewarded outcome however, differences in rewarded and unrewarded trials were still distinguishable when signals were aligned to side port exit indicating that these increases in EPSst+ neuronal activity on unrewarded trials were a combination of outcome evaluation (unrewarded) and side port withdrawal occurring in quick succession (SX, Figure 2 -Figure Supplement 1d). I presume that they mean Figure 2 -Figure Supplement 1e.

Yes, this will be corrected in the revised manuscript.

Figure 3 and supplement figures:

(1) Figure 3C-F: it is hard to compare the amplitude of calcium signals between different behaviour events without a uniform y-axis.

The scale for the y-axis on Figure 3C-D is uniform for all panels. Figure 3E is also uniform for all boxplots. The reviewer may be referring to Figure 2C-F, but the y-axis for all of the photometry data is uniform for all panels and the horizontal line represents zero. The y-axis for the quantification on the right of each panel is scaled to the max/min for each comparison.

(2) Figure 3E is difficult to follow. The authors explained that the 'SE' variable is generated by collapsing the ipsilateral and contralateral port entries, and hence the variable has no choice of direction information. I assumed that the 'SX', 'CE', and 'CX' variables are generated similarly. It is not clear if this is the case for the 'side', 'centre' and 'choice' variables. The authors explained that 'omitting center port entry/exit together or individually also resulted in decreased GLM performance but to a smaller degree than the omission of choice direction (Figure 3e, "-Center")'. My understanding is that they created the Centre variable by collapsing ipsilateral and contralateral centre port entry/exit together. The Centre variable should have no choice of direction information. How is the Center variable generated differently from omitting centre port entry/exit together? I would ask the authors to explain the model and different variables a bit more thoroughly in the text.

We apologize for the confusion. All ten variables used to train the full GLM are listed in Fig. 3C. In Figure 3E variable(s) were omitted to test how they contributed to GLM performance (data labeled “None” is the full model with all variables). Omitted variables are now defined as follows: -Rew = Rew+Unrew removed, -Direction = Ipsi/Contra designation removed and collapsed into CE, CX, SE, SX, -Direction & Rew = Ipsi/Contra info removed from all variables + Rew/Unrew removed, -CE/CX = Ipsi/Contra CE and CX removed, -CE = Ipsi/contra CE removed, -CX = Ipsi/contra CX removed, -SE/SX = Ipsi/Contra SE and SX removed, -SE = Ipsi/contra SE removed, -SX = Ipsi/contra SX removed. This clarification has also been added to the Generalized Linear Model section of Materials and Methods.

Figure 5 and supplement figures:

There are no representative and summary figures show the specificity and efficiency of oChief-tdTomato or Tetx-GFP expression. Body weight changes following virus injection are not well described.

A representative image of Tettx GFP expression are shown in Fig. 4A and percent of infected EP^Sst+ neurons is described in the text (70±15.1% (mean±SD), 1070±230 neurons/animal, n=6 mice). Most oChief-tdTom animals were used for post-hoc electrophysiology experiments and careful quantification of viral expression was not possible. However, Slc17a6 deletion was confirmed in these animals (Fig. 5 – Fig supplement 1J-K) to confirm the manipulation was effective in the experimental group. A representative image of oChief-tdTom expression is shown in Fig. 5A.

We now mention the body weight changes observed following Tettx injection in the narrative.

Reviewer #2 (Recommendations For The Authors):

(1) In the RFLR section you state that "this variable decays...", a variable can't decay only the value of a variable can change. Also, it is not mentioned what variable is being discussed. There are lots of variables in the model so this should be made clear.

We now state, “This variable (β) changes over trials and is updated with new evidence from each new trial’s choice and outcome with an additional bias towards or away from its most recent choice (Figure 1-figure supplement 2A-C).”

(2) I couldn't find in the results section, or the methods section the details for the Tet tx experiments, were mice trained and tested on 90/10 only? Were they trained while the virus was expressing etc? This should be added.

In the methods section we state, ”For experiments where we manipulated synaptic release in EP^Sst+ neurons (Figures 4-5) we trained mice (reward probabilities 90/10, no transparent barrier present) to the following criteria for the 5 days prior to virus injection: 1) p(highport) per session was greater than or equal to 0.80 with a variance less than 0.003, 2) p(switch) per session was less than or equal to 0.15 with a variance less than 0.001, 3) the p(left port) was between 0.45-0.55 with a variance less than 0.005, and 4) the animal performed at least 200 trials in a session. The mean and variance for these measurements was calculated across the five session immediately preceding surgery. The criterion were determined by comparing performance profiles in separate animals and chosen based on when animals first showed stable and plateaued behavioral performance. Following surgery, mice were allowed to recover for 3 days and then continued to train for 3 weeks during viral expression. Data collected during the 5 day pre-surgery period was then compared to data collected for 10 sessions following the 3 weeks allotted for viral expression (i.e. days 22-31 post-surgery).”

Reviewer #3 (Recommendations For The Authors):

(1) The kernel in Figure 3C shows an activation prior to CE on "contra" trials that is not apparent in Figure 2C which shows no activation prior to CE on either contra or ipsi trials. Given that movement directionality prior to CE is dictated by the choice on the PREVIOUS trial, is the "contra" condition in 3C actually based on the previous trial? If so, this should be clarified.

On most “contra” trials the animal is making an ipsiversive movement just prior to CE as it returns to the center from the contralateral side-port (as most trials are no “switch” trials). Therefore, an increase in activity is expected and shown most clearly following SX for contralateral trials in Fig 2 –Fig suppl 1F. A significant increase in activity prior to CE on contra trials compared to ipsi trials can also be seen in Fig 2C, its just not as large a change as the increase observed following CE for ipsi. trials. The comparison between activity observed during the two types of ipsiversive movements is now shown directly in Figure 2—figure supplement 1G.

(2) Paragraph 7 of the discussion uses a phrase "by-in-large", which probably should be "by and large".

Thank you for the correction.

Editor's note:

Should you choose to revise your manuscript, if you have not already done so, please include full statistical reporting including exact p-values wherever possible alongside the summary statistics (test statistic and df) and 95% confidence intervals. These should be reported for all key questions and not only when the p-value is less than 0.05 in the main manuscript.

Readers would also benefit from coding individual data points by sex and noting N/sex.

Sex breakdown has been added to figure legends for each experiment, full statistical reporting is now also include in the figure legends.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The manuscript by Bell et. al. describes an analysis of the effects of removing one of two mutually exclusive splice exons at two distinct sites in the Drosophila CaV2 calcium channel Cacophony (Cac). The authors perform imaging and electrophysiology, along with some behavioral analysis of larval locomotion, to determine whether these alternatively spliced variants have the potential to diversify Cac function in presynaptic output at larval neuromuscular junctions. The author provided valuable insights into how alternative splicing at two sites in the calcium channel alters its function.

Strengths:

The authors find that both of the second alternatively spliced exons (I-IIA and I-IIB) that are found in the intracellular loop between the 1st and second set of transmembrane domains can support Cac function. However, loss of the I-IIB isoform (predicted to alter potential beta subunit interactions) results in 50% fewer channels at active zones and a decrease in neurotransmitter release and the ability to support presynaptic homeostatic potentiation. Overall, the study provides new insights into Cac diversity at two alternatively spliced sites within the protein, adding to our understanding of how regulation of presynaptic calcium channel function can be regulated by splicing.

Weaknesses:

The authors find that one splice isoform (IS4B) in the first S4 voltage sensor is essential for the protein's function in promoting neurotransmitter release, while the other isoform (IS4A) is dispensable. The authors conclude that IS4B is required to localize Cac channels to active zones. However, I find it more likely that IS4B is required for channel stability and leads to the protein being degraded, rather than any effect on active zone localization. More analysis would be required to establish that as the mechanism for the unique requirement for IS4B.

(1) We thank the reviewer for this important point. In fact, all three reviewers raised the same question, and the reviewing editor pointed out that caution or additional experiments were required to distinguish between IS4 splicing being important for cac channel localization versus channel stability/degradation. We provide multiple sets of experiments as well as text and figure revisions to strengthen our claim that the IS4B exon is required for cacophony channels to enter motoneuron presynaptic boutons and localize to active zones.

a. If IS4B was indeed required for cac channel stability (and not for localization to active zones) IS4A channels should be instable wherever they are. This is not the case because we have recorded somatodendritic cacophony currents from IS4A expressing adult motoneurons that were devoid of cac channels with the IS4B exon. Therefore, IS4A cac channels are not instable but underlie somatodendritic voltage dependent calcium currents in these motoneurons. These new data are now shown in the revised figure 3C and referred to in the text on page 7, line 42 to page 8 line 9.

b. Similarly, if IS4B was required for channel stability, it should not be present anywhere in the nervous system. We tested this by immunohistochemistry for GFP tagged IS4A channels in the larval CNS. Although IS4A channels are sparsely expressed, which is consistent with low expression levels seen in the Western blots (Fig. 1E), there are always defined and reproducible patterns of IS4A label in the larval brain lobes as well as in the anterior part of the VNC. This again shows that the absence of IS4A from presynaptic active zones is not caused by channel instability, because the channel is expressed in other parts of the nervous system. These data are shown in the new supplementary figure 1 and referred to in the text on page 15, lines 3 to 8.

c. As suggested in a similar context by reviewers 1 and 2, we now show enlargements of the presence of IS4B channels in presynaptic active zones as well as enlargements of the absence of IS4A channels in presynaptic active zones in the revised figures 2A-C and 3A. In these images, no IS4A label is detectable in active zones or anywhere else throughout the axon terminals, thus indicating that IS4B is required for expressing cac channels in the axon terminal boutons and localizing it to active zones. Text and figure legends have been adjusted accordingly.

d. Related to this, reviewer 1 also recommended to quantify the IS4A and ISB4 channel intensity and co-localization with the active zone marker brp (recommendation for authors). After following the reviewers’ suggestion to adjust the background values in IS4A and IS4B immunolabels to identical (revised Figs. 2A-C), it becomes obvious that IS4A channel are not detectable above background in presynaptic terminals or active zones, thus intensity is close to zero. We still calculated the Pearsons co-localization coefficient for both IS4 variants with the active zone marker brp. For IS4B channels the Pearson’s correlation coefficient is control like, just above 0.6, whereas for IS4A channels we do not find colocalization with brp (Pearson’s below 0.25). These new analyses are now shown in the revised figure 2D and referred to on page 6, lines 33 to 38.

e. Consistent with our finding that IS4B is required for cac channel localization to presynaptic active zones, upon removal of IS4B we find no evoked synaptic transmission (Fig. 2 in initial submission, now Fig. 3B).

Together these data are in line with a unique requirement of IS4B at presynaptic active zones (not excluding additional functions of IS4B), whereas IS4A containing cac isoforms are not found in presynaptic active zones and mediate different functions.

Reviewer #2 (Public Review):

This study by Bell et al. focuses on understanding the roles of two alternatively spliced exons in the single Drosophila Cav2 gene cac. The authors generate a series of cac alleles in which one or the other mutually exclusive exons are deleted to determine the functional consequences at the neuromuscular junction. They find alternative splicing at one exon encoding part of the voltage sensor impacts the activation voltage as well as localization to the active zone. In contrast, splicing at the second exon pair does not impact Cav2 channel localization, but it appears to determine the abundance of the channel at active zones.

Together, the authors propose that alternative splicing at the Cac locus enables diversity in Cav2 function generated through isoform diversity generated at the single Cav2 alpha subunit gene encoded in Drosophila.

Overall this is an excellent, rigorously validated study that defines unanticipated functions for alternative splicing in Cav2 channels. The authors have generated an important toolkit of mutually exclusive Cac splice isoforms that will be of broad utility for the field, and show convincing evidence for distinct consequences of alternative splicing of this single Cav2 channel at synapses. Importantly, the authors use electrophysiology and quantitative live sptPALM imaging to determine the impacts of Cac alternative splicing on synaptic function. There are some outstanding questions regarding the mechanisms underlying the changes in Cac localization and function, and some additional suggestions are listed below for the authors to consider in strengthening this study. Nonetheless, this is a compelling investigation of alternative splicing in Cav2 channels that should be of interest to many researchers.

(2) We believe that the additional data on cac IS4A isoform localization and function as detailed above (response to public review 1) has strengthened the manuscript and answered some of the remaining questions the reviewer refers to. We are also grateful for the specific additional reviewer suggestions which we have addressed point-by-point and refer to below (section recommendations for authors).

Reviewer #3 (Public Review):

Summary:

Bell and colleagues studied how different splice isoforms of voltage-gated CaV2 calcium channels affect channel expression, localization, function, synaptic transmission, and locomotor behavior at the larval Drosophila neuromuscular junction. They reveal that one mutually exclusive exon located in the fourth transmembrane domain encoding the voltage sensor is essential for calcium channel expression, function, active zone localization, and synaptic transmission. Furthermore, a second mutually exclusive exon residing in an intracellular loop containing the binding sites for Caβ and G-protein βγ subunits promotes the expression and synaptic localization of around ~50% of CaV2 channels, thereby contributing to ~50% of synaptic transmission. This isoform enhances release probability, as evident from increased short-term depression, is vital for homeostatic potentiation of neurotransmitter release induced by glutamate receptor impairment, and promotes locomotion. The roles of the two other tested isoforms remain less clear.

Strengths:

The study is based on solid data that was obtained with a diverse set of approaches. Moreover, it generated valuable transgenic flies that will facilitate future research on the role of calcium channel splice isoforms in neural function.

Weaknesses:

(1) Based on the data shown in Figures 2A-C, and 2H, it is difficult to judge the localization of the cac isoforms. Could they analyze cac localization with regard to Brp localization (similar to Figure 3; the term "co-localization" should be avoided for confocal data), as well as cac and Brp fluorescence intensity in the different genotypes for the experiments shown in Figure 2 and 3 (Brp intensity appears lower in the dI-IIA example shown in Figure 3G)? Furthermore, heterozygous dIS4B imaging data (Figure 2C) should be quantified and compared to heterozygous cacsfGFP/+.

According to the reviewer’s suggestion, we have quantified cac localization relative to brp localization by computing the Pearson’s correlation coefficient for controls and IS4A as well as IS4B animals. These new data are shown in the revised Fig. 2D and referred to on page 6, lines 33-38. Furthermore, we now confirm control-like Pearson’s correlation coefficients for all exon out variants except ΔIS4B and show Pearson’s correlation coefficients for all genotypes side-by-side in the revised Fig. 4D (legend has been adjusted accordingly). In addition, in response to the recommendations to authors, we now provide selective enlargements for the co-labeling of Brp and each exon out variant in the revised figures 2-4. We have also adjusted the background in Fig. 2C (ΔIS4B) to match that in Figs. 2A and B (control and ΔIS4A). This allows a fair comparison of cac intensities following excision of IS4B versus excision of IS4A and control (see also Fig 3). Together, this demonstrates the absence of IS4A label in presynaptic active zones much clearer. As suggested, we have also quantified brp puncta intensity on m6/7 across homozygous exon excision mutants and found no differences (this is now stated for IS4A/IS4B in the results text on page 6, lines 37/38 and for I-IIA/I-IIB on page 8, lines 42-44.). We did not quantify the intensity of cacophony puncta upon excision of IS4B because the label revealed no significant difference from background (which can be seen much better in the images now), but the brp intensities remained control-like even upon excision of IS4B.

(2) They conclude that I-II splicing is not required for cac localization (p. 13). However, cac channel number is reduced in dI-IIB. Could the channels be mis-localized (e.g., in the soma/axon)? What is their definition of localization? Could cac be also mis-localized in dIS4B? Furthermore, the Western Blots indicate a prominent decrease in cac levels in dIS4B/+ and dI-IIB (Figure 1D). How do the decreased protein levels seen in both genotypes fit to a "localization" defect? Could decreased cac expression levels explain the phenotypes alone?

We have now precisely defined what we mean by cac localization, namely the selective label of cac channels in presynaptic active zones that are defined as brp puncta, but no cac label elsewhere in the presynaptic bouton (page 6, lines 18 to 20). On the level of CLSM microscopy this corresponds to overlapping cac puncta and brp puncta, but no cac label elsewhere in the bouton. Based on the additional analysis and data sets outlined in our response 1 (see above) we conclude that excision of IS4B does not cause channel mislocalization because we find reproducible expression patterns elsewhere in the nervous system as well as somatodendritic cac current in ΔIS4B (for detail see above). Therefore, the isoforms containing the mutually exclusive IS4A exon are expressed and mediate other functions, but cannot substitute IS4B containing isoforms at the presynaptic AZ. In fact, our Western blots are in line with reduced cac expression if all isoforms that mediate evoked release are missing, again indicating that the presynapse specific cac isoforms cannot be replaced by other cac isoforms. This is also in line with the sparse expression of IS4A throughout the CNS as seen in the new supplementary figure 1 (for detail see above).

(3) Cac-IS4B is required for Cav2 expression, active zone localization, and synaptic transmission. Similarly, loss of cac-I-IIB reduces calcium channel expression and number. Hence, the major phenotype of the tested splice isoforms is the loss of/a reduction in Cav2 channel number. What is the physiological role of these isoforms? Is the idea that channel numbers can be regulated by splicing? Is there any data from other systems relating channel number regulation to splicing (vs. transcription or post-transcriptional regulation)?

Our data are not consistent with the idea that splicing regulates channel numbers. Rather, splicing can be used to generate channels with specific properties that match the demand at the site of expression. For the IS4 exon pair we find differences in activation voltage between IS4A and IS4B channels (revised Fig. 3C), with IS4B being required for sustained HVA current. IS4A does not localize to presynaptic active zones at the NMJ and is only sparsely expressed elsewhere in the NS (new supplementary Fig. 1). By contrast, IS4B is abundantly expressed in many neuropils. Therefore, taking out IS4B takes out the more abundant IS4 isoform. This is consistent with different expression levels for IS4 isoforms that have different functions, but we do not find evidence for splicing regulating expression levels per se.

Similarly, the I-II mutually exclusive exon pair differs markedly in the presence or absence of G-protein βγ binding sites that play a role in acute channel regulation as well the conservation of the sequence for β-subunit binding (see page 5, lines 9-17). Channel number reduction in active zones occurs specifically if expression of the cac channels with the G_βγ-binding site as well as the more conserved β-subunit binding is prohibited by excision of the I-IIB exon (see Fig. 5F). Vice versa, excision of I-IIA does not result in reduced channel numbers. This scenario is consistent with the hypothesis that conserved β-subunit binding affects channel number in the active zone (see page 17, lines 3 to 6 and lines 33-36), but we have no evidence that I-II splicing per se affects channel number.

(4) Although not supported by statistics, and as appreciated by the authors (p. 14), there is a slight increase in PSC amplitude in dIS4A mutants (Figure 2). Similarly, PSC amplitudes appear slightly larger (Figure 3J), and cac fluorescence intensity is slightly higher (Figure 3H) in dI-IIA mutants. Furthermore, cac intensity and PSC amplitude distributions appear larger in dI-IIA mutants (Figures 3H, J), suggesting a correlation between cac levels and release. Can they exclude that IS4A and/or I-IIA negatively regulate release? I suggest increasing the sample size for Canton S to assess whether dIS4A mutant PSCs differ from controls (Figure 2E). Experiments at lower extracellular calcium may help reveal potential increases in PSC amplitude in the two genotypes (but are not required). A potential increase in PSC amplitude in either isoform would be very interesting because it would suggest that cac splicing could negatively regulate release.

There are several possibilities to explain this, but as none of the effects is statistically significant, we prefer to not investigate this in further depth. However, given that we cannot find IS4A in presynaptic active zones (revised figures 2C and 3A plus the new enlargements 2Ci and 3Ai, revised text page 6, lines 22 to 24 and 29 to 31, and page 7, second paragraph, same as public response 1D) IS4A channels cannot have a direct negative effect on release probability. Nonetheless, given that IS4A containing cac isoforms mediate functions in other neuronal compartments (see revised Fig. 3C) it may regulate release indirectly by affecting e.g. action potential shape. Moreover, in response to the more detailed suggestions to authors we provide new data that give additional insight.

(5) They provide compelling evidence that IS4A is required for the amplitude of somatic sustained HVA calcium currents. However, the evidence for effects on biophysical properties and activation voltage (p. 13) is less convincing. Is the phenotype confined to the sustained phase, or are other aspects of the current also affected (Figure 2J)? Could they also show the quantification of further parameters, such as CaV2 peak current density, charge density, as well as inactivation kinetics for the two genotypes? I also suggest plotting peaknormalized HVA current density and conductance (G/Gmax) as a function of Vm. Could a decrease in current density due to decreased channel expression be the only phenotype? How would changes in the sustained phase translate into altered synaptic transmission in response to AP stimulation?

Most importantly, sustained HVA current is abolished upon excision of IS4B (not IS4A, we think the reviewer accidentally mixed up the genotype) and presynaptic active zones at the NMJ contain only cac isoforms with the IS4B exon. This indicates that the cac isoforms that mediate evoked release encode HVA channels. The somatodendritic currents shown in the revised figure 3C (previously 2J) that remain upon excision of IS4B are mediated by IS4A containing cac isoforms. Please note that these never localize to the presynaptic active zone, and thus do not contribute to evoked release. Therefore, the interpretation is that specifically sustained HVA current encoded by IS4B cac isoforms is required for synaptic transmission. Reduced cac current density due to decreased channel expression is not the cause for impaired evoked release upon IS4B excision, but instead, the cause is the absence of any cac channels in active zones. IS4B-containing cac isoforms encode sustained HVA current, and we speculate that this might be a well suited current to minimize cacophony channel inactivation in the presynaptic active zone. Given that HVA current shows fast voltage dependent activation and fast inactivation upon repolarization, it is useful at large intraburst firing frequencies as observed during crawling (Kadas et al., 2017) without excessive cac inactivation (see page 15, Kadas, lines 16 to 20).

However, we agree with the reviewer that a deeper electrophysiological analysis of splice isoform specific cac currents will be instructive. We have now added traces of control and ΔIS4B from a holding potential of -90 mv (revised Fig. 3C, bottom traces and revised text on page 7, line 43 to page 8, lines 1 to 10), and these are also consistent with IS4B mediating sustained HVA cac current. However, further analysis of activation and inactivation voltages and kinetics suffers form space clamp issues in recordings from the somata of such complex neurons (DLM motoneurons of the adult fly contain roughly 6000 µm of dendrites with over 4000 branches, Ryglewski et al., 2017, Neuron 93(3):632-645). Therefore, we will analyze the currents in a heterologous expression system and present these data to the scientific community as a separate study at a later time point.

(6) Why was the STED data analysis confined to the same optical section, and not to max. intensity z-projections? How many and which optical sections were considered for each active zone? What were the criteria for choosing the optical sections? Was synapse orientation considered for the nearest neighbor Cac - Brp cluster distance analysis? How do the nearest-neighbor distances compare between "planar" and "side-view" Brp puncta?

Maximum intensity z-projections would be imprecise because they can artificially suggest close proximity of label that is close by in x and y but far away in z. Therefore, the analysis was executed in xy-direction of various planes of entire 3D image stacks. We considered active zones of different orientations (Figs. 5C, D) to account for all planes. In fact, we searched the entire z-stacks until we found active zones of all orientations within the same boutons, as shown in figures 5C1-C6. The same active zone orientations were analyzed for all exon-out mutants with cac localization in active zones. The distance between cac and brp did not change if viewed from the side or any other orientation. We now explain this in more clarity in the results text on page 9, lines 23/24.

(7) Cac clusters localize to the Brp center (e.g., Liu et al., 2011). They conclude that Cav2 localization within Brp is not affected in the cac variants (p. 8). However, their analysis is not informative regarding a potential offset between the central cac cluster and the Brp "ring". Did they/could they analyze cac localization with regard to Brp ring center localization of planar synapses, as well as Brp-ring dimensions?

In the top views (planar) we did not find any clear offset in cac orientation to brp between genotypes. In such planar synapses (top views, Fig. 5D, left row) we did not find any difference in Brp ring dimensions. We did not quantify brp ring dimensions rigorously, because this study focusses on cac splice isoform-specific localization and function. Possible effects of different cac isoforms on brp-ring dimensions or other aspects of scaffold structure are not central to our study, in particular given that brp puncta are clearly present even if cac is absent from the synapse (Fig. 3A), indicating that cac is not instructive for the formation of the brp scaffold.

(8) Given the accelerated PSC decay/ decreased half width in dI-IIA (Fig. 5Q), I recommend reporting PSC charge in Figure 3, and PPR charge in Figures 5A-D. The charge-based PPRs of dI-IIA mutants likely resemble WT more closely than the amplitude-based PPR. In addition, miniature PSC decay kinetics should be reported, as they may contribute to altered decay kinetics. How could faster cac inactivation kinetics in response to single AP stimulation result in a decreased PSC half-width? Is there any evidence for an effect of calcium current inactivation on PSC kinetics? On a similar note, is there any evidence that AP waveform changes accelerate PSC kinetics? PSC decay kinetics are mainly determined by GluR decay kinetics/desensitization. The arguments supporting the role of cac splice isoforms in PSC kinetics outlined in the discussion section are not convincing and should be revised.

We agree that reporting charge in figure 3 is informative and do so in the revised text. Since the result (no significant difference in the PSCs between between CS, cac^GFP, ^ΔI-IIA, and transheterozygous I-IIA/I-IIB, but significantly smaller values in ΔI-IIB) remained unchanged no matter whether charge or amplitude were analyzed, we decided to leave the figure as is and report the additional analysis in the text (page 8, lines 40 to 42). This way, both types of analysis are reported. Please note that EPSC amplitude is slightly but not significantly increased upon excision of I-IIA (Fig. 4J), whereas EPSC half amplitude width is significantly smaller (Fig. 5Q, now revised Fig 6R). Together, a tendency of increased EPSC amplitudes and smaller half amplitude width result in statistically insignificant changes in EPSC in ∆I-IIA (now discussed on page 15, lines 37 to 40). We also understand the reviewer’s concern attributing altered EPSC kinetics to presynaptic cac channel properties. We have toned down our interpretation in the discussion and list possible alterations in presynaptic AP shape or cac channel kinetics as alternative explanations (not conclusions; see revised discussion on page 15, line 40 to page 16, line 2). Moreover, we have quantified postsynaptic GluRIIA abundance to test whether altered PSC kinetics are caused by altered GluRIIA expression. In our opinion, the latter is more instructive than mini decay kinetic analysis because this depends strongly on the distance of the recording electrode to the actual site of transmission in these large muscle cells. Although we find no difference in GluRIIA expression levels we now clearly state that we cannot exclude other changes in GluR receptor fields, which of course, could also explain altered PSC kinetics. We have updated the discussion on page 16, lines 2/3 accordingly.

(9) Paired-pulse ratios (PPRs): On how many sweeps are the PPRs based? In which sequence were the intervals applied? Are PPR values based on the average of the second over the first PSC amplitudes of all sweeps, or on the PPRs of each sweep and then averaged? The latter calculation may result in spurious facilitation, and thus to the large PPRs seen in dI-IIB mutants (Kim & Alger, 2001; doi: 10.1523/JNEUROSCI.21-2409608.2001).

We agree that the PP protocol and analyses had to be described more precisely in the methods and have done so on page 23, lines 31 to 37 in the methods. Mean PPR values are based on the PPRs of each sweep and then averaged. We are aware of the study of Kim and Alger 2001 and have re-analyzed the PP data in both ways outlined by the reviewer. We get identical results with either analyses method. Spurious facilitation is thus not an issue in our data. We now explain this in the methods section along with the PPR protocol. The large spread seen in dI-IIB is indeed caused by reduced calcium influx into active zones with fewer channels, as anticipated by the reviewer (see next point).

(10) Could the dI-IIB phenotype be simply explained by a decrease in channel number/ release probability? To test this, I propose investigating PPRs and short-term dynamics during train stimulation at lower extracellular Ca2+ concentration in WT. The Ca2+ concentration could be titrated such that the first PSC amplitude is similar between WT and dI-IIB mutants. This experiment would test if the increased PPR/depression variability is a secondary consequence of a decrease in Ca2+ influx, or specific to the splice isoform.

In fact, the interpretation that decreased PSC amplitude upon I-IIB excision is caused mainly by reduced channel number is precisely our interpretation (see discussion page 14, last paragraph to page 15, first paragraph in the original submission, now page 16, second paragraph paragraph). In addition, we are grateful for the reviewer’s suggestion to triturate the external calcium such that the first PSC amplitude in matches in ∆I-IIB and control. This experiment tests whether altered short term plasticity is solely a function of altered channel number or whether additional causes, such as altered channel properties, also play into this. We triturated the first pulse amplitude in ∆I-IIB to match control and find that paired pulse ratio and the variance thereof are not different anymore. Therefore, the differences observed in identical external calcium can be fully explained by altered channel numbers. This additional dataset is shown in the revised figures 6D and E and referred to in the results section on page 10, lines 14 to 25 and the discussion on page16, lines 36 to 38.

(11) How were the depression kinetics analyzed? How many trains were used for each cell, and how do the tau values depend on the first PSC amplitude? Time constants in the range of a few (5-10) milliseconds are not informative for train stimulations with a frequency of 1 or 10 Hz (the unit is missing in Figure 5H). Also, the data shown in Figures 5E-K suggest slower time constants than 5-10 ms. Together, are the data indeed consistent with the idea that dIIIB does not only affect cac channel number, but also PPR/depression variability (p. 9)?

For each animal the amplitudes of all subsequent PSCs in each train were plotted over time and fitted with a single exponential. For depression at 1 and 10 Hz, we used one train per animal, and 5-6 animals per genotype (as reflected in the data points in Figs. 6I, M). This is now explained in more detail in the revised methods section (page 23, lines 39 to 41). The tau values are not affected by the amplitude of the first PSC. First, we carefully re-fitted new and previously presented depression data and find that the taus for depression at low stimulation frequencies (1 and 10Hz) are not affected by exon excisions at the I-II site. We thank the reviewer for detecting our error in units and tau values in the previous figure panels 5H and L (this has now been corrected in the revised figure panels 6I and M). Given that PSC amplitude upon I-IIB excision is significantly smaller than in controls and following I-IIA excision, we suspected that the time course of depression at low stimulation frequency is not significantly affected by the amount of calcium influx during the first PSC. To further test this, we followed the reviewer ’s suggestion and re-measured depression at 1 and 10 Hz for cac-GFP controls and for delta I-IIB in a higher external calcium concentration (1.8 mM), so that the first PSC was increased in amplitude in both genotypes (1.8 mM external calcium triturates the PSC amplitude in delta I-IIB to match that of controls measured in 0.5 mM external calcium, see revised Figs. 6H, L). Neither in control, nor in delta I-IIB did this affect the time course of synaptic depression (see revised Figs. 6I, M). This indicates that at low stimulation frequencies (1 and 10Hz) the time course of depression is not affected by mean quantal content. This is consistent with the paired pulse ratio at 100 ms interpulse interval shown in figures 6A-D. However, for synaptic depression at 1 Hz stimulation the variability of the data is higher for delta I-IIB (independent of external calcium concentration, see rev. Fig. 6I), which might also be due to reduced channel number in this genotype. Taken together, the data are in line with the idea that altered cac channel numbers in active zones are sufficient to explain all effects that we observe upon I-IIB excision on PPRs and synaptic depression at low stimulation frequencies. This is now clarified in the revised text on page 12, lines 3 to 7.

(12) The GFP-tagged I-IIA and mEOS4b-tagged I-IIB cac puncta shown in Figure 6N appear larger than the Brp puncta. Endogenously tagged cac puncta are typically smaller than Brp puncta (Gratz et al., 2019). Also, the I-IIA and I-IIB fluorescence sometimes appear to be partially non-overlapping. First, I suggest adding panels that show all three channels merged. Second, could they analyze the area and area overlap of I-IIA and I-IIB with regard to each other and to Brp, and compare it to cac-GFP? Any speculation as to how the different tags could affect localization? Finally, I recommend moving the dI-IIA and dI-IIB localization data shown in Figure 6N to an earlier figure (Figure 1 or Figure 3).

We now show panels with the two I-II cac isoforms merged in the revised figure 7H (previously 6N). We also tested merging all three labels as suggested, but found this not instructive for the reader. We thank the reviewer for pointing out that the Brp puncta appeared smaller than the cac puncta in some panels. We carefully went through the data and found that the Brp puncta are not systematically smaller than the cac puncta. Please note that punctum size can appear quite differently, depending on different staining qualities as well as different laser intensities and different point spread in different imaging channels. The purpose of this figure was not to analyze punctum size and labeling intensity, but instead, to demonstrate that I-IIA and I-IIB are both present in most active zones, but some active zones show only I-IIB labeling, as quantified in figure 7I. We did not follow the suggestion to conduct additional co-localization analyses and compare it with cac-GFP controls, because Pearson co-localization coefficients for cac-GFP and all exon-out variants analyzed, including delta I-IIA and delta I-IIB are presented in the revised figure 4D. Moreover, delta I-IIA and delta I-IIB show similar Manders 1 and 2 co-localization coefficients with Brp (see Figs. 4E, F). We do not want to speculate whether the different tags have any effect on localization precision. Artificial differences in localization precision can also be suggested by different antibodies, but we know from our STED analyses with identical tags and antibodies for all isoforms that I-IIA and I-IIB co-localize identically with Brp (see Figs. 5A-E). Finally, we prefer to not move the figure because we believe it is informative to show our finding that active zones usually contain both splice I-II variants together with the finding that only I-IIB is required for PHP.

Recommendations for the authors:

Reviewing Editor Comments:

We thank you for your submission. All three reviewers urge caution in interpreting the S4 splice variant playing a role specifically in Cac localization, as opposed to just leading to instability and degradation. There are other issues with the electrophysiological experiments, a need for improved imaging and analyses, and some areas of interpretation detailed in the reviews.

We agree that additional data was required to conclude that IS4 splicing plays a specific role in cac channel localization and is not just leading to channel instability and degradation. As outlined in detail in our response to reviewer 1, comment 1, we conducted several sets of experiments to support our interpretation. First, electrophysiological experiments show that upon removal of IS4B, which eliminates synaptic transmission at the larval NMJ and cac positive label in presynaptic active zones, somatodendritic cac current is reliably recorded (new data in revised figure 3C). This is not in line with a channel instability or degradation effect, but instead with IS4B containing isoforms being required and sufficient for evoked release from NMJ motor terminals, whereas IS4A isoforms are not sufficient for evoked release from axon terminals, but IS4A isoforms alone can mediate a distinct component of somatodendritic calcium current. Second, immunohostochemical analyses reveal that IS4A, which is not present in NMJ presynaptic active zones, is expressed sparsely, but in reproducible patterns in the larval brain lobes and in specific regions of the anterior VNC parts (new supplementary figure 1). Again, the absence of a IS4A-containing cac isoform from presynaptic active zones but their simultaneous presence in other parts of the nervous system is in accord with isoform specific localization, but not with general channel isoform instability. Third, enlargements of NMJ boutons with brp positive presynaptic active zones confirm the absence of IS4A and the presence of IS4B in active zones (these enlargements are now shown in the revised figures 2A-C, 3A, and 4A-C). Fourth, as suggested we have quantified the Pearson co-localization of IS4 isoforms with Brp in presynaptic active zones (revised Fig. 2D). This confirms quantitatively similar co-localization of IS4B and control with Brp, but no co-localization of IS4A with Brp. In fact, the labeling intensity of IS4A in presynaptic active zones is quantitatively not significantly different from background, no IS4A label is detected anywhere in the axon terminals at the NMJ, but we find IS4 label in the CNS. Together, these data strongly support our interpretation that the IS4 splice site plays a distinct role in cac channel localization. Figure legends as well as results and discussion section have been modified accordingly (the respective page and line numbers are listed in our-point-by-point responses).

In addition, we have carefully addressed all other public comments as well as all other recommendations for authors by providing multiple new data sets, new image analyses, and revising text. Addressing the insightful comments of all three reviewers and the reviewing editor has greatly helped to make the manuscript better.

Reviewer #1 (Recommendations For The Authors):

The conclusion that the IS4B exon controls Cac localization to active zones versus simply being required for channel abundance is not well supported. The authors need to either mention both possibilities or provide stronger support for the active zone localization model if they want to emphasize this point.

We agree and have included several additional data sets as outlined in our response to point 1 of reviewer 1 and to the reviewing editor (see above). These new data strongly support our interpretation that the IS4B exon controls Cac localization to active zones and is not simply required for channel abundance. The additions to the figures and accompanying text (including the respective figure panel, page, and line numbers) are listed in the point-bypoint responses to the reviewers’ public suggestions.

Figure 2C staining for Cac localization in the delta 4B line is difficult to compare to the others, as the background staining is so high (muscles are green for example). As such, it is hard to determine whether the arrows in C are just background.

We had over-emphasized the green label to show that there really is no cacophony label in active zones. However, we agree that this hampered image interpretation. Thus, we have adjusted brightness such that it matches the other genotypes (see new figure panel 2C, and figure 3A, bottom). Revising the figure as suggested by the reviewer shows much more clearly that IS4B puncta are detected exclusively in presynaptic active zones, whereas IS4A channels are not detectable in active zones or anywhere else in the axon terminal boutons. Quantification of IS4A label in brp positive active zones confirms that labeling intensity is not significantly above background (page 6, lines 29 to 31 and page 7, lines 19 to 21). Therefore, IS4A is not detectable in active zones at the NMJ.

It seems more likely that the removal of the 4B exon simply destabilizes the protein and causes it to be degraded (as suggested by the Western), rather than mislocalizing it away from active zones. It's hard to imagine how some residue changes in the S4 voltage sensor would control active zone localization to begin with. The authors should note that the alternative explanation is that the protein is just degraded when the 4B exon is removed.

Based on additional data and analyses, we disagree with the interpretation that removal of IS4B disrupts protein integrity and present multiple lines of evidence that support sparse expression of IS4A channels (ΔIS4B). As outlined in our response to reviewer 1 and to the reviewing editor, we show (1) in new immunohistochemical stainings (new supplementary figure 1) that upon removal of IS4B, sparse label is detectable in the VNC and the brain lobes (for detail see above). (2) In our new figure 3C, we show cacophony-mediated somatodendritic calcium currents recorded from adult flight motoneurons in a control situation and upon removal of IS4B that leaves only IS4A channels. This clearly demonstrates that IS4A underlies a substantial component of the HVA somatodendritic calcium current, although it is absence from axon terminals. This is in line with isoform specific functions at different locations, but not with IS4A instability/degradation. (3) We do not agree with the reviewer’s interpretation of the Western Blot data in figure 1E (formerly figure 1D). Together with our immunohistochemical data that show sparse cacophony IS4A expression, we think that the faint band upon removal of IS4B in a heterozygous background (that reduces labeled channels even further) reflects the sparseness of IS4A expression. This sparseness is not due to channel instability, but to IS4A functions that are less abundant than the ubiquitously expressed cac^IS4B channels at presynaptic active zones of fast chemical synapses (see page 15, lines 24 to 29).

If they really want to claim the 4B exon governs active zone localization, much higher quality imaging is required (with enlarged views of individual boutons and their AZs, rather than the low-quality full NMJ imaging provided). Similarly, higher resolution imaging of Cac localization at Muscle 12 (Figure 2H) boutons would be very useful, as the current images are blurry and hard to interpret. Figure 6N shows beautiful high-resolution Cac and Brp imaging in single boutons for the I-II exon manipulations - the authors should do the same for the 4B line. For all immuno in Figure 2, it is important to quantify Cac intensity as well. There is no quantification provided, just a sample image. The authors should provide quantification as they do for the delta I-II exons in Figure 3.

We did as suggested and added figure panels to figure 2A-C and to new figures 3A (formerly part of figure 2 and 4A-C (formerly figure 3) showing magnified label at the NMJ AZs to better judge on cacophony expression after exon excision. These data are now referred to in the results section on page 6, lines 22 to 24, page 7, lines 18 to 21 and page 8, lines 17/18.

As suggested, we now also provide quantification of co-localization with brp puncta as Pearson’s correlation coefficient for control, IS4B, and IS4A in the new figure panel 2D (text on page 6, lines 34 to 38). This further underscores control-like active zone localization of IS4B but no significant active zone localization of IS4A. As suggested, we quantified now also the intensity of IS4B label in active zones, and it was not different from control (see revised figure 4H and text on page 8, lines 38/39). We did not quantify the intensity of IS4A label, because it was not over background (text, page 6, lines 30/31).

Reviewer #2 (Recommendations For The Authors):

(1a) Questions about the engineered Cac splice isoform alleles:

The authors using CRISPR gene editing to selectively remove the entire alternatively spliced exons of interest. Do the authors know what happens to the cac transcript with the deleted exon? Is the deleted exon just skipped and spliced to the next exon? Or does the transcript instead undergo nonsense-mediated decay?

We do not believe that there is nonsense mediated mRNA decay, because for all exon excisions the respective mRNA and protein are made. Protein has been detected on the level of Western blotting and immunocytochemistry. Therefore, we are certain that the mRNA is viable for each exon excision (and we have confirmed this for low abundance cac protein isoforms by rt-PCR), but only subsets of cac isoforms can be made from mRNAs that are lacking specific exons. However, we can not make any statements as to whether the lack of specific protein isoforms exerts feedback on mRNA stability, the rate of transcription and translation, or other unknown effects.

(1b) While it is clear that the IS4 exons encode part of the voltage sensor in the first repeat, are there studies in Drosophila to support the putative Ca-beta and G-protein beta-gamma binding sites in the I-II loop? Or are these inferred from Mammalian studies?

To the best of our knowledge, there are no studies in Drosophila that unambiguously show Caβ and Gβγ binding sites in the I-II loop of cacophony. However, sequence analysis strongly suggests that I-IIB contains both, a Caβ as well as a Gβγ binding site (AID: α-interacting domain) because the binding motif QXXER is present. In mouse Cav2.1 and Ca_v2.2 channels the sequence is QQIER, while in Drosophila cacophony I-IIB it is QQLER. In the alternative IIIA, this motif is not present, strongly suggesting that G_βγ subunits cannot interact at the AID. However, as already suggested by Smith et al. (1998), based on sequence analysis, Ca_β should still be able to bind, although possibly with a lower affinity. We agree that this information should be given to the reader and have revised the text accordingly on page 5, lines 9 to 17.

(1c) The authors assert that splicing of Cav2/cac in flies is a means to encode diversity, as mammals obviously have 4 Cav2 genes vs 1 in flies. However, as the authors likely know, mammalian Cav2 channels also have various splice isoforms encoded in each of the 4 Cav2 genes. The authors should discuss in more detail what is known about the splicing of individual mammalian Cav2 channels and whether there are any homologous properties in mammalian channels controlled by alternative splicing.

We agree and now provide a more comprehensive discussion of vertebrate Ca_v2 splicing and its impact on channel function. In line to what we report in Drosophila, properties like G_βγ binding and activation voltage can also be affected by alternative splicing in vertebrate Ca_v2 channel, through the exon patterns are quite different from Drosophila. We integrated this part on page 14, first paragraph) in the revised discussion. The respective text is below for the reviewer’s convenience:

“However, alternative splicing increases functional diversity also in mammalian Ca_v2 channels. Although the mutually exclusive splice site in the S4 segment of the first homologous repeat (IS4) is not present in vertebrate Cav channels, alternative splicing in the extracellular linker region between S3 and S4 is at a position to potentially change voltage sensor properties (Bezanilla 2002). Alternative splice sites in rat Ca_v2.1 exon 24 (homologous repeat III) and in exon 31 (homologous repeat IV) within the S3-S4 loop modulate channel pharmacology, such as differences in the sensitivity of Ca_v2.1 to Agatoxin. Alternative splicing is thus a potential cause for the different pharmacological profiles of P- and Q-channels (both Ca_v2.1; Bourinet et al. 1999). Moreover, the intracellular loop connecting homologous repeats I and II is encoded by 3-5 exons and provides strong interaction with G_βγ-subunits (Herlitze et al. 1996). In Ca_v2.1 channels, binding to G_βγ subunits is potentially modulated by alternative splicing of exon 10 (Bourinet et al. 1999). Moreover, whole cell currents of splice forms α1A-a (no Valine at position 421) and α1A-b (with Valine) represent alternative variants for the I-II intracellular loop in rat Ca_v2.1 and Ca_v2.2 channels. While α1A-a exhibits fast inactivation and more negative activation, α1A-b has delayed inactivation and a positive shift in the IV-curve (Bourinet et al. 1999). This is phenotypically similar to what we find for the mutually exclusive exons at the IS4 site, in which IS4B mediates high voltage activated cacophony currents while IS4A channels activate at more negative potentials and show transient current (Fig. 3; see also Ryglewski et al. 2012). Furthermore, altered Ca_β interaction have been shown for splice isoforms in loop III (Bourinet et al. 1999), similar to what we suspect for the I-II site in cacophony. Finally, in mammalian VGCCs, the C-terminus presents a large splicing hub affecting channel function as well as coupling distance to other proteins. Taken together, Ca_v2  channel diversity is greatly enhanced by alternative splicing also in vertebrates, but the specific two mutually exclusive exon pairs investigated here are not present in vertebrate Ca_v2 genes.”

(1d) In Figure 1, it would be helpful to see the entire cac genomic locus with all introns/exons and the 4 specific exons targeted for deletion.

We agree and have changed figure 1 accordingly.

(2a) Cav2.IS4B deletion alleles:

More work is necessary to explain the localization of Cac controlled by the IS4B exon. First, can the authors determine whether actual Cac channels are present at NMJ boutons? The authors seem to indicate that in the IS4B deletion mutants, some Cac (GFP) signal remains in a diffuse pattern across NMJ boutons. However, from the imaging of wild-type Cac-GFP (and previous studies), there is no Cac signal outside of active zones defined by the BRP signal. It would benefit the study to a) take additional, higher resolution images of the remaining Cac signal at NMJs in IS4B deletion mutants, and b) comment on whether the apparent remaining signal in these mutants is only observed in the absence of IS4Bcontaining Cac channels, or if the IS4A-positive channels are normally observed (but perhaps mis-localized?).

We have conducted additional analyses to show convincingly that IS4A channels (that remain upon IS4B deletion) are absent from presynaptic active zone. Please see also responses to reviewers 1 and 3. By adjusting the background values in of CLSM images to identical values in control, delta IS4A, and delta IS4B, as well as by providing selective enlargements as suggested, the figure panels 2C, Ci and 3A now show much clearer, that upon deletion of IS4B no cac label remains in active zones or anywhere else in the axon terminal boutons (see text on page 6, lines 22 to 24). This is further confirmed by quantification showing the in IS4B mutants cac labeling intensity in active zones is not above background (see text on page 6, lines 27 to 31). We never intended to indicate that there was cac signal outside of active zones defined by the brp signal, and we now carefully went through the text to not indicate this possibility unintentionally anywhere in the manuscript.

(2b) Do the authors know whether any presynaptic Ca2+ influx is contributed by IS4Apositive Cac channels at boutons, given the potential diffuse localization? There are various approaches for doing presynaptic Ca2+ imaging that could provide insight into this question.

We agree that this is an interesting question. However, based on the revisions made, we now show with more clarity that IS4A channels are absent from the presynaptic terminal at the NMJ. IS4A labeling intensities within active zones and anywhere else in the axon terminals are not different from background (see text on page 6, lines 27 to 31 and revised Figs. 2C, Ci, and 3A with new selective enlargements in response to comments of both other reviewers). This is in line with our finding that evoked synaptic transmission from NMJ axon terminals to muscle cells is mostly absent upon excision of IS4B (see Fig. 3B). The very small amplitude EPSC (below 5 % of the normal amplitude of evoked EPSCs) that can still be recorded in the absence of IS4B is similar to what is observed in cac null mutant junctions and is mediated by calcium influx through another voltage gated calcium channels, a Ca_v1 homolog named Dmca1D, as we have previously published (Krick et al., 2021, PNAS 118(28):e2106621118. Gathering additional support for the absence of IS4A from presynaptic terminals by calcium imaging experiments would suffer significantly from the presence of additional types of VGCCs in presynaptic terminals (for sure Dmca1D (Krick et al., 2021) and potentially also the Ca_v3 homolog DmαG or Dm-α1T). Such experiments would require mosaic null mutants for cac and DmαG channels in a mosaic IS4B excision mutant, which, if feasible at all, would be very hard and time consuming to generate. In the light of the additional clarification that IS4A is not located in NMJ axon terminal boutons, as shown by additional labeling intensity analysis, revised figures with selective enlargement, and revised text, we feel confident to state that IS4A is not sufficient for evoked SV release.

(2c) Mechanistically, how are amino acid changes in one of the voltage sensing domains in Cac related to trafficking/stabilization/localization of Cac to AZs?

This is an exciting question that has occupied our discussions a lot. Some sorting mechanism must exist that recognizes the correct protein isoforms, just as sorting and transport mechanisms exist that transport other synaptic proteins to the synapse. We do not think that the few amino acid changes in the voltage sensor are directly involved in protein targeting. We rather believe that the cacophony variants that happen to contain this specific voltage sensor are selected for transport out to the synapse. There are possibilities to achieve this cell biological, but we have not further addressed potential mechanisms because we do not want enter the realms of speculation.

(3) How are auxiliary subunits impacted in the Cac isoform mutants?

Recent work by Kate O'Connor-Giles has shown that both Stj and Ca-Beta subunits localize to active zones along with Cac at the Drosophila NMJ. Endogenously tagged Stj and CaBeta alleles are now available, so it would be of interest to determine if Stj and particular Cabeta levels or localization change in the various Cac isoform alleles. This would be particularly interesting given the putative binding site for Ca-beta encoded in the I-II linker.

We agree that the synthesis of the work of Kate O'Connor-Giles group and our study open up new avenues to explore exciting hypotheses about differential coupling of specific cacophony splice isoforms with distinct accessory proteins such as Caβ and α₂δ subunits. However, this requires numerous full sets of additional experiments and is beyond the scope of this study.

(4a) Interpretation of short-term plasticity in the I-IIB exon deletion:

The changes in short-term plasticity presented in Figure 5 are interpreted as an additional phenotype due to the loss of the I-IIB exon, but it seems this might be entirely explained simply due to the reduced Cac levels. Reduced Cac levels at active zones will obviously reduce Ca2+ influx and neurotransmitter release. This may be really the only phenotype/function of the I-IIB exon. Hence, to determine whether loss of the I-IIB exon encodes any functions in short-term plasticity, separate from reduced Cac levels, the authors should compare short-term plasticity in I-IIB loss alleles compared to wild type with starting EPSC amplitudes are equal (for example by reducing extracellular Ca2+ levels in wild type to achieve the same levels at in Cac I-IIB exon deleted alleles). Reduced release probability, simply by reduced Ca2+ influx (either by reduced Cac abundance or extracellular Ca2+) should result in more variability in transmission, so I am not sure there is any particular function of the I-IIB exon in maintaining transmission variability beyond controlling Cac abundance at active zones.

For two reasons we are particularly grateful for this comment. First, it shows us that we needed to explain much clearer that our interpretation is that changes in paired pulse ratios (PPRs) and in depression at low stimulation frequencies are a causal consequence of lower channel numbers upon I-IIB exon deletion, precisely as pointed out by the reviewer. We have carefully revised the text accordingly on page 10, lines 14-25, page 11, lines 3-7 and 22-28; page 16, lines 36-38. Second, the experiment suggested by the reviewer is superb to provide additional evidence that the cause of altered PPRs is in fact reduced channel number, but not altered channel properties. Accordingly, we have conducted additional TEVC recordings in elevated external calcium (1.8 mM) so that the single PSC amplitudes in I-IIB excision animals match those of controls in 0.5 mM extracellular calcium. This makes the amplitudes and the variance of PPR for all interpulse intervals tested control-like (see revised Figs. 6D, E). This strongly indicates that differences observed in PPRs as well as the variance thereof were caused by the amount of calcium influx during the first EPSC, and thus by different channel numbers in active zones.

(4b) Another point about the data in Figure 5: If "behaviorally relevant" motor neuron stimulation and recordings are the goal, the authors should also record under physiological Ca2+ conditions (1.8 mM), rather than the highly reduced Ca2+ levels (0.5 mM) they are using in their protocols.

Although we doubt that the effective extracellular calcium concentration that determines the electromotoric force for calcium to enter the ensheathed motoneuron terminals in vivo during crawling is known, we followed the reviewer’s suggestion partly and have repeated the high frequency stimulation trains for ΔI-IIB in 1.8 mM calcium. As for short-term plasticity this brings the charge conducted to values as observed in control and in ΔI-IIA in 0.5 mM calcium. Therefore, all difference observed in previous figure 5 (now revised figure 6) can be accounted to different channel numbers in presynaptic active zones. This is now explained on page 11, lines 19-28. For controls recordings at high frequency stimulation in higher external calcium (e.g. 2 mM) have previously been published and show significant synaptic depression (e.g. Krick et al., 2021, PNAS). Given that in the exon out variants we do not expect any differences except from those caused by different channel numbers, we did not repeat these experiments for control and ΔI-IIA.

(5a) Mechanism of Cac's role in PHP :

As the authors likely know, mutations in Cac were previously reported to disrupt PHP expression (see Frank et al., 2006 Neuron). Inexplicably, this finding and publication were not cited anywhere in this manuscript (this paper should also be cited when introducing PhTx, as it was the first to characterize PhTx as a means of acutely inducing PHP). In the Frank et al. paper (and in several subsequent studies), PHP was shown to be blocked in mutations in Cac, namely the CacS allele. This allele, like the I-IIB excision allele, reduces baseline transmission presumably due to reduced Ca2+ influx through Cac. The authors should at a minimum discuss these previous findings and how they relate to what they find in Figure 6 regarding the block in PHP in the Cac I-IIB excision allele.

We thank the reviewer for pointing this out and apologize for this oversight. We agree that it is imperative to cite the 2006 paper by Frank et al. when introducing PhTx mediated PHP as well as when discussing cac the effects of cac mutants on PHP together with other published work. We have revised the text accordingly on page 12, lines 9-11 and 21-23 and on page 17, lines 29-33.

In terms of data presentation in Fig. 6, as is typical in the field, the authors should normalize their mEPSC/QC data as a percentage of baseline (+PhTx/-PhTx). This makes it easier to see the reduction in mEPSC values (the "homeostatic pressure" on the system) and then the homeostatic enhancement in QC. Similarly, in Fig. 6M, the authors should show both mEPSC and QC as a percentage of baseline (wild type or non-GluRIIA mutant background).

We agree and have changed figure presentation accordingly. Figure 7 (formerly figure 6) was updated as was the accompanying results text on page 12, lines 23-40.

(6) Cac I-IIA and I-IIB excision allele colocalization at AZs:

These are very nice and important experiments shown in Figures 6N and O, which I suggest the authors consider analyzing in further detail. Most significantly:

(6i) The authors nicely show that most AZs have a mix of both Cac IIA and IIB isoforms. Using simple intensity analysis, can the authors say anything about whether there is a consistent stoichiometric ratio of IIA vs IIB at single AZs? It is difficult to extract actual numbers of IIA vs IIB at individual AZs without having both isoforms labeled mEOS4b, but as a rough estimate can the authors say whether the immunofluorescence intensity of IIA:IIB is similar across each AZ? Or is there broad heterogeneity, with some AZs having low vs high ratios of each isoform (as the authors suggest across proximal to distal NMJ AZs)?

We agree and have conducted experiments and analyses to provide these data. We measured the cac puncta fluorescence intensities for heterozygous cac^sfGFP/cac, cacIIIA^sfGFP/cacI-IIB, and cacI-IIB^sfGFP/cacI-IIA animals. We preferred this strategy, because intensity was always measured from cac puncta with the same GFP tag. Next, we normalized all values to the intensities obtained in active zones from heterozygous cac^sfGFP/cac controls and then plotted the intensities of I-IIA versus I-IIB containing active zones side by side. Across junctions and animals, we find a consistent ratio 2:1 in the relative intensities of I-IIB and I-IIA, thus indicating on average roughly twice as many I-IIB as compared to I-IIA channels across active zones. This is consistent with the counts in our STED analysis (see Fig. 5F). These new data are shown in the new figure panel 7J and referred to on page 13, lines 10-16 in the revised text.

(6ii) Intensity analysis of Cac IIA vs IIB after PHP: Previous studies have shown Cac abundance increases at NMJ AZs after PHP. Can the authors determine whether both Cac IIA vs IIB isoforms increase after PHP or whether just one isoform is targeted for this enhancement?

We already show that PHP is not possible in the absence of I-IIB channels (see figure 7). However, we agree that it is an interesting question to test whether I-IIA channel are added in the presence of I-IIB channels during PHP, but we consider this a detail beyond the scope of this study.

Minor points:

(1) Including line numbers in the manuscript would help to make reviewing easier.

We agree and now provide line numbers.

(2) Several typos (abstract "The By contrast", etc).

We carefully double checked for typos.

(3) Throughout the manuscript, the authors refer to Cac alleles and channels as "Cav2", which is unconventional in the field. Unless there is a compelling reason to deviate, I suggest the authors stick to referring to "Cac" (i.e. cacdIS4B, etc) rather than Cav2. The authors make clear in the introduction that Cac is the sole fly Cav2 channel, so there shouldn't be a need to constantly reinforce that cac=Cav2.

We agree and have changed all fly Ca_v2 reference to cac.

(4) In some figures/text the authors use "PSC" to refer to "postsynaptic current", while in others (i.e. Figure 6) they switch to the more conventional terms of mEPSC or EPSC. I suggest the authors stick to a common convention (mEPSC and EPSC).

We have changed PSC to EPSC throughout.

Reviewer #3 (Recommendations For The Authors):

(1) The abstract could focus more on the results at the expense of the background.

We agree and have deleted the second introductory background sentence and added information on PPRs and depression during low frequency stimulation.

(2) What does "strict" active zone localization refer to? Could they please define the term strict?

Strict active zone localization means that cac puncta are detected in active zones but no cac label above background is found anywhere else throughout the presynaptic terminal, now defined on page 6, lines 27-29.

(3) Single boutons/zoomed versions of the confocal images shown in Figures 2A-C, 2H, and 3A-C would be very helpful.

We have provided these panels as suggested (see above and revised figures 2-4). Figure 3 is now figure 4.

(4) The authors cite Ghelani et al. (2023) for increased cac levels during homeostatic plasticity. I recommend citing earlier work making similar observations (Gratz et al., 2019; DOI: 10.1523/JNEUROSCI.3068-18.2019), and linking them to increased presynaptic calcium influx (Müller & Davis, 2012; DOI: 10.1016/j.cub.2012.04.018).

We agree and have added Gratz et al. 2019 and Davis and Müller 2012 to the results section on page 12, lines 17/18 and lines 21-23, in the discussion on page 17, lines 29-33.

(5) The data shown in Figure 3 does not directly support the conclusion of altered release probability in dI-IIB. I therefore suggest changing the legend's title.

We have reworded to “Excisions at the I-II exon do not affect active zone cacophony localization but can alter cacsfGFP label intensity in active zones and PSC amplitude” as this is reflecting the data shown in the figure panels more directly.

(6) It would be helpful to specify "adult flight muscle" in Figure 2J.

We agree that it is helpful to specify in the figure (now revised figure 3C) that the voltage clamp recordings of somatodendritic calcium current were conducted in adult flight motoneurons and have revised the headline of figure panel 3C and the legend accordingly. Please note, these are not muscle cells but central neurons.

(7) Do dIS4B/Cav2null MNs indeed show an inward or outward current at -90 to -70 mV/-40 and -50 mV, or is this an analysis artifact?

No, this is due to baseline fluctuations as typical for voltage clamp in central neurons with more than 6000 µm dendritic length and more than 4000 dendritic branches.

(8) Loss of several presynaptic proteins, including Brp (Kittel et al., 2006), and RBP (Liu et al., 2011), induce changes in GluR field size (without apparent changes in miniature amplitude). The statement regarding the Cav2 isoform and possible effects on GluR number (p. 8) should be revised accordingly.

We understand and have done two things. First, we measured the intensity of GluRIIA immunolabel in ΔI-IIA, ΔI-IIB, and controls and found no differences. Second, we reworded the statement. It now reads on page 9, lines 1-6: “It seems unlikely that presynaptic cac channel isoform type affects glutamate receptor types or numbers, because the amplitude of spontaneous miniature postsynaptic currents (mEPSCs, Fig. 4K) and the labeling intensity of postsynaptic GluRIIA receptors are not significantly different between controls, I-IIA, and I-IIB junctions (see suppl. Fig. 2, p = 0.48, ordinary one-way ANOVA, mean and SD intensity values are 61.0 ± 6.9 (control), 55.8 ± 8.5 (∆I-IIA), 61.1 ± 17.3 (∆I-IIB)). However, we cannot exclude altered GluRIIB numbers and have not quantified GluR receptor field sizes.”

(9) The statement relating miniature frequency to RRP size is unclear (p. 8). Is there any evidence for a correlation between miniature frequency to RRP size? Could the authors please clarify?

We agree that this statement requires caution. Although there is some published evidence for a correlation of RRP size and mini frequency (Neuron, 2009 61(3):412-24. doi: 10.1016/j.neuron.2008.12.029 and Journal of Neuroscience 44 (18) e1253232024; doi: 10.1523/JNEUROSCI.1253-23.2024), which we now refer to on page 9, it is not clear whether this is true for all synapses and how linear such a relationship may be. Therefore, we have revised the text on page 9, lines 6-9. It now reads: “Similarly, the frequency of miniature postsynaptic currents (mEPSCs) remains unaltered. Since mEPSCs frequency has been related to RRP size at some synapses (Pan et al., 2009; Ralowicz et al., 2024) this indicates unaltered RRP size upon I-IIB excision, but we have not directly measured RRP size.”

(10) Please define the "strict top view" of synapses (p. 8).

Top view is what this reviewer referred to as “planar view” in the public review points 6 and 7. In our responses to these public review points we now also define “strict top view”, see page 9, lines 17-19.

(11) Two papers are cited regarding a linear relationship between calcium channel number and release probability (p. 15). Many more papers could be cited to demonstrate a supralinear relationship (e.g., Dodge & Rahaminoff, 1967; Weyhersmüller et al., 2011 doi: 10.1523/JNEUROSCI.6698-10.2011). The data of the present study were collected at an extracellular calcium concentration of 0.5 mM, whereas Meideiros et al. (2023) used 1.5 mM. The relationship between calcium and release is supra-linear around 0.5 mM extracellular calcium (Weyhersmüller et al. 2011). This should be discussed/the statements be revised. Also, the reference to Meideiros et al. (2023) should be included in the reference list.

We have now updated the Medeiros reference (updated version of that paper appeared in eLife in 2024) in the text and reference list. We agree that the relationship of the calcium concentration and P_r can also be non-linear and refer to this on page 16, lines 26-32, but the point we want to make is to relate defined changes in calcium channel number (not calcium influx) as assessed by multiple methods (CLSM intensity measures and sptPALM channel counting) to release probability. We now also clearly state that we measured at 0.5 mM external calcium (page 16, lines 27/28) whereas Medeiros et al. 2024 measured at 1.5 mM calcium (page 16, lines 31/32).

(12) Figure 6: Quantal content does not have any units - please remove "n vesicles".

We have revised this figure in response to reviewer 2 (comment 5) and quantal content is now expressed as percent baseline, thus without units (see revised figure 7).

(13) Figure 6C should be auto-scaled from zero.

This has been fixed by revising that figure in response to reviewer 2 (comment 5)

(14) The data supporting the statement on impaired motor behavior and reduced vitality of adult IS4A should be either shown, or the statement should be removed (p. 13). Any hypotheses as to why IS4A is important for behavior and or viability?

As suggested, we have removed that statement.

(15) They do not provide any data supporting the statement that changes in PSC decay kinetics "counteract" the increase in PSC amplitude (p. 14). The sentence should be changed accordingly.

We agree and have down toned. It now reads on page 16, lines 7-9: “During repetitive firing, the median increase of PSC amplitude by ~10 % is potentially counteracted by the significant decrease in PSC half amplitude width by ~25 %...”.

(16) How do they explain the net locomotion speed increase in dI    -IIA larvae? Although the overall charge transfer is not affected during the stimulus protocols used, could the accelerated PSC decay affect PSP summation (I would actually expect a decrease in summation/slower speed)? Independent of the voltage-clamp data, is muscle input resistance changed in dI-IIA mutants?

Muscle input resistance is not altered in I-II mutants. We refer to potential causes of the locomotion effects of I-IIA excision in the discussion. On page 16, lines 12 to 21 it reads: “there is no difference in charge transfer from the motoneuron axon terminal to the postsynaptic muscle cell between ∆I-IIA and control. Surprisingly, crawling is significantly affected by the removal of I-IIA, in that the animals show a significantly increased mean crawling speed but no significant change in the number of stops. Given that the presynaptic function at the NMJ is not strongly altered upon I-IIA excision, and that I-IIA likely mediates also Ca_v2 functions outside presynaptic AZs (see above) and in other neuron types than motoneurons, and that the muscle calcium current is mediated by Ca_v1>/i> and Ca_v3, the effects of I-IIA excision of increasing crawling speed is unlikely caused by altered pre- or postsynaptic function at the NMJ. We judge it more likely that excision of I-IIA has multiple effects on sensory and pre-motor processing, but identification of these functions is beyond the scope of this study.”

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

The authors thank the reviewer for the positive response. Regarding the ELISA assays used to measure the array of complement proteins described, these were extensively validated for the following parameters: specificity, intra-assay and inter-assay precision, accuracy, stability, reference range, and parallelism. All assays were validated in plasma, vitreous and aqueous humour. Due to the limited volume and availability of ocular fluids from individuals in the study, validation in vitreous and aqueous matrices was performed using a pool of several samples from post-mortem donors. At the time this study was initiated, the Millipore Luminex complement panels and the Quidel C3a and Ba EIA were the most sensitive assays and the only commercially available options capable of measuring the proteins of interest in the context of limited vitreous and aqueous humor sample. The concentrations measured were observed at similar ranges as those published in the literature using assays in distinct patient populations e.g. in (Mandava et al, Invest Ophthalmol Vis Sci, 2020).

Measurements from vitreous and aqueous from subject samples were deemed reportable if they were within the quantifiable ranges defined for these sample types during the validation (coefficient of variation of 20%, or 30% when results were below the lower limit of quantification but above limit of detection). Notably, given the limited amount of biomarker data due to small sample size, we share results from outlier biomarker measurements, to illustrate the heterogeneity in sample quality. We further publish plasma sample biomarker results in supplemental table 5 wherein complement protein concentrations can be observed and compared to normal ranges in the literature.

Adding confidence to the robustness of our assays was the observation that some of the complement proteins quantified by standard assay (e.g. plate and bead-based ELISAs) were also measured by the OLINK assay, and there was a general trend observed for positive correlation between results from both assays for FI levels post-treatment. However, we did not provide detailed correlative statistical analyses for further complement proteins as OLINK findings were deemed highly exploratory and hypothesis generating, and because the OLINK assay produced normalised results which are challenging to directly compare to ELISA results that were absolute.

Reviewer #2 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

The authors thank the reviewer for the positive response and we agree that a limitation of the biomarker strategy for ocular gene therapy delivered to the retinal tissues is inferring PK/PD from vitreous and aqueous samples, which are the fluid sample compartments accessible from subjects available to measure molecular treatment response. We agree that these compartments may not accurately represent sub-retinal and tissue level complement turnover. In the discussion, line 508, we state: ‘Overall, the data suggests that fully functional FI is being secreted into the VH, but the regulatory effects on the level of Ba may be representative of convertase formation in the VH and not the macula retina/RPE nor the choroid. To validate this hypothesis, one approach would be to conduct vitreal sampling using an effective drug targeting C3 for GA in a larger cohort’.

However, the observation of elevation of FI in VH (and AH) post treatment, and changes in levels of downstream complement proteins that align with prior knowledge of control of alternative pathway activation, is compelling evidence that these measurements reflect modest but direct consequences of an FI-gene therapy that was delivered to the subretinal space. We add to the discussion, line 479: ‘the findings of elevated FI in the VH after sub-retinally delivered CFI gene therapy and changes in complement pathway proteins post-treatment build confidence that VH matrix is at least partially reflecting the complement system at the retinal layers and treatment site, and is a valid biomarker for PK/PD insights in response to treatment.’

Furthermore, the observation of moderately raised FI levels in modelled VH post treatment being insufficient to control CS activation in vitro accords with the lack of clinical response observed at phase II. We note that measuring FI and complement biomarkers in retinal tissues from treated eyes at post-mortem would be one way to explore the PK/PD effects from AAV2-FI gene therapy.

Reviewer #3 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

See response to reviewer 3’s review after reviewer 3 recommendations section below.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

The authors present strong evidence using validated complement biomarker assays and comprehensive proteomic profiling that support their findings. The presentation of complement biomarker data in vitreous humor and aqueous humor after FI augmentation is presented in a clear and concise format. The direct comparison of complement biomarkers in vitreous humor and aqueous humor from the same patients and demonstrating similarities and differences is important for the nascent complement gene therapy field. Developing a novel in vitro complement model and comparing pegcetacoplan, FH, and FI inhibitors provides the field with a valuable assay to benchmark other complement therapeutics. As currently designed, the in vitro assay supports why FI augmentation did not contribute to clinical success. It also suggests that non-physiological concentrations of FI protein (over 100 µg/mL) maximally inhibit C3a signal by ~50%, whereas both pegcetacoplan and FH reduce the signal by 100%. Does this suggest that CFI is not an appropriate therapeutic target to control complement overactivation in the eye?

We agree with the reviewer that the new data from the novel in vitro assay coupled with the clinical findings from the phase II gene therapy trial does now suggest FI is less attractive as a therapeutic target for controlling complement activation in the retinal tissues of subjects with Geographic Atrophy.

Reviewer #3 (Recommendations For The Authors):

I think the authors have done a great job collecting and analysing these clinical samples and elucidating the baseline complement protein profile in both the AH and VH. I only have minimal suggested changes.

Perhaps a more direct discussion around the limitations of adding more FI into environments where there is no excess of FI-cofactors present? And a discussion around the limitations of VH (and VA for that matter) biomarker sampling for a disease that primarily affects the neurosensory retina and outer blood/retinal barrier: perhaps the landscape of complement proteins is different yet again (although, admittedly, impossible to sample in a patient)? Finally, would it not have been better to perform complement activation experiments using the VH of treated patients directly rather than creating an artificial VH matrix (there may, or may not, be a couple of things in human VH that directly affect complement turnover...)?

We thank the reviewer for the supportive comments. This study is the first to describe FI and FH levels and respective ratios in vitreous humour (plus aqueous and plasma) from GA subjects, before and after sub-retinal gene therapy. It is compelling to observe that in the VH the levels of FI are greater than FH, the primary fluid phase co-factor for FI enzymatic activity. This new information does indeed argue against further FI supplementation (using gene therapy) being of added benefit to controlling the complement system in the broader population in individuals with Geographic Atrophy. We note that at the start of the clinical development of GT005/PPY988 AAV2-FI gene therapy, there was limited information on FI and FH levels in AMD in ocular fluids to inform the pharmacodynamics of complement activation. Now, by running the FOCUS phase I clinical trial and measuring the complement biomarker data using validated assays we have added to our understanding on the levels and ratio of FI to FH and other complement proteins in a larger number of GA subjects’ ocular samples.  We report the levels of complement proteins measured in ocular and systemic samples, to show the ranges and also the differences in ratios between the different matrices.   

Regarding the statement that FI supplementation could likely be ineffective due to limited FH cofactor; FH is not the only co-factor that FI may partner with at cell surfaces to become enzymatically active (others include MCP (CD46) and CR1 (CD35), although the latter is known to be of limited expression in the eye), as such, it is certainly true that other proteins may be present in the tissue altering the kinetics of FI’s activity after sub-retinal gene-therapy. In addition, the ratio between FI and FH detected in the VH may not be the same as in retinal tissue. As such, we agree that drawing insights from biomarkers in the VH may not fully reflect the disease processes and treatment response at the retinal cell layers, but it is the closest fluid sample available to sample tissue released soluble proteins. We acknowledge that VH biomarkers will not fully capture retinal disease processes and treatment responses, but due to their proximity, will reflect retina-released soluble proteins. The findings of elevated FI in the VH after sub-retinally delivered CFI gene therapy and changes in complement pathway proteins post-treatment build confidence that VH matrix is at least partially reflecting the complement system at the retinal layers and treatment site, and is a valid biomarker for PK/PD insights in response to treatment. We agree modelling different inhibitor effects on complement activation directly using subject’s vitreous would be informative, but this was not possible due to the limitations of very small sample volume.

We add several sentences to the discussion regarding the points above. Line 473: ‘Notably, that FI does not reduce C3a breakdown to baseline even at supermolecular concentrations suggests cofactor limitation that might be more pronounced in VH given FH is not in excess of FI as is the case in blood 27. Moreover, there are additional cell-bound cofactors for FI that may be present in retinal tissue that are not present in the VH and could further alter the kinetics of the assay, such as MCP (CD46) albeit with disease related changes observed 37. However, the findings of elevated FI in the VH after sub-retinally delivered CFI gene therapy and changes in complement pathway proteins post-treatment build confidence that VH matrix is at least partially reflecting the complement system at the retinal layers and treatment site, and is a valid biomarker for PK/PD insights in response to treatment.’

Minor comments:

Line 237: Missing parenthesis at the end of the sentence

Manuscript updated.

Line 435: Missing secondary parenthesis after .....Figure 3A)......

Manuscript updated.

Line 536: I don't think suggesting the addition of FHR proteins into the neurosensory retina/VH is such a good idea

The reference to FHRs has been clarified in the manuscript, line 558. The authors note that FHR dimerization domains have been engineered to dimerize Factor H constructs increasing half-life and potency for drugs currently in development.

Author response:

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

Reviewer # 1 (Public Review):

Summary:

Inthispreprint, theauthorssystematicallyandrigorouslyinvestigatehowspecificclassesofresiduemutations alter the critical temperature as a proxy for the driving forces for phase separation. The work is well executed, the manuscript well-written, and the results reasonable and insightful.

Strengths:

The introductory material does an excellent job of being precise in language and ideas while summarizing the state of the art. The simulation design, execution, and analysis are exceptional and set the standard for these types of large-scale simulation studies. The results, interpretations, and Discussion are largely nuanced, clear, and well-motivated.

We thank the reviewer for their assessment of our work and for highlighting the key strengths of the paper.

Weaknesses:

This is not exactly a weakness, but I think it would future-proof the authors’ conclusions to clarify a few key caveats associated with this work. Most notably, given the underlying implementation of the Mpipi model, temperature dependencies for intermolecular interactions driven by solvent effects (e.g., hydrophobic effect and charge-mediated interactions facilitated by desolvation penalties) are not captured. This itself is not a “weakness” per se, but it means I would imagine CERTAIN types of features would not be wellcaptured; notably, my expectation is that at higher temperatures, proline-rich sequences drive intermolecular interactions, but at lower temperatures, they do not. This is likely also true for the aliphatic residues, although these are found less frequently in IDRs. As such, it may be worth the authors explicitly discussing.

We also thank the reviewer for pointing out that a more detailed discussion of the model limitations is needed. The original Mpipi model was designed to probe UCST-type transitions (that are associative in nature) of disordered sequences. The reviewer is correct, that in its current form, the model does not capture LCST-type transitions that depend on changes in solvation of hydrophobic residues with temperature. We have amended the discussion to highlight this fact.

Similarly, prior work has established the importance of an alpha-helical region in TDP-43, as well as the role of aliphatic residues in driving TDP-43’s assembly (see Schmidt et al 2019). I recognize the authors have focussed here on a specific set of mutations, so it may be worth (in the Discussion) mentioning [1] what impact, if any, they expect transient or persistent secondary structure to have on their conclusions and [2] how they expect aliphatic residues to contribute. These can and probably should be speculative as opposed to definitive.

Again - these are not raised as weaknesses in terms of this work, but the fact they are not discussed is a minor weakness, and the preprint’s use and impact would be improved on such a discussion.

We agree with the reviewer that the effects of structural changes/propensities on these scaling behaviors would be an interesting and important angle to probe. We also comment on this in the discussion.

Reviewer # 2 (Public Review):

This is an interesting manuscript where a CA-only CG model (Mpipi) was used to examine the critical temperature (Tc) of phase separation of a set of 140 variants of prion-like low complexity domains (PLDs). The key result is that Tc of these PLDs seems to have a linear dependence on substitutions of various sticker and space residues. This is potentially useful for estimating the Tc shift when making novel mutations of a PLD. However, I have strong reservations about the significance of this observation as well as some aspects of the technical detail and writing of the manuscript.

We thank the reviewer for their thoughtful and detailed feedback on the manuscript.

(1) Writing of the manuscript: The manuscript can be significantly shortened with more concise discussions. The current text reads as very wordy in places. It even appears that the authors may be trying a bit too hard to make a big deal out of the observed linear dependence.

The manuscript needs to be toned done to minimize self-promotion throughout the text. Some of the glaring examples include the wording “unprecedented”, “our research marks a significant milestone in the field of computational studies of protein phase behavior ..”, “Our work explores a new framework to describe, quantitatively, the phase behavior ...”, and others.

We thank the reviewer for their suggestions on the writing of the manuscript. We understand the concern regarding the length and tone of the manuscript, and in response to their feedback, we have revised the language throughout the manuscript.

There is really little need to emphasize the need to manage a large number of simulations for all 140 variants. Yes, some thoughts need to go into designing and managing the jobs and organizing the data, but it is pretty standard in computational studies. For example, large-scale protein ligand-free energy calculations can require one to a few orders of magnitude larger number of runs, and it is pretty routine.

We fully agree with the reviewer that this aspect of the study is relatively standard in computational research and does not require special emphasis. In response, we have revised the manuscript to shorten the aforementioned section, focusing instead on the scientific insights gained from the simulations rather than the logistical challenges of managing them.

When discussing the agreement with experimental results on Tm, it should be noted that the values of R > 0.93 and RMSD < 14 K are based on only 16 data points. I am not sure that one should refer to this as “extended validation”. It is more like a limited validation given the small data size.

We thank the reviewer for their consideration of our validation set. Indeed, the agreement with experimental results is based on 16 data points, as this set represents the available published data at the time of writing of this manuscript. The term “extended validation” is used to signify that our current dataset builds upon previous validations (in Joseph, Reinhardt et al. Nat Comput. Sci. 2021), incorporating additional variants not previously examined. The metrics of an r>0.93 and a low RMSD indicate a strong agreement between the model and experiments, and an improvement with respect to other reported models. We are committed to continue validating our methods.

Results of linear fitting shown in Eq 4-12 should be summarized in a single table instead of scattering across multiple pages.

We considered the reviewer’s suggestion to compile all the laws into a single table. However, we believe it would be more effective for readers to reference each relationship directly where it is first discussed in the text. That said, we do include Table 1 in the original manuscript, which provides a summary of all the laws.

The title may also be toned down a bit given the limited significance of the observed linear dependence.

We respectfully disagree with the reviewer and believe that the current title accurately captures the scope of the manuscript.

(2) Significance and reliability of Tc: Given the simplicity of Mpipi (a CA-only model that can only describe polymerchaindimension)andthelowcomplexitynatureofPLDs, thesequencecompositionitselfisexpected to be the key determinant of Tc. This is also reflected in various mean-field theories. It is well known that other factors will contribute, such as patterning (examined in this work as well), residual structures, and conformational preferences in dilute and dense phases. The observed roughly linear dependence is a nice confirmation but really unsurprising by itself. It appears how many of the constructs deviate from the expected linear dependence (e.g., Figure 4A) may be more interesting to explore.

While linear dependencies in critical solution temperatures may appear expected for certain systems, for example, symmetric hard spheres, the heterogeneity of intrinsically disordered regions (IDRs), like prion-like domains (PLDs), make this finding notable. The simplicity of our linear scaling law belies the underlying complexity of multivalent interactions and sequence-dependent behaviors in a certain sequence regime, which has not been quantitatively characterized in this manner before. Likewise, although linear dependencies may be expected in simplified models, the real-world applicability and empirical validation of these laws in biologically relevant systems are not guaranteed. Our chemically based model provides the robustness needed to do that. The linear relationship observed is significant because it provides a predictive framework for understanding how specific mutations affect a diverse set of PLDs. The framework presented can be extended to other protein families upon the application of a validated model, which might or might not yield linear relationships depending on the cooperative effects of their collective behavior. This extends beyond confirming known theories—it offers a practical tool for predicting phase behavior based on sequence composition

We agree with the reviewer that, while the overarching linear trend is clear, deviations from linearity observed in constructs like those in Figure 4A point to additional, and interesting, layers of complexity. These deviations offer interesting avenues for future research and suggest that while linearity might dominate PLD critical behavior, other factors may modulate this behavior under specific conditions.

This is an excellent suggestion from the reviewer that, while it falls outside the scope of the current study, we are interested in exploring in the future.

Finally, the relationships are all linear, they have been normalized in different ways—the strength of the study also lies in that. Instead of focusing solely on linearity, our study explores the physical mechanisms that underlie these relationships. This approach provides a more complete understanding of how sequence composition and the underlying chemistry of the mutated residues influence T<sub>c</sub.

The assumption that all systems investigated here belong to the same universality class as a 3D Ising model and the use of Eqn 20 and 21 to derive Tc is poorly justified. Several papers have discussed this issue, e.g., see Pappu Chem Rev 2023 and others. Muthukumar and coworkers further showed that the scaling of the relevant order parameters, including the conserved order parameter, does not follow the 3D Ising model. More appropriate theoretical models including various mean field theories can be used to derive binodal from their data, such as using Rohit Pappu’s FIREBALL toolset. Imposing the physics of the 3D Ising model as done in the current work creates challenges for equivalence relationships that are likely unjustified.

We thank the reviewer for raising this point and for highlighting the FIREBALL toolset. Based on our understanding, FIREBALL is designed to fit phase diagrams using mean-field theories, such as Flory–Huggins and Gaussian Cluster Theory. Our experience with this toolset suggests that it places a higher weight on the dilute arm of the binodal. However, in our slab simulations, we observe greater uncertainty in the density of the dilute arm. This leads to only a moderate fit of the data to the mean-field theories employed in the toolset. While we agree that there is no reason to assume the phase behavior of these systems is fully captured by the 3D Ising model, we expect that such a model will describe the behavior near the critical point better than mean-field theories. Testing our results further with different critical exponents would be valuable in assessing how these predictions compare to a broader set of experimental data. Additionally, we have made the raw data points for the phase diagrams available on our GitHub, enabling practitioners to apply alternative fitting methods.

While it has been a common practice to extract Tc when fitting the coexistence densities, it is not a parameter that is directly relevant physiologically. Instead, Csat would be much more relevant to think about if phase separation could occur in cells.

WhileitistruethatCsatisdirectlyrelevanttowhetherphaseseparationcanoccurincellsunder physiological conditions, T_c should not be dismissed as irrelevant.T_c provides fundamental insights into the thermodynamics of phase separation, reflecting the overall stability and strength of interactions driving condensate formation. This stability is crucial for understanding how environmental factors, such as temperature or mutations, might affect phase behavior. In Figure 2C and D we compare experimental C_sat values with our predicted T_c from simulations. These quantities are roughly inversely proportional to each other and so we expect that, to a first approximation, the relationships recovered for T_c should hold when consideringC_sat at a fixed temperature.

Reviewer # 3 (Public Review):

Summary:

“Decoding Phase Separation of Prion-Like Domains through Data-Driven Scaling Laws” by Maristany et al. offers a significant contribution to the understanding of phase separation in prion-like domains (PLDs). The study investigates the phase separation behavior of PLDs, which are intrinsically disordered regions within proteins that have a propensity to undergo liquid-liquid phase separation (LLPS). This phenomenon is crucial in forming biomolecular condensates, which play essential roles in cellular organization and function. The authors employ a data-driven approach to establish predictive scaling laws that describe the phase behavior of these domains.

Strengths:

The study benefits from a robust dataset encompassing a wide range of PLDs, which enhances the generalizability of the findings. The authors’ meticulous curation and analysis of this data add to the study’s robustness. The scaling laws derived from the data provide predictive insights into the phase behavior of PLDs, which can be useful in the future for the design of synthetic biomolecular condensates.

We thank the reviewer for highlighting the importance of our work and for their critical feedback.

Weaknesses:

While the data-driven approach is powerful, the study could benefit from more experimental validation. Experimental studies confirming the predictions of the scaling laws would strengthen the conclusions. For example, in Figure 1, the Tc of TDP-43 is below 300 K even though it can undergo LLPS under standard conditions. Figure 2 clearly highlights the quantitative accuracy of the model for hnRNPA1 PLD mutants, but its applicability to other systems such as TDP-43, FUS, TIA1, EWSR1, etc., may be questionable.

In the manuscript, we have leveraged existing experimental data for the A1-LCD variants, extracting critical temperatures and saturation concentrations to compare with our model and scaling law predictions. We acknowledge that a larger set of experiments would be beneficial. By selecting sequences that are related, we hypothesize that the scaling laws described herein should remain robust. In the case of TDP-43, to our knowledge this protein does not phase separate on its own under standard conditions. In vitro experiments that report phase separation at/above 300 K involve either the use of crowding agents (such as dextran or PEG) or multicomponent mixtures that include RNA or other proteins. Therefore, our predictions for TDP-43 are consistent with experiments. In general, we hope that the scaling laws presented in our work will inspire other researchers to further test their validity.

The authors may wish to consider checking if the scaling behavior is only observed for Tc or if other experimentally relevant quantities such as Csat also show similar behavior. Additionally, providing more intuitive explanations could make the findings more broadly accessible.

In Figure 2C and D we compare experimental C_sat values with our predicted T_c from simulations. These quantities are roughly inversely proportional to each other and so we expect that, to a first approximation, the relationships recovered for T_c should hold when considering C_sat at a fixed temperature.

The study focuses on a particular subset of intrinsically disordered regions. While this is necessary for depth, it may limit the applicability of the findings to other types of phase-separating biomolecules. The authors may wish to discuss why this is not a concern. Some statements in the paper may require careful evaluation for general applicability, and I encourage the authors to exercise caution while making general conclusions. For example, “Therefore, our results reveal that it is almost twice more destabilizing to mutate Arg to Lys than to replace Arg with any uncharged, non-aromatic amino acid...” This may not be true if the protein has a lot of negative charges.

A significant number of proteins, in addition to those mentioned in the manuscript, that contain prion-like low complexity domains have been reported to exhibit phase separation behaviors and/or are constituents of condensates inside cells. We therefore expect these laws to be applicable to such systems and have further revised the text to emphasize this point. As the reviewer suggests, we have also clarified that the reported scaling of various mutations applies to these systems.

I am surprised that a quarter of a million CPU hours are described as staggering in terms of computational requirements.

We have removed the note on CPU hours from the manuscript. However, we would like to clarify that the amount of CPU hours was incorrectly reported. The correct estimate is 1.25 million hours, but this value was unfortunately misrepresented during the editing process. We thank the reviewer for catching this mistake on our part.

Reviewer # 1 (Recommendations For The Authors):

Some minor points here:

“illustrating that IDPs indeed behave like a polymer in a good solvent [43]. ” Whether or not an IDP depends as a polymer in a good solvent depends on the amino acid sequence - the referenced paper selected a set of sequences that do indeed appear on average to map to a good-solvent-like polymer, but lest we forget SAXS experiments require high protein concentrations and until the recent advent of SEC-SAXS, your protein essentially needed to be near infinitely soluble to be measured. As such, this paper’s conclusions are, apparently, ignorant of the limitations associated with the data they are describing, drawing sweeping generalizations that are clearly not supported by a multitude of studies in which sequence-dependencies have led to ensembles with a scaling exponent far below 0.59 (See Riback et al 2017, Peng et al 2019, Martin et al 2020, etc).

We thank the reviewer for raising this point. To avoid making incorrect generalizations and potentially misleading readers, we have removed the quoted statement from our manuscript.

As of right now, the sequences are provided in a convenient multiple-sequence alignment figure. However, it would be important also to provide all sequences in an Excel table to make it easy for folks to compare.

In addition to the sequence alignment figure, we now provide all tested sequences in an Excel table format in the GitHub repository.

Maybe I’m missing it, but it would be extremely valuable if the coexistence points plot in all the figures were provided as so-called source data; this could just be on the GitHub repository, but I’m envisaging a scenario where for each sequence you have a 4 column file where Col1=concentration and Col2=temperature, col3=fit concentration and col4=fit temperature, such that someone could plot col1 vs. col2 and col3 vs. col4 and reproduce the binodals in the various figures. Given the tremendous amount of work done to achieve binodals:

The coexistence points used to plot the figures are now provided in the GitHub, in a format similar to that suggested by the reviewer.

It would be nice to visually show how finite size effects are considered/tested for (which they are very nicely) because I think this is something the simulation field should be thinking about more than they are.

Thank you for highlighting this point. In our previous work (supporting information of the original Mpipi paper), we demonstrated a thorough approach by varying both the cross-sectional area of the box and the long axis while keeping the overall density constant. In this work, we verified that the cross-sectional area was larger than the average R_g of the protein. We then maintained a fixed cross-sectional area to long-axis ratio, varying the number of proteins while keeping the overall density constant. We have updated Appendix 1–Figure 2 to clarify our procedure and revised the caption to better explain how we ensured the number of proteins was adequate.

When explaining the law of reticular diameters, it would be good to explain where the 3.06 exponent comes from.

Based on the reviewer’s suggestion, we have added to the text: “The constant 3.06 in the equation is a dimensionless empirical factor that was derived from simulations of the 3D Ising model.”

The NCPR scale in Figure 5 being viridis is not super intuitive and may benefit from being seismic or some other r-w-b colormap just to make it easier for a reader to map the color to meaning.

We thank the reviewer for this suggestion and have replaced the scale with a r-w-b colormap.

The “sticker and spacer” framework has received critiques recently given its perceived simplicity. However, this work seems to clearly illustrate that certain types of residues have a large effect on Tc when mutated, whereas others have a smaller effect. It may be worth re-phrasing the sticker-spacer introduction not as “everyone knows aromatic/arginine residues are stickers” but as “aromatic and arginine residues have been proposed to be stickers, yet other groups have argued all residues matter equally” and then go on to make the point that while a black-and-white delineation is probably not appropriate, based on the data, certain residues ARE demonstrably more impactful on Tc than others, which is the definition of stickers. With this in mind, it may be useful to separate out a sticker and a spacer distribution in Figure 1D, because the different distribution between the two residues types is not particularly obvious from the overlapping points.

We have revised the introduction of the sticker–spacer model in the manuscript for clarity. As the reviewer suggests, we have also separated the sticker and spacer distribution, which is now summarized in new Appendix 0–figure 8.

Reviewer # 3 (Recommendations For The Authors):

Figure 2 clearly highlights the quantitative accuracy of the model for hnRNPA1 PLD mutants, but its applicability to other systems such as TDP-43, FUS, TIA1, EWSR1, etc., may be questionable. The following sentence may be revised to reflect this: “Our extended validation set confirms that the Mpipi potential can ...”

Based on the reviewer’s suggestion, we have revised the text: “Our validation set, which expands the range of proteins variants originally tested [32], highlights that the Mpipi potential can effectively capture the thermodynamic behavior of a wide range of hnRNPA1-PLD variants, and suggests that Mpipi is adequate for proteins with similar sequence compositions, as in the set of proteins analyzed in this study. In recent work by others [66], Mpipi was tested against experimental radius of gyration data for 137 disordered proteins and the model produced highly accurate results, which further suggests the applicability of the approach to a broad range of sequences.”

Author response:

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

Reviewer #1 (Public review):

As a starting point, the authors discuss the so-called "additive partitioning" (AP) method proposed by Loreau & Hector in 2001. The AP is the result of a mathematical rearrangement of the definition of overyielding, written in terms of relative yields (RY) of species in mixtures relative to monocultures. One term, the so-called complementarity effect (CE), is proportional to the average RY deviations from the null expectations that plants of both species "do the same" in monocultures and mixtures. The other term, the selection effect (SE), captures how these RY deviations are related to monoculture productivity. Overall, CE measures whether relative biomass gains differ from zero when averaged across all community members, and SE, whether the "relative advantage" species have in the mixture, is related to their productivity. In extreme cases, when all species benefit, CE becomes positive.

This is not true; positive CE does not require positive RY deviations of all species. CE is positive as long as average RY deviation is greater than 0. In a 2-species mixture, for example, if the RY deviation of one species is -0.2 and that of the other species is +0.3, CE would be still positive. Positive CE can be associated with negative NE (net biodiversity effects) when more productivity species have smaller negative RY deviation compared to positive RY deviation of less productive species. Therefore, the suggestion by the reviewer “This is intuitively compatible with the idea that niche complementarity mitigates competition (CE>0)” is not correct.   

When large species have large relative productivity increases, SE becomes positive. This is intuitively compatible with the idea that niche complementarity mitigates competition (CE>0), or that competitively superior species dominate mixtures and thereby driver overyielding (SE>0).

The use of word “mitigate” indicates that the effects of niche complementarity and competition are in opposite directions, which is not true with biodiversity experiments based on replacement design. We have explained this in detail in our first responses to reviewers.    

However, it is very important to understand that CE and SE capture the "statistical structure" of RY that underlies overyielding. Specifically, CE and SE are not the ultimate biological mechanisms that drive overyielding, and never were meant to be. CE also does not describe niche complementarity. Interpreting CE and SE as directly quantifying niche complementarity or resource competition, is simply wrong, although it sometimes is done. The criticism of the AP method thus in large part seems unwarranted. The alternative methods the authors discuss (lines 108-123) are based on very similar principles.

Agree. However, If CE and SE are not meant to be biological mechanisms, as suggested by the reviewer, the argument “This is intuitively compatible with the idea that niche complementarity mitigates competition (CE>0), or that competitively superior species dominate mixtures and thereby driver overyielding (SE>0)” would be invalid.  

Lines 108-123 are not on our method.   

The authors now set out to develop a method that aims at linking response patterns to "more true" biological mechanisms.

Assuming that "competitive dominance" is key to understanding mixture productivity, because "competitive interactions are the predominant type of interspecific relationships in plants", the authors introduce "partial density" monocultures, i.e. monocultures that have the same planting density for a species as in a mixture. The idea is that using these partial density monocultures as a reference would allow for isolating the effect of competition by the surrounding "species matrix".

The authors argue that "To separate effects of competitive interactions from those of other species interactions, we would need the hypothesis that constituent species share an identical niche but differ in growth and competitive ability (i.e., absence of positive/negative interactions)." - I think the term interaction is not correctly used here, because clearly competition is an interaction, but the point made here is that this would be a zero-sum game.

We did not say that competition is not an interaction.

The authors use the ratio of productivity of partial density and full-density monocultures, divided by planting density, as a measure of "competitive growth response" (abbreviated as MG). This is the extra growth a plant individual produces when intraspecific competition is reduced.

Here, I see two issues: first, this rests on the assumption that there is only "one mode" of competition if two species use the same resources, which may not be true, because intraspecific and interspecific competition may differ. Of course, one can argue that then somehow "niches" are different, but such a niche definition would be very broad and go beyond the "resource set" perspective the authors adopt. Second, this value will heavily depend on timing and the relationship between maximum initial growth rates and competitive abilities at high stand densities.

True. Research findings indicate that biodiversity effect detected with AP is not constant.    

The authors then progress to define relative competitive ability (RC), and this time simply uses monoculture biomass as a measure of competitive ability. To express this biomass in a standardized way, they express it as different from the mean of the other species and then divide by the maximum monoculture biomass of all species.

I have two concerns here: first, if competitive ability is the capability of a species to preempt resources from a pool also accessed by another species, as the authors argued before, then this seems wrong because one would expect that a species can simply be more productive because it has a broader niche space that it exploits. This contradicts the very narrow perspective on competitive ability the authors have adopted. This also is difficult to reconcile with the idea that specialist species with a narrow niche would outcompete generalist species with a broad niche.

Competitive ability is not necessarily associated with species niche space. Both generalist and specialist species can be more productive at a particular study site, as long as they are more capable of obtaining resources from a local pool. Remember, biodiversity experiments are conducted at a site of particular conditions, not across a range of species niche space at landscape level.

Second, I am concerned by the mathematical form. Standardizing by the maximum makes the scaling dependent on a single value.

As explained in lines 370-376, the mathematical form is a linear approximation as the relationship between competitive growth responses and species relative competitive ability is generally unknow but would be likely nonlinear. Once the relationship is determined in future research, the scaling factor is not needed.    

As a final step, the authors calculate a "competitive expectation" for a species' biomass in the mixture, by scaling deviations from the expected yield by the product MG ⨯ RC. This would mean a species does better in a mixture when (1) it benefits most from a conspecific density reduction, and (2) has a relatively high biomass.

Put simply, the assumption would be that if a species is productive in monoculture (high RC), it effectively does not "see" the competitors and then grows like it would be the sole species in the community, i.e. like in the partial density monoculture.

Overall, I am not very convinced by the proposed method.

Comments on revised version:

Only minimal changes were made to the manuscript, and they do not address the main points that were raised.

Reviewer #2 (Public review):

This manuscript by Tao et al. reports on an effort to better specify the underlying interactions driving the effects of biodiversity on productivity in biodiversity experiments. The authors are especially concerned with the potential for competitive interactions to drive positive biodiversity-ecosystem functioning relationships by driving down the biomass of subdominant species. The authors suggest a new partitioning schema that utilizes a suite of partial density treatments to capture so-called competitive ability. While I agree with the authors that understanding the underlying drivers of biodiversity-ecosystem functioning relationships is valuable - I am unsure of the added value of this specific approach for several reasons.

No responses.

Comments on revised version:

The authors changed only one minor detail in response to the last round of reviews.

Reviewer #3 (Public review):

Summary:

This manuscript claims to provide a new null hypothesis for testing the effects of biodiversity on ecosystem functioning. It reports that the strength of biodiversity effects changes when this different null hypothesis is used. This main result is rather inevitable. That is, one expects a different answer when using a different approach. The question then becomes whether the manuscript's null hypothesis is both new and an improvement on the null hypothesis that has been in use in recent decades.

Our approach adopts two hypotheses, null hypothesis that is also with the additive partitioning model and competitive hypothesis that is new. Null hypothesis assumes that inter- and intra-specie interactions are the same, while competitive hypothesis assumes that species differ in competitive ability and growth rate. Therefore, our approach is an extension of current approach. Our approach separates effects of competitive interactions from those of other species interactions, while the current approach does not.      

Strengths:

In general, I appreciate studies like this that question whether we have been doing it all wrong and I encourage consideration of new approaches.

Weaknesses:

Despite many sweeping critiques of previous studies and bold claims of novelty made throughout the manuscript, I was unable to find new insights. The manuscript fails to place the study in the context of the long history of literature on competition and biodiversity and ecosystem functioning.

We have explained in our first responses that competition and biodiversity effects are studied in different experimental approaches, i.e., additive and replacement designs. Results from one approach are not compatible with those from the other. For example, competition effect with additive design is negative but generally positive with replacement design that is used extensively in biodiversity experiments. We have considered species competitive ability, density-growth relationship, and different effects of competitive interactions between additive and replacement design, while the current method does not reflect any of those.        

The Introduction claims the new approach will address deficiencies of previous approaches, but after reading further I see no evidence that it addresses the limitations of previous approaches noted in the Introduction. Furthermore, the manuscript does not reproducibly describe the methods used to produce the results (e.g., in Table 1) and relies on simulations, claiming experimental data are not available when many experiments have already tested these ideas and not found support for them.

We used simulation data, as partial density monocultures are generally not available in previous biodiversity experiments.

Finally, it is unclear to me whether rejecting the 'new' null hypothesis presented in the manuscript would be of interest to ecologists, agronomists, conservationists, or others.

Our null hypothesis is the same as the null hypothesis with the additive partitioning assuming that inter- and intra-species interactions are the same, while our competitive hypothesis assumes that species differ in competitive ability and growth rate. Rejecting null hypothesis means that inter- and intra-species interactions are different, whereas rejecting competitive hypothesis indicates existence of positive/negative species interactions. This would be interesting to everyone.       

Comments on revised version:

Please see review comments on the previous version of this manuscript. The authors have not revised their manuscript to address most of the issues previously raised by reviewers.

No responses.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Do take reviews seriously. Even if you think the reviewers all are wrong and did not understand your work, then this seems to indicate that it was not clearly presented.

Reviewer #2 (Recommendations for the authors):

I can understand that the authors are perhaps frustrated with what they perceive as a basic misunderstanding of their goals and approach. This misunderstanding however, provides with it an opportunity to clarify. I believe that the authors have tried to clarify in rebutting our statements but would do better to clarify in the manuscript itself. If we reviewers, who are deeply invested in this field, don't understand the approach and its value, then it is likely that many readers will not as well.

The additive partitioning has been publicly questioned at least for serval times since the conception of the method in 2001. Our work provides an alternative.

Reviewer #2 (Public review):

Summary:

The authors present a paper that attempts to tackle an important question, with potential impact far beyond the field of animal behavior research: what are the relative contributions of innate personality traits versus early life experience on individual behavior in the wild? The study, performed on Egyptian fruit bats that are caught in the wild and later housed in an outdoor colony, is solidly executed, and benefits greatly from a unique setup in which controlled laboratory experiments are combined with monitoring of individuals as they undertake undirected, free exploration of their natural environment.

The primary finding of the paper is that there is a strong effect of early life experience on behavior in the wild, where individual bats that were exposed to an enriched environment as juveniles later travelled farther and over greater distances when permitted to explore and forage ad libitum, as compared with individual bats who were subjected to a more impoverished environment. Meanwhile, no prominent effect of innate "personality", as assessed by indices of indoor foraging behavior early on, before the bats were exposed to the controlled environmental treatment, was observed on three metrics of outdoor foraging behavior. The authors conclude that the early environment plays a larger role than innate personality on the behavior of adult bats.

Strengths:

(1) Elegant design of experiments and impressive combination of methods<br /> Bats used in the experiment were taken from wild colonies in different geographical areas, but housed during the juvenile stage in a controlled indoor environment. Bats are tested on the same behavioral paradigm at multiple points in their development. Finally, the bats are monitored with GPS as they freely explore the area beyond the outdoor colony.

(2) Development of a behavioral test that yields consistent results across time<br /> The multiple-foraging box paradigm, in which behavioral traits such as overall activity, levels of risk-taking, and exploratoriness can be evaluated as creative, and suggestive of behavioral paradigms other animal behavior researchers might be able to use. It is especially useful, given that it can be used to evaluate the activity of animals seemingly at most stages of life, and not just in adulthood.

Weaknesses:

(1) Robustness and validity of personality measures<br /> Coming up with robust measures of "personality" in non-human animals is tricky. While this paper represents an important attempt at a solution, some of the results obtained from the indoor foraging paradigm raise questions as to the reliability of this task for assessing "personality".

(2) Insufficient exploitation of data<br /> Between the behavioral measures and the very multidimensional GPS data, the authors are in possession of a rich data set. However, I don't feel that this data has been adequately exploited for underlying patterns and relationships. For example, many more metrics could be extracted from the GPS data, which may then reveal correlations with early measures of personality or further underscore the role of the early environment. In addition, the possibility that these personality measures might in combination affect outdoor foraging is not explored.

(3) Interpretation of statistical results and definition of statistical models<br /> Some statistical interpretations may not be entirely accurate, particularly in the case of multiple regression with generalized linear models. In addition, some effects which may be present in the data are dismissed as not significant on the basis of null hypothesis testing.

Below I have organized the main points of critique by theme, and ordered subordinate points by order of importance:

(1) Assessing personality metrics and the indoor paradigm: While I applaud this effort and think the metrics used are justified, I see a few issues in the results as they are currently presented:<br /> (a) [Major] I am somewhat concerned that here, the foraging box paradigm is being used for two somewhat conflicting purposes: (1) assessing innate personality and (2) measuring changes in personality as a result of experience. If the indoor foraging task is indeed meant to measure and reflect both at the same time, then perhaps this can be made more explicit throughout the manuscript. In this circumstance, I think the authors could place more emphasis on the fact that the task, at later trials/measurements, begins to take on the character of a "composite" measure of personality and experience.

(b) [Major] Although you only refer to results obtained in trials 1 and 2 when trying to estimate "innate personality" effects, I am a little worried that the paradigm used to measure personality, i.e. the stable components of behavior, is itself affected by other factors such as age (in the case of activity, Fig. 1C3, S1C1-2), the environment (see data re trial 3), and experience outdoors (see data re trials 4/5).

Ideally, a study that aims to disentangle the role of predisposition from early-life experience would have a metric for predisposition that is relatively unchanging for individuals, which can stand as a baseline against a separate metric that reflects behavioral differences accumulated as a result of experience.

I would find it more convincing that the foraging box paradigm can be used to measure personality if it could be shown that young bats' behavior was consistent across retests in the box paradigm prior to any environmental exposure across many baseline trials (i.e. more than 2), and that these "initial settings" were constant for individuals. I think it would be important to show that personality is consistent across baseline trials 1 and 2. This could be done, for example, by reproducing the plots in Fig. 1C1-3 while plotting trial 1 against trial 2. (I would note here that if a significant, positive correlation were to be found (as I would expect) between the measures across trial 1 and 2, it is likely that we would see the "habituation effect" the authors refer to expressed as a steep positive slope on the correlation line (indicating that bold individuals on trial 1 are much bolder on trial 2).)

(c) Related to the previous point, it was not clear to me why the data from trial 2 (the second baseline trial) was not presented in the main body of the paper, and only data from trial 1 was used as a baseline.

In the supplementary figure and table, you show that the bats tended to exhibit more boldness and exploratory behavior, but fewer actions, in trial 2 as compared with trial 1. You explain that this may be due to habituation to the experimental setup, however, the precise motivation for excluding data from trial 2 from the primary analyses is not stated. I would strongly encourage the authors to include a comparison of the data between the baseline trials in their primary analysis (see above), combine the information from these trials to form a composite baseline against which further analyses are performed, or further justify the exclusion of data as a baseline.

(2) Comparison of indoor behavioral measures and outdoor behavioral measures<br /> Regarding the final point in the results, correlation between indoor personality on Trial 4 and outdoor foraging behavior: It is not entirely clear to me what is being tested (neither the details of the tests nor the data or a figure are plotted). Given some of the strong trends in the data - namely, (1) how strongly early environment seems to affect outdoor behavior, (2) how strongly outdoor experience affects boldness, measured on indoor behavior (Fig. 1D) - I am not convinced that there is no relationship, as is stated here, between indoor and outdoor behavior. If this conclusion is made purely on the basis of a p-value, I would suggest revisiting this analysis.

(3) Use of statistics/points regarding the generalized linear models<br /> While I think the implementation of the GLMM models is correct, I am not certain that the interpretation of the GLMM results is entirely correct for cases where multivariate regression has been performed (Tables 4s and S1, and possibly Table 3). (You do not present the exact equation they used for each model (this would be a helpful addition to the methods), therefore it is somewhat difficult to evaluate if the following critique properly applies, however...)

The "estimate" for a fixed effect in a regression table gives the difference in the outcome variable for a 1 unit increase in the predictor variable (in the case of numeric predictors) or for each successive "level" or treatment (in the case of categorical variables), compared to the baseline, the intercept, which reflects the value of the outcome variable given by the combination of the first value/level of all predictors. Therefore, for example, in Table 4a - Time spend outside: the estimate for Bat sex: male indicates (I believe) the difference in time spent outside for an enriched male vs. an enriched female, not, as the authors seem to aim to explain, the effect of sex overall. Note that the interpretation of the first entry, Environmental condition: impoverished, is correct. I refer the authors to the section "Multiple treatments and interactions" on p. 11 of this guide to evaluating contrasts in G/LMMS: https://bbolker.github.io/mixedmodels-misc/notes/contrasts.pdf

Author response:

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

Public Reviews:

Reviewer #1 (Public Review): 

Summary: 

The authors introduced their previous paper with the concise statement that "the relationships between lineage-specific attributes and genotypic differences of tumors are not understood" (Chen et al., JEM 2019, PMID: 30737256). For example, it is not clear why combined loss of RB1 and TP53 is required for tumorigenesis in SCLC or other aggressive neuroendocrine (NE) cancers, or why the oncogenic mutations in KRAS or EGFR that drive NSCLC tumorigenesis are found so infrequently in SCLC. This is the main question addressed by the previous and current papers. 

One approach to this question is to identify a discrete set of genetic/biochemical manipulations that are sufficient to transform non-malignant human cells into SCLC-like tumors. One group reported the transformation of primary human bronchial epithelial cells into NE tumors through a complex lentiviral cocktail involving the inactivation of pRB and p53 and activation of AKT, cMYC, and BCL2 (PARCB) (Park et al., Science 2018, PMID: 30287662). The cocktail previously reported by Chen and colleagues to transform human pluripotent stem-cell (hPSC)-derived lung progenitors (LPs) into NE xenografts was more concise: DAPT to inactivate NOTCH signaling combined with shRNAs against RB1 and TP53. However, the resulting RP xenografts lacked important characteristics of SCLC. Unlike SCLC, these tumors proliferated slowly and did not metastasize, and although small subpopulations expressed MYC or MYCL, none expressed NEUROD1. 

MYC is frequently amplified or expressed at high levels in SCLC, and here, the authors have tested whether inducible expression of MYC could increase the resemblance of their hPSC-derived NE tumors to SCLC. These RPM cells (or RPM T58A with stabilized cMYC) engrafted more consistently and grew more rapidly than RP cells, and unlike RP cells, formed liver metastases when injected into the renal capsule. Gene expression analyses revealed that RPM tumor subpopulations expressed NEUROD1, ASCL1, and/or YAP1. 

The hPSC-derived RPM model is a major advance over the previous RP model. This may become a powerful tool for understanding SCLC tumorigenesis and progression and for discovering gene dependencies and molecular targets for novel therapies. However, the specific role of cMYC in this model needs to be clarified. 

cMYC can drive proliferation, tumorigenesis, or apoptosis in a variety of lineages depending on concurrent mutations. For example, in the Park et al., study, normal human prostate cells could be reprogrammed to form adenocarcinoma-like tumors by activation of cMYC and AKT alone, without manipulation of TP53 or RB1. In their previous manuscript, the authors carefully showed the role of each molecular manipulation in NE tumorigenesis. DAPT was required for NE differentiation of LPs to PNECs, shRB1 was required for expansion of the PNECs, and shTP53 was required for xenograft formation. cMYC expression could influence each of these steps, and importantly, could render some steps dispensable. For example, shRB1 was previously necessary to expand the DAPT-induced PNECs, as neither shTP53 nor activation of KRAS or EGFR had no effect on this population, but perhaps cMYC overexpression could expand PNECs even in the presence of pRB, or even induce LPs to become PNECs without DAPT. Similarly, both shRB1 and shTP53 were necessary for xenograft formation, but maybe not if cMYC is overexpressed. If a molecular hallmark of SCLC, such as loss of RB1 or TP53, has become dispensable with the addition of cMYC, this information is critically important in interpreting this as a model of SCLC tumorigenesis.  

The reviewer’s suggestion may be possible; indeed, in a recent report from our group (Gardner EE, et al., Science 2024) we have shown, using genetically engineered mouse modeling coupled with lineage tracing, that the cMyc oncogene can selectively expand Ascl1+ PNECs in the lung.

We agree with the reviewer that not having a better understanding of the individual components necessary and/or sufficient to transform hESC-derived LPs is an important shortcoming of this current work. However, we would like to stress three important points about the comments:  1) tumors were reviewed and the histological diagnoses were certified by a practicing pulmonary pathologist at WCM (our co-author, C. Zhang); 2 )the observed  transcriptional programs were consistent with primary human SCLC; and 3) RB1-proficient SCLC is now recognized as a rare presentation of SCLC (Febrese-Aldana CA, et al., Clin. Can. Res. 2022. PMID: 35792876).

To interpret the role of cMYC expression in hPSC-derived RPM tumors, we need to know what this manipulation does without manipulation of pRB, p53, or NOTCH, alone or in combination. Seven relevant combinations should be presented in this manuscript: (1) cMYC alone in LPs, (2) cMYC + DAPT, (3) cMYC + shRB1, (4) cMYC + DAPT + shRB1, (5) cMYC + shTP53, (6) cMYC + DAPT + shTP53, and (7) cMYC + shRB1 + shTP53. Wildtype cMYC is sufficient; further exploration with the T58A mutant would not be necessary. 

We respectfully disagree that an interrogation of the differences between the phenotypes produced by wildtype and Myc(T58A) would not be informative. (Our view is confirmed by the second reviewer; see below.)    It is well established that Myc gene or protein dosage can have profound effects on in vivo phenotypes (Murphy DJ, et al., Cancer Cell 2008. PMID: 19061836). The “RPM” model of variant SCLC developed by Trudy Oliver’s lab relied on the conditional T58A point mutant of cMyc, originally made by Rob Wechsler-Reya. While we do not discuss the differences between Myc and Myc(T58A), it is nonetheless important to present our results with both the WT and mutant MYC constructs, as we are aware of others actively investigating differences between them in GEMM models of SCLC tumor development.

We agree with the reviewer about the virtues of trying to identify the effects of individual gene manipulations; indeed our original paper (Chen et al., J. Expt. Med. 2019), describing the RUES2derived model of SCLC did just that, carefully dissecting events required to transform LPs towards a SCLC-like state. The central  purpose of the current study was to determine the effects of adding cMyc on the behavior of weakly tumorigenic SCLC-like cells cMyc.  Presenting data with these two alleles to seek effects of different doses of MYC protein seems reasonable.

This reviewer considers that there should be a presentation of the effects of these combinations on LP differentiation to PNECs, expansion of PNECs as well as other lung cells, xenograft formation and histology, and xenograft growth rate and capacity for metastasis. If this could be clarified experimentally, and the results discussed in the context of other similar approaches such as the Park et al., paper, this study would be a major addition to the field.  

Reviewer #2 (Public Review): 

Summary: 

Chen et al use human embryonic stem cells (ESCs) to determine the impact of wildtype MYC and a point mutant stable form of MYC (MYC-T58A) in the transformation of induced pulmonary neuroendocrine cells (PNEC) in the context of RB1/P53 (RP) loss (tumor suppressors that are nearly universally lost in small cell lung cancer (SCLC)). Upon transplant into immune-deficient mice, they find that RP-MYC and RP-MYC-T58A cells grow more rapidly, and are more likely to be metastatic when transplanted into the kidney capsule, than RP controls. Through single-cell RNA sequencing and immunostaining approaches, they find that these RPM tumors and their metastases express NEUROD1, which is a transcription factor whose expression marks a distinct molecular state of SCLC. While MYC is already known to promote aggressive NEUROD1+ SCLC in other models, these data demonstrate its capacity in a human setting that provides a rationale for further use of the ESC-based model going forward. Overall, these findings provide a minor advance over the previous characterization of this ESC-based model of SCLC published in Chen et al, J Exp Med, 2019. 

We consider the findings more than a “minor” advance in the development of the model, since any useful model for SCLC would need to form aggressive and metastatic tumors.

The major conclusion of the paper is generally well supported, but some minor conclusions are inadequate and require important controls and more careful analysis. 

Strengths:

(1) Both MYC and MYC-T58A yield similar results when RP-MYC and RP-MYCT58A PNEC ESCs are injected subcutaneously, or into the renal capsule, of immune-deficient mice, leading to the conclusion that MYC promotes faster growth and more metastases than RP controls. 

(2) Consistent with numerous prior studies in mice with a neuroendocrine (NE) cell of origin (Mollaoglu et al, Cancer Cell, 2017; Ireland et al, Cancer Cell, 2020; Olsen et al, Genes Dev, 2021), MYC appears sufficient in the context of RB/P53 loss to induce the NEUROD1 state. Prior studies also show that MYC can convert human ASCL1+ neuroendocrine SCLC cell lines to a NEUROD1 state (Patel et al, Sci Advances, 2021); this study for the first time demonstrates that RB/P53/MYC from a human neuroendocrine cell of origin is sufficient to transform a NE state to aggressive NEUROD1+ SCLC. This finding provides a solid rationale for using the human ESC system to better understand the function of human oncogenes and tumor suppressors from a neuroendocrine origin. 

Weaknesses:

(1) There is a major concern about the conclusion that MYC "yields a larger neuroendocrine compartment" related to Figures 4C and 4G, which is inadequately supported and likely inaccurate. There is overwhelming published data that while MYC can promote NEUROD1, it also tends to correlate with reduced ASCL1 and reduced NE fate (Mollaoglu et al, Cancer Cell, 2017; Zhang et al, TLCR, 2018; Ireland et al, Cancer Cell, 2020; Patel et al, Sci Advances, 2021). Most importantly, there is a lack of in vivo RP tumor controls to make the proper comparison to judge MYC's impact on neuroendocrine identity. RPM tumors are largely neuroendocrine compared to in vitro conditions, but since RP control tumors (in vivo) are missing, it is impossible to determine whether MYC promotes more or less neuroendocrine fate than RP controls. It is not appropriate to compare RPM tumors to in vitro RP cells when it comes to cell fate. Upon inspection of the sample identity in S1B, the fibroblast and basal-like cells appear to only grow in vitro and are not well represented in vivo; it is, therefore, unclear whether these are transformed or even lack RB/P53 or express MYC. Indeed, a close inspection of Figure S1B shows that RPM tumor cells have little ASCL1 expression, consistent with lower NE fate than expected in control RP tumors. 

We would like to clarify two points related to the conclusions that we draw about MYC’s ability to promote an increase in the neuroendocrine fraction in hESC-derived cultures:  1) The comparisons in Figures 4C were made between cells isolated in culture following the standard 50 day differentiation protocol, where, following generation of LPs around day 25, MYC was added to the other factors previously shown to enrich for a PNEC phenotype (shRB1, shTP53, and DAPT). Therefore, the argument that MYC increased the frequency of “neuroendocrine cells” (which we define by a gene expression signature) is a reasonable conclusion in the system we are using; and 2) following injection of these cells into immunocompromised mice, an ASCL1-low / NEUROD1-high presentation is noted (Supplemental Figures 1F-G). In the few metastases that we were able use to sequence bulk RNA, there is an even more pronounced increase in expression of NEUROD1 with a decrease in ASCL1.

Some confusion may have arisen from our previous characterization of neuroendocrine (NE) cells using either ASCL1 or NEUROD1 as markers. To clarify, we have now designated cells positive for ASCL1 as classical NE cells and those positive for NEUROD1 as the NE variant. According to this revised classification, our findings indicate that MYC expression leads to an increase in the NEUROD1+ NE variant and a decrease in ASCL1+ classical NE cells. This adjustment has been reflected on the results section titled, “Inoculation of the renal capsule facilitates metastasis of the RUES2-derived RPM tumors” of the manuscript.  

From the limited samples in hand, we compared the expression of ASCL1 and NEUROD1 in the weakly tumorigenic hESC RP cells after successful primary engraftment into immunocompromised mice. As expected, the RP tumors were distinguished by the lack of expression of NEUROD1, compared to levels observed in the RPM tumors.

In addition, since MYC appears to require Notch signaling to induce  NE fate (cf Ireland et al), the presence of DAPT in culture could enrich for NE fate despite MYC's presence. It's important to clarify in the legend of Fig 4A which samples are used in the scRNA-seq data and whether they were derived from in vitro or in vivo conditions (as such, Supplementary Figure S1B should be provided in the main figure). Given their conclusion is confusing and challenges robustly supported data in other models, it is critical to resolve this issue properly. I suspect when properly resolved, MYC actually consistently does reduce NE fate compared to RP controls, even though tumors are still relatively NE compared to completely distinct cellular identities such as fibroblasts.

We have clarified the source of tumor sequencing data and the platform (single cell or bulk) in Figure 4 and Supplemental Figure 1. To reiterate – the RNA sequencing results from paired metastatic and primary tumors from the RPM model are derived from bulk RNA;  the single cell RNA data in RP or RPM datasets are from cells in culture.  These distinctions are clarified in the legend to Supplemental Figure 1.

(2) The rigor of the conclusions in Figure 1 would be strengthened by comparing an equivalent number of RP animals in the renal capsule assay, which is n = 6 compared to n = 11-14 in the MYC conditions.

As we did not perform a power calculation to determine a sample size required to draw a level of statistical significance from our conclusions, this comment is not entirely accurate. Our statistical rigor was limited by the availability of samples from the RP tumor model.

(3) Statistical analysis is not provided for Figures 2A-2B, and while the results are compelling, may be strengthened by additional samples due to the variability observed. 

We acknowledge that the cohorts are relatively small but we have added statistical comparisons in Figure 2B. 

(4a) Related to Figure 3, primary tumors and liver metastases from RPM or RPM-T58A-expressing cells express NEUROD1 by immunohistochemistry (IHC) but the putative negative controls (RP) are not shown, and there is no assessment of variability from tumor to tumor, ie, this is not quantified across multiple animals. 

The results of H&E and IF staining for ASCL1, NEUROD1, CGRP, and CD56 in negative control (RP tumors) are presented in the updated Figure 3F-G.

(4b) Relatedly, MYC has been shown to be able to push cells beyond NEUROD1 to a double-negative or YAP1+ state (Mollaoglu et al, Cancer Cell, 2017; Ireland et al, Cancer Cell, 2020), but the authors do not assess subtype markers by IHC. They do show subtype markers by mRNA levels in Fig 4B, and since there is expression of ASCL1, and potentially expression of YAP1 and POU2F3, it would be valuable to examine the protein levels by IHC in control RP vs. RPM samples.

YAP1 positive SCLC is still somewhat controversial, so it is not clear what value staining for YAP1 offers beyond showing the well-established markers, ASCL1 and NEUROD1.  

(5) Given that MYC has been shown to function distinctly from MYCL in SCLC models, it would have raised the impact and value of the study if MYC was compared to MYCL or MYCL fusions in this context since generally, SCLC expresses a MYC family member. However, it is quite possible that the control RP cells do express MYCL, and as such, it would be useful to show. 

We now include Supplemental Figure S2 to illustrate four important points raised by this reviewer and others:  1) expression of MYC family members in the merged dataset (RP and RPM) is low or undetectable in the basal/fibroblast cultures; 2) MYC does have a weak correlation with EGFP in the neuroendocrine cluster when either WT MYC or T58A MYC is overexpressed; 3) MYCL and MYCN are detectable, but at low levels compared to CMYC; and 4) Expression of  ASCL1 is anticorrelated with MYC expression across the merged single cell datasets using RP and RPM models.

Reviewer #3 (Public Review): 

Summary: 

The authors continue their study of the experimental model of small cell lung cancer (SCLC) they created from human embryonic stem cells (hESCs) using a protocol for differentiating the hESCs into pulmonary lineages followed by NOTCH signaling inactivation with DAPT, and then knockdown of TP53 and RB1 (RP models) with DOX inducible shRNAs. To this published model, they now add DOX-controlled activation of expression of a MYC or T58A MYC transgenes (RPM and RPMT58A models) and study the impact of this on xenograft tumor growth and metastases. Their major findings are that the addition of MYC increased dramatically subcutaneous tumor growth and also the growth of tumors implanted into the renal capsule. In addition, they only found liver and occasional lung metastases with renal capsule implantation. Molecular studies including scRNAseq showed that tumor lines with MYC or T58A MYC led surprisingly to more neuroendocrine differentiation, and (not surprisingly) that MYC expression was most highly correlated with NEUROD1 expression. Of interest, many of the hESCs with RPM/RPMT58A expressed ASCL1. Of note, even in the renal capsule RPM/RPMT58A models only 6/12 and 4/9 mice developed metastases (mainly liver with one lung metastasis) and a few mice of each type did not even develop a renal sub capsule tumor. The authors start their Discussion by concluding: " In this report, we show that the addition of an efficiently expressed transgene encoding normal or mutant human cMYC can convert weakly tumorigenic human PNEC cells, derived from a human ESC line and depleted of tumor suppressors RB1 and TP53, into highly malignant, metastatic SCLC-like cancers after implantation into the renal capsule of immunodeficient mice.". 

Strengths: 

The in vivo study of a human preclinical model of SCLC demonstrates the important role of c-Myc in the development of a malignant phenotype and metastases. Also the role of c-Myc in selecting for expression of NEUROD1 lineage oncogene expression. 

Weaknesses: 

There are no data on results from an orthotopic (pulmonary) implantation on generation of metastases; no comparative study of other myc family members (MYCL, MYCN); no indication of analyses of other common metastatic sites found in SCLC (e.g. brain, adrenal gland, lymph nodes, bone marrow); no studies of response to standard platin-etoposide doublet chemotherapy; no data on the status of NEUROD1 and ASCL1 expression in the individual metastatic lesions they identified. 

We have acknowledged from the outset that our study has significant limitations, as noted by this reviewer, and we explained in our initial letter of response why we need to present this limited, but still consequential, story at this time. 

In particular, while we have attempted orthotopic transplantations of RPM tumor cells into NSG mice (by tail vein or intra-pulmonary injection, or intra-tracheal instillation of tumor cells), these methods were not successful in colonizing the lung. Additionally, we have compared the efficacy of platinum/etoposide to that of removing DOX in established RPM subcutaneous tumors, but we chose not to include these data as we lacked a chemotherapy responsive tumor model, and thus could not say with confidence that the chemotherapeutic agants were active and that the RPM models were truly resistant to standard SCLC chemotherapy. In a discussion about other metastatic sites, we have now included the following text: 

“In animals administered DOX, histological examinations showed that approximately half developed metastases in distant organs, including the liver or lung (Figure 1D). No metastases were observed in the bone, brain, or lymph nodes. For a more detailed assessment, future studies could employ more sensitive imaging methods, such as luciferase imaging.”

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors): 

Technical points related to Major Weakness #1: 

For Figure 4: Cells were enriched for EGFP-high cells only, under the hypothesis that cells with lower EGFP may have silenced expression of the integrated vector. Since EGFP is expressed only in the shRB1 construct, selection for high EGFP may inadvertently alter/exclude heterogeneity within the transformed population for the other transgenes (shP53, shMYC/MYC-T58A). Can authors include data to show the expression of MYC/MYC T58A in EGFP-high v -med v-low cells? MYC levels may alter the NEdifferentiation status of tumor cells. 

Please now refer to Supplemental Figure S2.

Related to the appropriateness of the methods for Figure 4C, the authors state, "We performed differential cluster abundance analysis after accounting for the fraction of cells that were EGFP+". If only EGFP+ cells were accounted for in the analysis for 4C, the majority of RP cells in the "Neuroendocrine differentiated" cluster would not be included in the analysis (according to EGFP expression in Fig S1A-B), and therefore inappropriately reduce NE identity compared to RPM samples that have higher levels of EGFP. 

There is no consideration or analysis of cell cycling/proliferation until after the conclusion is stated. Yet, increased proliferation of MYC-high vs MYC-low cultures would enhance selection for more tumors (termed "NE-diff") than non-tumors (basal/fibroblast) in 2D cultures. 

The expression of MYC itself isn't assessed for this analysis but assumed, and whether higher levels of MYC/MYC-T58A may be present in EGFP+ tumor cells that are in the NE-low populations isn't clear. Can MYC-T58A/HA also be included in the reference genome? 

We did not include an HA tag in our reference transcriptome. For [some] answers to this and other related questions, please refer to Supplemental Figure S2.

Reviewer #3 (Recommendations For The Authors): 

(1) The experiments are all technically well done and clearly presented and represent a logical extension exploring the role of c-Myc in the hESC experimental model system. 

We appreciate this supportive comment!

(2) It is of great interest that both the initial RP model only forms "benign" tumors and that with the addition of a strong oncogene like c-myc, where expression is known to be associated with a very bad prognosis in SCLC, that while one gets tumor formation there are still occasional mice both for subcutaneous and renal capsule test sites that don't get tumors even with the injection of 500,000 RPM/RPMT58A cells. In addition, of the mice that do form tumors, only ~50% exhibit metastases from the renal sub-capsule site. The authors need to comment on this further in their Discussion. To me, this illustrates both how incredibly resistant/difficult it is to form metastases, thus indicating the need for other pathways to be activated to achieve such spread, and also represents an opportunity for further functional genomic tests using their preclinical model to systematically attack this problem. Obvious candidate genes are those recently identified in genetically engineered mouse models (GEMMs) related to neuronal behavior. In addition, we already know that full-fledged patient-derived SCLC when injected subcutaneously into immune-deprived mice don't exhibit metastases - thus, while the hESC RPM result is not surprising, it indicates to me the power of their model (logs less complicated genetically than a patient SCLC) to sort through a mechanism that would allow metastases to develop from subcutaneous sites. The authors can point these things out in their Discussion section to provide a "roadmap" for future research. 

Although we remain mindful of the relatively small cohorts we have studied, the thrust of Reviewer #3’s comments is now included in the Discussion. And there is, of course, a lot more to do, and it has taken several years already to get to this point. Additional information about the prolonged gestation of this project and about the difficulties of doing more in the near future was described in our initial response to reviewers/Editor, included near the start of this letter.    

(3) I will state the obvious that this paper would be much more valuable if they had compared and contrasted at least one of the myc family members (MYCL or MYCN) with the CMYC findings whatever the results would be. Most SCLC patients develop metastases, and most of their tumors don't express high levels of CMYC (and often use MYCL). In any event, as the authors Discuss, this will be an important next stage to test.

We have acknowledged and explained the limitations of the work in several ways. Further, we were unaware of the relationship between metastases and the expression of MYC and MYCL1 noted by the reviewer; we will look for confirmation of this association in any future studies, although we have not encountered it in current literature.

(4) Their assays for metastases involved looking for anatomically "gross" lesions. While that is fine, particularly given that the "gross" lesions they show in figures are actually pretty small, we still need to know if they performed straightforward autopsies on mice and looked for other well-known sites of metastases in SCLC patients besides liver and lung - namely lymph nodes, adrenal, bone marrow, and brain. I would guess these would probably not show metastatic growth but with the current report, we don't know if these were looked for or not. Again, while this could be a "negative" result, the paper's value would be increased by these simple data. Let's assume no metastases are seen, then the authors could further strengthen the case for the value of their hESC model in systematically exploring with functional genomics the requirements to achieve metastases to these other sites.

We have included descriptions of what we found and didn’t find at other potential sites of metastasis in the results section, with the following sentences: 

“In animals administered DOX, histological examinations showed that approximately half developed metastases in distant organs, including the liver or lung (Figure 1D). No metastases were observed in the bone, brain, or lymph nodes. For a more detailed assessment, future studies could employ more sensitive imaging methods, such as luciferase imaging.”

(5) Related to this, we have no idea if the mice that developed liver metastases (or the one mouse with lung metastasis) had more than one metastatic site. They will know this and should report it. Again, my guess is that these were isolated metastases in each mouse. Again, they can indicate the value of their model in searching for programs that would increase the number of the various organs. 

We appreciate the suggestion. We observed that one of the mice developed metastatic tumors in both the liver and lungs. This information has been incorporated into the Results section.

(6) While renal capsule implantation for testing growth and metastatic behavior is reasonable and based on substantial literature using this site for implantation of patient tumor specimens, what would have increased the value of the paper is knowing the results from orthotopic (lung implantation). Whatever the results were (they occurred or did not occur) they will be important to know. I understand the "future experiments" argument, but in reading the manuscript this jumped out at me as an obvious thing for the authors to try. 

We conducted orthotopic implantation several ways, including via intra-tracheal instillation of 0.5 million RP or RPM cells in PBS per mouse. However, none of the subjects (0/5 mice) developed tumor-like growths and the number of animals used was small. Further, this outcome could be attributed to biological or physical factors. For instance, the conducting airway is coated with secretory cells producing protective mucins and may not have retained the 0.5 million cells. This is one example that may have hindered effective colonization. Future adjustments, such as increasing the number of cells, embedding them in Matrigel, or damaging the airway to denude secretory cells and trigger regeneration might alter the outcomes. These ideas might guide future work to strengthen the utility of the models.

(7) Another obvious piece of data that would have improved the value of this manuscript would be to know whether the RPM tumors responded to platin-etoposide chemotherapy. Such data was not presented in their first RP hESC notch inhibition paper (which we now know generated what the authors call "benign" tumors). While I realize chemotherapy responses represent other types of experiments, as the authors point out one of the main reasons they developed their new human model was for therapy testing. Two papers in and we are all still asking - does their model respond or not respond dramatically to platin-etoposide therapy? Whatever the results are they are a vital next step in considering the use of their model. 

Please see the comments above regarding our decision not to include data from a clinical trial that lacked appropriate controls.

(8) The finding of RPM cells that expressed NEUROD1, ASCL1, or both was interesting. From the way the data were presented, I don't have a clear idea which of these lineage oncogenes the metastatic lesions from ~11 different mice expressed. Whatever the result is it would be useful to know - all NEUROD1, some ASCL1, some mixed etc.

Based on the bulk RNA-sequencing of a few metastatic sites (Figure 4H), what we can demonstrate is that all sites were NEUROD1 and expressed low or no detectable  ASCL1.

(9) While several H&E histologic images were presented, even when I enlarged them to 400% I couldn't clearly see most of them. For future reference, I think it would be important to have several high-quality images of the RP, RPM, RPMT58A subcutaneous tumors, sub-renal capsule tumors, and liver and lung metastatic lesions. If there is heterogeneity in the primary tumors or the metastases it would be important to show this. The quality of the images they have in the pdf file is suboptimal. If they have already provided higher-quality images - great. If not, I think in the long run as people come back to this paper, it will help both the field and the authors to have really great images of their tumors and metastases. 

We have attempted to improve the quality of the embedded images. Digital resolution is a tradeoff with data size – higher resolution images are always available upon request, but may not be suitable  for generation of figures in a manuscript viewed on-line.

Author response:

Reviewer #1 (Public review):

Summary:

The authors revealed the cellular heterogeneity of companion cells (CCs) and demonstrated that the florigen gene FT is highly expressed in a specific subpopulation of these CCs in Arabidopsis. Through a thorough characterization of this subpopulation, they further identified NITRATE-INDUCIBLE GARP-TYPE TRANSCRIPTIONAL REPRESSOR 1 (NIGT1)-like transcription factors as potential new regulators of FT. Overall, these findings are intriguing and valuable, contributing significantly to our understanding of florigen and the photoperiodic flowering pathway. However, there is still room for improvement in the quality of the data and the depth of the analysis. I have several comments that may be beneficial for the authors.

Strengths:

The usage of snRNA-seq to characterize the FT-expressing companion cells (CCs) is very interesting and important. Two findings are novel: 1) Expression of FT in CCs is not uniform. Only a subcluster of CCs exhibits high expression level of FT. 2) Based on consensus binding motifs enriched in this subcluster, they further identify NITRATE-INDUCIBLE GARP-TYPE TRANSCRIPTIONAL REPRESSOR 1 (NIGT1)-like transcription factors as potential new regulators of FT.

We are pleased to hear that reviewer 1 noted the novelty and importance of our work. As reviewer 1 mentioned, we are also excited about the identification of a subcluster of companion cells with very high FT expression. We believe that this work is an initial step to describe the molecular characteristics of these FT-expressing cells. We are also excited to share our new findings on NIGT1_s as potential _FT regulators. We think that this finding attracts broader audiences, as the molecular factor that coordinates plant nutrition status with flowering time remains largely unknown despite its well-known plant phenomenon.

Weaknesses:

(1) Title: "A florigen-expressing subpopulation of companion cells". It is a bit misleading. The conclusion here is that only a subset of companion cells exhibit high expression of FT, but this does not imply that other companion cells do not express it at all.

We agree with this comment, as we also did not intend to say that FT is not produced in other companion cells than the subpopulation we identified. We will revise the title to more accurately reflect the point.

(2) Data quality: Authors opted for fluorescence-activated nuclei sorting (FANS) instead of traditional cell sorting method. What is the rationale behind this decision? Readers may wonder, especially given that RNA abundance in single nuclei is generally lower than that in single cells. This concern also applies to snRNA-seq data. Specifically, the number of genes captured was quite low, with a median of only 149 genes per nucleus. Additionally, the total number of nuclei analyzed was limited (1,173 for the pFT:NTF and 3,650 for the pSUC2:NTF). These factors suggest that the quality of the snRNA-seq data presented in this study is quite low. In this context, it becomes challenging for the reviewer to accurately assess whether this will impact the subsequent conclusions of the paper. Would it be possible to repeat this experiment and get more nuclei?

We appreciate this comment; we noticed that we did not clearly explain the rationale of using single-nucleus RNA sequencing (snRNA-seq) instead of single-cell RNA-seq (scRNA-seq). As reviewer 1 mentioned, RNA abundance in scRNA-seq is higher than in snRNA-seq. To conduct scRNA-seq using plant cells, protoplasting is the necessary step. However, in our study, protoplasting has many drawbacks in isolating our target cells from the phloem. It is technically challenging to efficiently isolate protoplasts from highly embedded phloem companion cells from plant tissues. Usually, it requires a minimum of several hours of enzymatic incubation to protoplast companion cells and the efficiencies of protoplasting these cells are still low. For our analysis, restoring the time information within a day is also crucial. Therefore, we performed more speedy isolation method. In the revision, we will explain our rationale of choosing snRNA-seq due to the technical limitations.

Here, reviewer 1 raised a concern about the quality of our snRNA-seq data, referring to the relatively low readcounts per nucleus. Although we believe that shallow reads do not necessaryily indicate low quality and are confident in the accuracy of our snRNA-seq data, as supported by the detailed follow-up experiments (e.g., imaging analysis in Fig. 4B), we agree that it is important to address this point in the revision and alleviate readers’ concerns regarding the data quality.

(3) Another disappointment is that the authors did not utilize reporter genes to identify the specific locations of the FT-high expressing cells (cluster 7 cells) within the CC population in vivo. Are there any discernible patterns that can be observed?

As we previously showed only limited spatial images of overlap between FT-expressing cells and other cluster 7 gene-expressing cells in Fig. 4B, this comment is understandable. To respond to it, we will include whole leaf images of FT- and cluster 7 gene-expressing cells to assess the spatial overlaps between FT and cluster 7 genes within a leaf.

(4) The final disappointment is that the authors only compared FT expression between the nigtQ mutants and the wild type. Does this imply that the mutant does not have a flowering time defect particularly under high nitrogen conditions?

To answer this question, we will include the flowering time measurement data of the nigtQ mutants grown on the soil with sufficient nitrogen sources.

Reviewer #2 (Public review):

This manuscript submitted by Takagi et al. details the molecular characterization of the FT-expressing cell at a single-cell level. The authors examined what genes are expressed specifically in FT-expressing cells and other phloem companion cells by exploiting bulk nuclei and single-nuclei RNA-seq and transgenic analysis. The authors found the unique expression profile of FT-expressing cells at a single-cell level and identified new transcriptional repressors of FT such as NIGT1.2 and NIGT1.4.

Although previous researchers have known that FT is expressed in phloem companion cells, they have tended to neglect the molecular characterization of the FT-expressing phloem companion cells. To understand how FT, which is expressed in tiny amounts in phloem companion cells that make up a very small portion of the leaf, can be a key molecule in the regulation of the critical developmental step of floral transition, it is important to understand the molecular features of FT-expressing cells in detail. In this regard, this manuscript provides insight into the understanding of detailed molecular characteristics of the FT-expressing cell. This endeavor will contribute to the research field of flowering time.

We are grateful that reviewer 2 recognizes the importance of transcriptome profiling of FT-expressing cells at the single-cell level.

Here are my comments on how to improve this manuscript.

(1) The most noble finding of this manuscript is the identification of NTGI1.2 as the upstream regulator of FT-expressing cluster 7 gene expression. The flowering phenotypes of the nigtQ mutant and the transgenic plants in which NIGT1.2 was expressed under the SUC2 gene promoter support that NIGT1.2 functions as a floral repressor upstream of the FT gene. Nevertheless, the expression patterns of NIGT1.2 genes do not appear to have much overlap with those of NIGT1.2-downstream genes in the cluster 7 (Figs S14 and F3). An explanation for this should be provided in the discussion section.

We agree reviewer 2 that spatial expression patterns of NIGT1.2 and cluster 7 genes do not overlap much, and some discussion should be provided in the manuscript. Although we do not have a concrete answer for this phenomenon, NIGT1.2 may suppress FT gene expression in non-cluster 7 cells to prevent the misexpression of FT. Another possible explanation is that NIGT1.2 negatively affects the formation of cluster 7 cells. If so, cells with high NIGT1.2 gene expression hardly become cluster 7 cells. We will discuss it further in the discussion section in our revised manuscript.

(2) To investigate gene expression in the nuclei of specific cell populations, the authors generated transgenic plants expressing a fusion gene encoding a Nuclear Targeting Fusion protein (NTF) under the control of various cell type-specific promoters. Since the public audience would not know about NTF without reading reference 16, some explanation of NTF is necessary in the manuscript. Please provide a schematic of constructs the authors used to make the transformants.

As reviewer 2 pointed out, we lacked a clear explanation why we used NTF in this study. NTF is the fusion protein that consists of a nuclear envelope targeting domain, GFP, and biotin acceptor peptide. It was originally designed for the INTACT (isolation of nuclei tagged in specific cell types) method that enables us to isolate bulk nuclei from specific tissues. Although our original intention was profiling the bulk transcriptome of mRNAs that exist in nuclei of the FT-expressing cells using INTACT, we utilized our NTF transgenic lines for snRNA-seq analysis. To explain what NTF is to readers, we will include a schematic diagram of NTF.

Author response:

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

We have carefully addressed all the reviewers' suggestions, and detailed responses are provided at the end of this letter. In summary:

• We conducted two additional replicates of the study to obtain more robust and reliable data.

• The Introduction has been revised for greater clarity and conciseness.

• The Results section was shortened and reorganized to highlight the key findings more effectively.

• The Discussion was modified according to the reviewers' suggestions, with a focus on reorganization and conciseness.

We hope you find this revised version of the manuscript satisfactory.

Reviewer #1 (Public Review):

Summary:

This study examines the role of host blood meal source, temperature, and photoperiod on the reproductive traits of Cx. quinquefasciatus, an important vector of numerous pathogens of medical importance. The host use pattern of Cx. quinquefasciatus is interesting in that it feeds on birds during spring and shifts to feeding on mammals towards fall. Various hypotheses have been proposed to explain the seasonal shift in host use in this species but have provided limited evidence. This study examines whether the shifting of host classes from birds to mammals towards autumn offers any reproductive advantages to Cx. quinquefasciatus in terms of enhanced fecundity, fertility, and hatchability of the offspring. The authors found no evidence of this, suggesting that alternate mechanisms may drive the seasonal shift in host use in Cx. quinquefasciatus.

Strengths:

Host blood meal source, temperature, and photoperiod were all examined together.

Weaknesses:

The study was conducted in laboratory conditions with a local population of Cx. quinquefasciatus from Argentina. I'm not sure if there is any evidence for a seasonal shift in the host use pattern in Cx. quinquefasciatus populations from the southern latitudes.

Comments on the revision: 

Overall, I am not quite convinced about the possible shift in host use in the Argentinian populations of Cx. quinquefasciatus. The evidence from the papers that the authors cite is not strong enough to derive this conclusion. Therefore, I think that the introduction and discussion parts where they talk about host shift in Cx. quinquefasciatus should be removed completely as it misleads the readers. I suggest limiting the manuscript to talking only about the effects of blood meal source and seasonality on the reproductive outcomes of Cx. quinquefasciatus. 

As mentioned in the previous revision, we agree on the reviewer observation about the lack of evidence on seasonal shift in the host use pattern in Cx. quinquefasciatus populations from Argentina. We include this topic in the discussion.

Additionally, we also added a paragraph in the discussion section to include the limitations of our study and conclusions. One of them is the fact that our results are based on controlled conditions experiments. Future studies are needed to elucidate if the same trend is found in the field.

Reviewer #1 (Recommendations for the authors): 

Abstract

Line 73: shift in feeding behavior

Accepted as suggested. 

Discussion

Line 258: addressed that Accepted as suggested.

Line 263: blood is nutritionally richer

Accepted as suggested.

Reviewer #2 (Public Review): 

Summary:

Conceptually, this study is interesting and is the first attempt to account for the potentially interactive effects of seasonality and blood source on mosquito fitness, which the authors frame as a possible explanation for previously observed host-switching of Culex quinquefasciatus from birds to mammals in the fall. The authors hypothesize that if changes in fitness by blood source change between seasons, higher fitness on birds in the summer and on mammals in the autumn could drive observed host switching. To test this, the authors fed individuals from a colony of Cx. quinquefasciatus on chickens (bird model) and mice (mammal model) and subjected each of these two groups to two different environmental conditions reflecting the high and low temperatures and photoperiod experienced in summer and autumn in Córdoba, Argentina (aka seasonality). They measured fecundity, fertility, and hatchability over two gonotrophic cycles. The authors then used a generalized linear model to evaluate the impact of host species, seasonality, and gonotrophic cycle on fecundity, fertility, and hatchability. The authors were trying to test their hypothesis by determining whether there was an interactive effect of season and host species on mosquito fitness. This is an interesting hypothesis; if it had been supported, it would provide support for a new mechanism driving host switching. While the authors did report an interactive impact of seasonality and host species, the directionality of the effect was the opposite from that hypothesized. The authors have done a very good job of addressing many of the reviewer concerns, with several exception that continue to cause concern about the conclusions of the study. 

Strengths:

(1) Using a combination of laboratory feedings and incubators to simulate seasonal environmental conditions is a good, controlled way to assess the potentially interactive impact of host species and seasonality on the fitness of Culex quinquefasciatus in the lab.

(2) The driving hypothesis is an interesting and creative way to think about a potential driver of host switching observed in the field. 

(3) The manuscript has become a lot clearer and easier to read with the revisions - thank you to the authors for working hard to make many of the suggested changes. 

Weaknesses:

(1) The authors have decided not to follow the suggestion of conducting experimental replicates of the study. This is understandable given the significant investment of resources and time necessary, however, it leaves the study lacking support. Experimental replication is an important feature of a strong study and helps to provide confidence that the observed patterns are real and replicable. Without replication, I continue to lack confidence in the conclusions of the study. 

We included replicates as suggested.  

(2) The authors have included some additional discussion about the counterintuitive nature of their results, but the paragraph discussing this in the discussion was confusing. I believe that this should be revised. This is a key point of the paper and needs to be clear to the reader.

Revised as suggested. 

(3) There should be more discussion of the host switching observed in the two studies conducted in Argentina referenced by the authors. Since host switching is the foundation for the hypothesis tested in this paper, it is important to fully explain what is currently known in Argentina. 

Accepted as suggested.

(4) In some cases, the explanations of referenced papers are not entirely accurate. For example, when referencing Erram et al 2022, I think the authors misrepresented the paper's discussion regarding pre-diuresis- Erram et al. are suggesting that pre-diuresis might be the mechanism by which C. furens compensates for the lower nutritional value of avian blood, leading to no significant difference between avian/mammal blood on fecundity/fertility (rather than leading to higher fecundity on birds, as stated in this manuscript). The study performed by Erram et al. also didn't prove this phenomenon, they just suggest it as a possible mechanism to explain their results, so that should be made clear when referencing the paper. 

Changed as suggested.

(5) In some cases, the conclusions continue to be too strongly worded for the evidence available. For example, lines 322-324: I don't think the data is sufficient to conclude that a different physiological state is induced, nor that they are required to feed on a blood source that results in higher fitness. 

Redaction was modified as suggested to tight our discussion with results.

(6) There is limited mention of the caveat that this experiment performed with simulated seasonality that does not perfectly replicate seasonality in the field. I think this caveat should be discussed in the discussion (e.g. that humidity is held constant).

This topic is now included in the discussion as suggested. 

Reviewer #2 (Recommendations for the authors): 

59-60: These terms should end with -phagic instead of -philic. These papers study blood feeding patterns, not preference. I understand that the Janssen papers calls it "mammalophilic" in their title, but this was an incorrect use of the term in their paper. There are some review papers that explain the difference in this terminology if it's helpful.

Accepted as suggested. 

73: edit to "in" feeding behavior 

Accepted as suggested.

77-78: Given that the premise of your study is based on the phenomenon of host switching, I suggest that you expand your discussion of these two papers. What did they observe? Which hosts did they switch from / to and how dramatic was the shift?

Accepted as suggested. 

79: replace acknowledged with experienced 

Accepted as suggested.

79-80: the way that this is written is misleading. It suggests that Spinsanti showed that seasonal variation in SLEV could be attributed to a host shift, which isn't true. This citation should come before the comma and then you should use more cautious language in the second half. E.g which MIGHT be possible to attribute to .... 

Accepted as suggested.

80-82: this is not convincing. Even if the Robin isn't in Argentina, Argentina does have migrating birds, so couldn't this be the case for other species of birds? Do any of the birds observed in previous blood meal analyses in Argentina migrate? If so, couldn't this hypothesis indeed play a role? 

A paragraph about this topic was added to the discussion as suggested.

90: hypotheses for what? The fall peak in cases? Or host switching? 

Changed to be clearer.

98: where was this mentioned before? I think "as mentioned before" can be removed. 

Accepted as suggested.

101: edit to "whether an interaction effect exists" 

Accepted as suggested.

104: edit to "We hypothesize that..." 

Accepted as suggested.

106: reported host USE changes, not host PREFERENCE changes, right? 

All the terminology was change to host pattern and not preference to avoid confusion.

200: Briefly reading Carsey and Harden, it looks like the methodology was developed for social science. Is there anything you can cite to show this applied to other types of data? If not, I think this requires more explanation in your MS. 

This was removed as replicates were included.

237-239: I think it is best not to make a definitive statement about greater/higher if it isn't statistically significant; I suggest modifying the sentences to state that the differences you are listing were not significantly different up front rather than at the end, otherwise if people aren't reading carefully, they may get the wrong impression. 

Accepted as suggested.

245: you only use the term MS-I once before and I forgot what it meant since it wasn't repeated, so I had to search back through with command-F. I suggest writing this out rather than using the acronym. 

Accepted as suggested.

249: edit to: "an interaction exists between the effect of..." 

Accepted as suggested.

253-254: greater compared to what? 

Change for clearness. 258-260: edit for grammar 

Accepted as suggested.

260-262: edit for grammar; e.g. "However, this assumption lacks solid evidence; there is a scarcity of studies regarding nutritional quality of avian blood and its impact on mosquito fitness." 

Accepted as suggested.

263: edit: blood is nutritionally... 

Accepted as suggested.

264-267: This doesn't sound like an accurate interpretation of what the paper suggests regarding pre-diuresis in their discussion - they are suggesting that pre-diuresis might be the mechanism by which C. furens compensates for the lower nutritional value of avian blood, leading to no significant difference between avian/mammal blood on fecundity/fertility. They also don't show this, they just suggest it as a possible mechanism to explain their results. 

This topic was removed given the restructuring of discussion.

253-269: You should tie this paragraph back to your results to explicitly compare/contrast your findings with the previous literature. 

Accepted as suggested.

270-282: This paragraph would be a good place to explain the caveat of working in the laboratory - for example, humidity was the same across the two seasons which I'm guessing isn't the case in the field in Argentina. You can discuss what aspects of laboratory season simulation do not accurately replicate field conditions and how this can impact your findings. You said in your response to the reviewers that you weren't interested in measuring other variables (which is fair, and not expected!), but the beauty of the discussion section is to be able to think about how your experimental design might impact your results - one possibility is that your season simulation may not have produced the results produced by true seasonal shifts. 

Accepted as suggested.

279-281: You say your experiment was conducted within the optimal range, which would suggest that both summer and autumn were within that range, but then you only talk about summer as optimal in the following sentence. 

Changed for clearness.

281-282: You should clarify this sentence - state what the interaction has an effect on. 

Accepted as suggested.

283-291: I appreciate that your discussion now acknowledges the small sample size and the questions that remain unanswered due to the results being opposite to that of the hypothesis, but this paragraph lacks some details and in places doesn't make sense. 

I think you need to emphasize which groups had small sample size and which conclusions that might impact. I also think you need to explain why the sample size was substantially smaller for some groups (e.g. did they refuse to feed on the mouse in the autumn?). I appreciate that sample sizes are hard to keep high across many groups and two gonotrophic periods, but unfortunately, that is why fitness experiments are so hard to do and by their nature, take a long time. I understand that other papers have even lower sample size, but I was not asked to review those papers and would have had the same critique of them. I don't believe that creating simulated data via a Monte Carlo approach can make up for generating real data. As I understand it from your explanation, you are parametrizing the Monte Carlo simulations with your original data, which was small to begin with for autumn mouse. Using this simulation doesn't seem like a satisfactory replacement for an experimental replicate in my opinion. I maintain that at least a second replicate is necessary to see whether the patterns that you have observed hold. 

The performing of a power analysis and addition of more replicates tried to solve the issue of sample size. More about this critic is added in the discussion. The simulation approach was totally removed.

Regarding the directionality of the interaction effect, I think this warrants more discussion. Lines 287-291 don't make sense to me. You suggest that feeding on birds in the autumn may confer a reproductive advantage when conditions are more challenging. But then why wouldn't they preferentially feed on birds in the autumn, rather than mammals? I suggest rewriting this paragraph to make it clearer. 

Accepted as suggested.

297: earlier mentioned treatments? Do you mean compared to the first gonotrophic cycle? This isn't clear. 

Changed for clearness.

302-303: Did you clarify whether you are allowed to reference unpublished data in eLife? 

This was removed to follow the guidelines of eLife.

316-317: "it becomes apparent" sounds awkward, I suggest rewording and also explaining how this conclusion was made. 

Accepted as suggested.

322-324: I think that this statement is too strongly worded. I don't think your data is sufficient to conclude that a different physiological state is induced, nor that they are required to feed on a blood source that results in higher fitness. Please modify this and make your conclusions more cautious and closely linked to what you actually demonstrated. 

Accepted as suggested.

325: change will perform to would have 

Accepted as suggested.

326: add to the sentence: "and vice versa in the summer" 

Accepted as suggested.

330: possible explanations, not explaining scenarios. 

Accepted as suggested.

517: I think you should repeat the abbreviation definitions in the caption to make it easier for readers, otherwise they have to flip back and forth which can be difficult depending on formatting.

Accepted as suggested. 

In general, I think that your captions need more information. I think the best captions explain the figure relatively thoroughly such that the reader can look at the figure and caption and understand without reading the paper in depth. (e.g. the statistical test used).

Data availability: The eLife author instructions do say that data must be made available, so there should be a statement on data availability in your MS. I also suggest you make the code available.

Accepted as suggested.

Author response:

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

Reviewer #1 (Public Review):

Summary:

BMP signaling is, arguably, best known for its role in the dorsoventral patterning, but not in nematodes, where it regulates body size. In their paper, Vora et al. analyze ChIP-Seq and RNA-Seq data to identify direct transcriptional targets of SMA-3 (Smad) and SMA-9 (Schnurri) and understand the respective roles of SMA-3 and SMA-9 in the nematode model Caenorhabditis elegans. The authors use publicly available SMA-3 and SMA-9 ChIP-Seq data, own RNA-Seq data from SMA-3 and SMA-9 mutants, and bioinformatic analyses to identify the genes directly controlled by these two transcription factors (TFs) and find approximately 350 such targets for each. They show that all SMA-3-controlled targets are positively controlled by SMA-3 binding, while SMA-9-controlled targets can be either up or downregulated by SMA-9. 129 direct targets were shared by SMA-3 and SMA-9, and, curiously, the expression of 15 of them was activated by SMA-3 but repressed by SMA-9. Since genes responsible for cuticle collagen production were eminent among the SMA-3 targets, the authors focused on trying to understand the body size defect known to be elicited by the modulation of BMP signaling. Vora et al. provide compelling evidence that this defect is likely to be due to problems with the BMP signaling-dependent collagen secretion necessary for cuticle formation.

We thank the reviewer for this supportive summary. We would like to clarify the status of the publicly available ChIP-seq data. We generated the GFP tagged SMA-3 and SMA‑9 strains and submitted them to be entered into the queue for ChIP-seq processing by the modENCODE (later modERN) consortium. Thus, the publicly available SMA-3 and SMA-9 ChIP-seq datasets used here were derived from our efforts.  Due to the nature of the consortium’s funding, the data were required to be released publicly upon completion. Nevertheless, our current manuscript provides the first comprehensive analysis of these datasets. We have updated the text to clarify this point.

Strengths:

Vora et al. provide a valuable analysis of ChIP-Seq and RNA-Seq datasets, which will be very useful for the community. They also shed light on the mechanism of the BMP-dependent body size control by identifying SMA-3 target genes regulating cuticle collagen synthesis and by showing that downregulation of these genes affects body size in C. elegans.

Weaknesses:

(1) Although the analysis of the SMA-3 and SMA-9 ChIP-Seq and RNA-Seq data is extremely useful, the goal "to untangle the roles of Smad and Schnurri transcription factors in the developing C. elegans larva", has not been reached. While the role of SMA-3 as a transcriptional activator appears to be quite straightforward, the function of SMA-9 in the BMP signaling remains obscure. The authors write that in SMA-9 mutants, body size is affected, but they do not show any data on the mechanism of this effect.

We thank the reviewer for directing our attention to the lack of clarity about SMA-9’s function. We have revised the text to highlight what this study and others demonstrate about SMA-9’s role in body size. Simply stated, SMA-9 is needed together with SMA-3 to promote the expression of genes involved in one-carbon metabolism, collagens, and chaperones, all of which are required for body size. SMA-3 has additional, SMA-9-independent transcriptional targets, including chaperones and ER secretion factors, that also contribute to body size. Finally, SMA-9 regulates additional targets independent of SMA-3 that likely have a minimal role in body size. We have adjusted Figure 5 with new graphs of the original data to make these points more clear.

(2) The authors clearly show that both TFs can bind independently of each other, however, by using distances between SMA-3 and SMA-9 ChIP peaks, they claim that when the peaks are close these two TFs act as complexes. In the absence of proof that SMA-3 and SMA-9 physically interact (e.g. that they co-immunoprecipitate - as they do in Drosophila), this is an unfounded claim, which should either be experimentally substantiated or toned down.

We acknowledge that we have not demonstrated a physical interaction between SMA-3 and SMA-9 through a co-immunoprecipitation, and we have indicated in the text that a formal biochemical demonstration would be required to make this point. Moreover, we toned down the text by stating that our results suggest that either SMA-3 and SMA-9 frequently bind as either subunits in a complex or in close vicinity to each other along the DNA. As the reviewer has indicated, a physical interaction between Smads and Schnurris has been amply demonstrated in other systems. A limitation in these previous studies is that only a small number of target genes were analyzed. Our goal in this study was to determine how widespread this interaction is on a genomic scale. Our analyses demonstrate for the first time that a Schnurri transcription factor has significant numbers of both Smad-dependent and Smad-independent target genes. We have revised the text to clarify this point.

(3) The second part of the paper (the collagen story) is very loosely connected to the first part. dpy-11 encodes an enzyme important for cuticle development, and it is a differentially expressed direct target of SMA-3. dpy-11 can be bound by SMA-9, but it is not affected by this binding according to RNA-Seq. Thus, technically, this part of the paper does not require any information about SMA-9. However, this can likely be improved by addressing the function of the 15 genes, with the opposing mode of regulation by SMA-3 and SMA-9.

We appreciate this suggestion and have clarified in the text how SMA-9 contributes to collagen organization and body size regulation.

(4) The Discussion does not add much to the paper - it simply repeats the results in a more streamlined fashion.

We thank the reviewer for this suggestion. We have added more context to the Discussion.

Reviewer #2 (Public Review):

In the present study, Vora et al. elucidated the transcription factors downstream of the BMP pathway components Smad and Schnurri in C. elegans and their effects on body size. Using a combination of a broad range of techniques, they compiled a comprehensive list of genome-wide downstream targets of the Smads SMA-3 and SMA-9. They found that both proteins have an overlapping spectrum of transcriptional target sites they control, but also unique ones. Thereby, they also identified genes involved in one-carbon metabolism or the endoplasmic reticulum (ER) secretory pathway. In an elaborate effort, the authors set out to characterize the effects of numerous of these targets on the regulation of body size in vivo as the BMP pathway is involved in this process. Using the reporter ROL-6::wrmScarlet, they further revealed that not only collagen production, as previously shown, but also collagen secretion into the cuticle is controlled by SMA-3 and SMA-9. The data presented by Vora et al. provide in-depth insight into the means by which the BMP pathway regulates body size, thus offering a whole new set of downstream mechanisms that are potentially interesting to a broad field of researchers.

The paper is mostly well-researched, and the conclusions are comprehensive and supported by the data presented. However, certain aspects need clarification and potentially extended data.

(1) The BMP pathway is active during development and growth. Thus, it is logical that the data shown in the study by Vora et al. is based on L2 worms. However, it raises the question of if and how the pattern of transcriptional targets of SMA-3 and SMA-9 changes with age or in the male tail, where the BMP pathway also has been shown to play a role. Is there any data to shed light on this matter or are there any speculations or hypotheses?

We agree that these are intriguing questions, and we are interested in the roles of transcriptional targets at other developmental stages and in other physiological functions, but these analyses are beyond the scope of the current study.

(2) As it was shown that SMA-3 and SMA-9 potentially act in a complex to regulate the transcription of several genes, it would be interesting to know whether the two interact with each other or if the cooperation is more indirect.

A physical interaction between Smads and Schnurri has been amply demonstrated in other systems. Our goal in this study was not to validate this physical interaction, but to analyze functional interactions on a genome-wide scale.

(3) It would help the understanding of the data even more if the authors could specifically state if there were collagens among the genes regulated by SMA-3 and SMA-9 and which.

We thank the reviewer for this suggestion. col-94 and col-153 were identified as direct targets of both SMA-3 and SMA-9. We noted this in the Discussion.

(4) The data on the role of SMA-3 and SMA-9 in the regulation of the secretion of collagens from the hypodermis is highly intriguing. The authors use ROL-6 as a reporter for the secretion of collagens. Is ROL-6 a target of SMA-9 or SMA-3? Even if this is not the case, the data would gain even more strength if a comparable quantification of the cuticular levels of ROL-6 were shown in Figure 6, and potentially a ratio of cuticular versus hypodermal levels. By that, the levels of secretion versus production can be better appreciated.

We previously showed that rol-6 mRNA levels are reduced in dbl-1 mutants at L2, but RNA-seq analysis did not find enough of a statistically significant change in rol-6 to qualify it as a transcriptional target and total levels of protein are also not significantly reduced in mutants. We added this information in the text.

(5) It is known that the BMP pathway controls several processes besides body size. The discussion would benefit from a broader overview of how the identified genes could contribute to body size. The focus of the study is on collagen production and secretion, but it would be interesting to have some insights into whether and how other identified proteins could play a role or whether they are likely to not be involved here (such as the ones normally associated with lipid metabolism, etc.).

We have added more information to the Discussion.

Reviewer #1 (Recommendations For The Authors):

Figure 1 - Figure 3: The authors might want to think about condensing this into two figures.

To avoid confusion with the different workflows, we prefer to keep these as three separate figures.

Figure 1a-b: Measurement unit missing on X.

We added the unit “bps” to these graphs.

Line 244-246: The authors should stress in the Results that they analyzed publicly available ChIP-Seq data, which was not generated by them, - not just by providing a reference to Kudron et al., 2018. As far as I understood, ChIP was performed with an anti-GFP antibody. Please mention this, and specify the information about the vendor and the catalog number in the Methods.

We would like to clarify the status of the publicly available ChIP-seq data. We generated the GFP tagged SMA-3 and SMA‑9 strains and submitted them to be entered into the queue for ChIP-seq processing by the modENCODE (later modERN) consortium. Thus, the publicly available SMA-3 and SMA-9 ChIP-seq datasets used here were derived from our efforts.  Due to the nature of the consortium’s funding, the data were required to be released publicly upon completion. Nevertheless, our current manuscript provides the first comprehensive analysis of these datasets. We have clarified these issues in the text.  We have also added information regarding the anti-GFP antibody to the Methods.

Line 267-270: The authors should either provide experimental evidence that SMA-3 and SMA-9 form complexes or write something like "significant overlap between SMA-3 and SMA-9 peaks may indicate complex formation between these two transcription factors as shown in Drosophila" - but in the absence of proof, this must be a point for the Discussion, not for the Results. Moreover, similar behavior of fat-6 (overlapping ChIP peaks) and nhr-114 (non-overlapping ChIP peaks) in SMA-3 and SMA-9 mutants may be interpreted as a circumstantial argument against SMA-3/SMA-9 complex formation (see Lines 342-348). Importantly, since ChIP-Seq data are available for a wide array of C. elegans TFs, it would be very useful to have an estimate of whether SMA-3/SMA-9 peak overlap is significantly higher than the peak overlap between SMA-3 and several other TFs expressed at the same L2 stage.

We have clarified our goals regarding SMA-3 and SMA-9 interactions and softened our conclusions by indicating in the text that a formal biochemical demonstration would be required to demonstrate a physical interaction. Moreover, we toned down the text by stating that our results suggest that either SMA-3 and SMA-9 frequently bind as either subunits in a complex or in close vicinity to each other along the DNA. We have added an analysis of HOT sites to address overlap of binding with other transcription factors. We disagree with the interpretation that transcription factors with non-overlapping sites cannot act together to regulate gene expression; however, nhr-114 also has an overlapping SMA-3 and SMA-9 site, so this point becomes less relevant. We have clarified the categorization of nhr-114 in the text.

Lines 272-292: The authors do not comment on the seemingly quite small overlap between the RNA-Seq and the ChIP-Seq dataset, but I think they should. They have 3205 SMA-3 ChIP peaks and 1867 SMA-3 DEGs, but the amount of directly regulated targets is 367. It is important that the authors provide information on the number of genes to which their peaks have been assigned. Clearly, this will not be one gene per peak, but if it were, this would mean that just 11.5% of bound targets are really affected by the binding. The same number would be 4.7% for the SMA-9 peaks.

We have added a discussion of the discrepancy between binding sites and DEGs. The high number of additional sites classified as non-functional could represent the detection of weak affinity targets that do not have an actual biological purpose. Alternatively, these sites could have an additional role in DBL-1 signaling besides transcriptional regulation of nearby genes, or they could be regulating the expression of target genes at a far enough distance to not be detected by our BETA analysis as per the constraints chosen for the analysis. The difference between total binding sites and those associated with changes in gene expression underscores the importance of combining RNA-seq with ChIP-seq to identify the most biologically relevant targets. And as the reviewer indicated, more than one gene can be assigned to a single neighboring peak.

Lines 294-323: I feel like there is a terminology problem, which makes reading very difficult. The authors use "direct targets" as bound genes with significant expression change, but then run into a problem when the gene is bound by SMA-9 and SMA-3, but significant expression change is only associated with one of the two factors. I am not sure this is consistent with the idea of the SMA3/SMA9 complex. Also, different modalities of the SMA3 and SMA9 effect in 15 cases can be explained by co-factors. Reading would be also simplified if the order of the panels in Figure 3 were different. Currently, the authors start their explanation by referring to the shared SMA-3/SMA-9 targets (Figures 3c-d), and only later come to Figure 3b. In general, the authors should start with a clear explanation of what is on the figure (currently starting on Line 313), otherwise, it is unclear why, if the authors only discuss common targets, it is not just 114+15=129 targets, but more.

We have re-ordered the columns in Figure 3 to match the order discussed in the text. We also incorporated more precise language about regulation by SMA-3 and/or SMA-9 in the text.

Lines 325-355: The chapter has a rather unfortunate name "Mechanisms of integration of SMA-3 and SMA-9 function", although the authors do not provide any mechanism. Using 3 target genes, they show that if the regulatory modality of SMA-3 and SMA-9 is the same (2 examples), there is no difference in the expression of the targets, but if the modalities are opposing (1 example), SMA-9 repressive action is epistatic to the SMA-3 activating action. Can this be generalized? The authors should test all their 15 targets with opposite regulations. Moreover, it seems obvious to ask whether the intermediate phenotype of the double-mutants can be attributed to the action of these 15 genes activated by SMA-3 and repressed by SMA-9. I would suggest testing this by RNAi. I would also suggest renaming the chapter to something better reflecting its content.

We have removed the word “mechanism” from the title of this section. We also performed additional RT-PCR experiments on another 5 targets with opposing directions of regulation. The results from these genes are consistent with the result from C54E4.5, demonstrating that the epistasis of sma-9 is generalizable.

Figure 4b: Why was a two-way ANOVA performed here? With the small number of measurements, I would consider using a non-parametric test.

These data are parametric and the distribution of the data is normal, so we chose to use a parametric test (ANOVA).

Lines 354-355. The authors offer two suggestions for the mechanism of the epistatic action of SMA-9 on SMA-3 in the case of C54E4.5, but this is something for the Discussion. If they want to keep it in the Results they should address this experimentally by performing SMA-3 ChIP-seq in the SMA-9 mutants and SMA-9 ChIP-Seq in the SMA-3 mutants.

We moved these models to the discussion as suggested.

Lines 365-367: "We expect that clusters of genes involved in fatty acid metabolism and innate immunity mediate the physiological functions of BMP signaling in fat storage and pathogen resistance, respectively." - This is pretty confusing since the Authors claim in the previous sentence that regulation of immunity by SMA-9 is TGF-beta independent.

Co-regulation of immunity by BMP signaling and SMA-9 is already known. The novel insight is that SMA-9 may have an additional independent role in immunity. We have clarified the language to address this confusion.

Lines 377, and 380: Please explain in non-C. elegans-specific terminology, what rrf-3 and LON-2 are (e.g. write "glypican LON-2" instead of just "LON-2") and add relevant references.

We added information on the proteins encoded by these genes.

Lines 382-384: I am not sure what the Authors mean here by "more limiting".

We substituted the phrase “might have a more prominent requirement in mediating the exaggerated growth defect of a lon-2 mutant”.

Lines 388-392: I found this very confusing. What were these 36 genes? Were these direct targets of SMA-3, SMA-9, or both? Top 36 targets? 36 targets for which mutants are available?

The new Figure 5 clarifies whether target genes are SMA-3-exclusive, SMA-9-exclusive, or co-regulated. The text was also updated for clarity.

Line 397: This is the first time the authors mention dpy-11 but they do not say what it is until later, and they do not say whether it is a target of SMA3/SMA9. Checking Figure 3, I found that it is among the 238 genes bound by both but upregulated only by SMA3. The authors need to explicitly state this - from this point on, they have a section for which SMA-9 appears to be irrelevant.

We added the molecular function of dpy-11 at its first mention. Furthermore, we included the hypothesis that SMA-3 may regulate collagen secretion independently of SMA-9. Our subsequent results with sma-9 mutants disprove this hypothesis.

Line 402: Is ROL-6 a SMA-3/SMA-9 target or just a marker gene?

We previously showed that rol-6 mRNA levels are reduced in dbl-1 mutants at L2, but RNA-seq analysis did not find enough of a statistically significant change in rol-6 to qualify it as a transcriptional target and total levels of protein are also not significantly reduced in mutants. We added this information in the text.

Line 421: I am not sure what "more skeletonized" means.

Replaced with “thinner and skeletonized”

Figure 2b and 2d legends: "Non-target genes nevertheless showing differential expression are indicated with green squares." (l. 581-582 and again l. 588-589) I think should be "Non-direct target genes...".

Changed to “non-direct target genes”

Figure 7 legend: Please indicate the scale bar size in the legend.

Indicated the scale bar size in the legend.

Figure 7: The ER marker is referred to as "ssGFP::KDEL" (in the image and Line 700), however in the text it is called "KDEL::oxGFP" (Line 419). Please use consistent naming.

We fixed the inconsistent naming.

All the experiment suggestions made are optional and can, in principle, be ignored if the authors tone down their claims (for example, the SMA-3/SMA-9 complex formation).

Reviewer #2 (Recommendations For The Authors):

(1) As a control: Have the authors found the known regulated genes among the differentially regulated ones?

Previously known target genes such as fat-6 and zip-10 were identified here. We have added this information in the text.

(2) How many repetitions were performed in Figure 4b? I am wondering as the deviation for C54E4.5 is quite large and that makes me worry that the significant differences stated are not robust.

There were two biologically independent collections from which three cDNA syntheses were analyzed using two technical replicates per point.

(3) Lines 333-336: Can you really make this claim that the antagonistic effects seen in the regulation of body size can be correlated with some targets being regulated in the opposite direction? I would assume that the situation is far more complex as SMADs also regulate other processes.

We agree with the reviewer that multiple models could explain this antagonism, and we have added distinct alternatives in the text.

(4) Lines 367-369: Add the respective reference please.

We have added the relevant references.

Author response:

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

The revised manuscript contains new results and additional text. Major revisions:

(1) Additional simulations and analyses of networks with different biophysical parameters and with identical time constants for E and I neurons (Methods, Supplementary Fig. 5).

(2) Additional simulations and analyses of networks with modifications of connectivity parameters to further analyze effects of E/I assemblies on manifold geometry (Supplementary Fig. 6).

(3) Analysis of synaptic current components (Figure 3 D-F; to analyze mechanism of modest amplification in Tuned networks). 

(4) More detailed explanation of pattern completion analysis (Results).

(5) Analysis of classification performance of Scaled networks (Supplementary Fig.8).

(6) Additional analysis (Figure 5D-F) and discussion (particularly section “Computational functions of networks with E/I assemblies”) of functional benefits of continuous representations in networks with E-I assemblies. 

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

Meissner-Bernard et al present a biologically constrained model of telencephalic area of adult zebrafish, a homologous area to the piriform cortex, and argue for the role of precisely balanced memory networks in olfactory processing. 

This is interesting as it can add to recent evidence on the presence of functional subnetworks in multiple sensory cortices. It is also important in deviating from traditional accounts of memory systems as attractor networks. Evidence for attractor networks has been found in some systems, like in the head direction circuits in the flies. However, the presence of attractor dynamics in other modalities, like sensory systems, and their role in computation has been more contentious. This work contributes to this active line of research in experimental and computational neuroscience by suggesting that, rather than being represented in attractor networks and persistent activity, olfactory memories might be coded by balanced excitation-inhibitory subnetworks. 

Strengths: 

The main strength of the work is in: (1) direct link to biological parameters and measurements, (2) good controls and quantification of the results, and (3) comparison across multiple models. 

(1) The authors have done a good job of gathering the current experimental information to inform a biological-constrained spiking model of the telencephalic area of adult zebrafish. The results are compared to previous experimental measurements to choose the right regimes of operation. 

(2) Multiple quantification metrics and controls are used to support the main conclusions and to ensure that the key parameters are controlled for - e.g. when comparing across multiple models.  (3) Four specific models (random, scaled I / attractor, and two variant of specific E-I networks - tuned I and tuned E+I) are compared with different metrics, helping to pinpoint which features emerge in which model. 

Weaknesses: 

Major problems with the work are: (1) mechanistic explanation of the results in specific E-I networks, (2) parameter exploration, and (3) the functional significance of the specific E-I model. 

(1) The main problem with the paper is a lack of mechanistic analysis of the models. The models are treated like biological entities and only tested with different assays and metrics to describe their different features (e.g. different geometry of representation in Fig. 4). Given that all the key parameters of the models are known and can be changed (unlike biological networks), it is expected to provide a more analytical account of why specific networks show the reported results. For instance, what is the key mechanism for medium amplification in specific E/I network models (Fig. 3)? How does the specific geometry of representation/manifolds (in Fig. 4) emerge in terms of excitatory-inhibitory interactions, and what are the main mechanisms/parameters? Mechanistic account and analysis of these results are missing in the current version of the paper. 

We agree that further mechanistic insights would be of interest and addressed this issue at different levels:

(1) Biophysical parameters: to determine whether network behavior depends on specific choices of biophysical parameters in E and I neurons we equalized biophysical parameters across neuron types. The main observations are unchanged, suggesting that the observed effects depend primarily on network connectivity (see also response to comment [2]).

(2) Mechanism of modest amplification in E/I assemblies: analyzing the different components of the synaptic currents demonstrate that the modest amplification of activity in Tuned networks results from an “imperfect” balance of recurrent excitation and inhibition within assemblies (see new Figures 3D-F and text p.7). Hence, E/I co-tuning substantially reduces the net amplification in Tuned networks as compared to Scaled networks, thus preventing discrete attractor dynamics and stabilizing network activity, but a modest amplification still occurs, consistent with biological observations.

(3) Representational geometry: to obtain insights into the network mechanisms underlying effects of E/I assemblies on the geometry of population activity we tested the hypothesis that geometrical changes depend, at least in part, on the modest amplification of activity within E/I assemblies (see Supplementary Figure 6). We changed model parameters to either prevent the modest amplification in Tuned networks (increasing I-to-E connectivity within assemblies) or introduce a modest amplification in subsets of neurons by other mechanisms (concentration-dependent increase in the excitability of pseudo-assembly neurons; Scaled I networks with reduced connectivity within assemblies). Manipulations that introduced a modest, input-dependent amplification in neuronal subsets had geometrical effects similar to those observed in Tuned networks, whereas manipulations that prevented a modest amplification abolished these effects (Supplementary Figure 6). Note however that these manipulations generated different firing rate distributions. These results provide a starting point for more detailed analyses of the relationship between network connectivity and representational geometry (see p.12).

In summary, our additional analyses indicate that effects of E/I assemblies on representational geometry depend primarily on network connectivity, rather than specific biophysical parameters, and that the resulting modest amplification of activity within assemblies makes an important contribution. Further analyses may reveal more specific relationships between E/I assemblies and representational geometry, but such analyses are beyond the scope of this study.

(2) The second major issue with the study is a lack of systematic exploration and analysis of the parameter space. Some parameters are biologically constrained, but not all the parameters. For instance, it is not clear what the justification for the choice of synaptic time scales are (with E synaptic time constants being larger than inhibition: tau_syn_i = 10 ms, tau_syn_E = 30 ms). How would the results change if they are varying these - and other unconstrained - parameters? It is important to show how the main results, especially the manifold localisation, would change by doing a systematic exploration of the key parameters and performing some sensitivity analysis. This would also help to see how robust the results are, which parameters are more important and which parameters are less relevant, and to shed light on the key mechanisms.  

We thank the reviewer for raising this point. We chose a relatively slow time constant for excitatory synapses because experimental data indicate that excitatory synaptic currents in Dp and piriform cortex contain a prominent NMDA component. Nevertheless, to assess whether network behavior depends on specific choices of biophysical parameters in E and I neurons, we have performed additional simulations with equal synaptic time constants and equal biophysical parameters for all neurons. Each neuron also received the same number of inputs from each population (see revised Methods). Results were similar to those observed previously (Supplementary Fig.5 and p.9 of main text). We therefore conclude that the main effects observed in Tuned networks cannot be explained by differences in biophysical parameters between E and I neurons but is primarily a consequence of network connectivity.

(3) It is not clear what the main functional advantage of the specific E-I network model is compared to random networks. In terms of activity, they show that specific E-I networks amplify the input more than random networks (Fig. 3). But when it comes to classification, the effect seems to be very small (Fig. 5c). Description of different geometry of representation and manifold localization in specific networks compared to random networks is good, but it is more of an illustration of different activity patterns than proving a functional benefit for the network. The reader is still left with the question of what major functional benefits (in terms of computational/biological processing) should be expected from these networks, if they are to be a good model for olfactory processing and learning. 

One possibility for instance might be that the tasks used here are too easy to reveal the main benefits of the specific models - and more complex tasks would be needed to assess the functional enhancement (e.g. more noisy conditions or more combination of odours). It would be good to show this more clearly - or at least discuss it in relation to computation and function. 

In the previous manuscript, the analysis of potential computational benefits other than pattern classification was limited and the discussion of this issue was condensed into a single itemized paragraph to avoid excessive speculation. Although a thorough analysis of potential computational benefits exceeds the scope of a single paper, we agree with the reviewer that this issue is of interest and therefore added additional analyses and discussion.

In the initial manuscript we analyzed pattern classification primarily to investigate whether Tuned networks can support this function at all, given that they do not exhibit discrete attractor states. We found this to be the case, which we consider a first important result.

Furthermore, we found that precise balance of E/I assemblies can protect networks against catastrophic firing rate instabilities when assemblies are added sequentially, as in continual learning. Results from these simulations are now described and discussed in more detail (see Results p.11 and Discussion p.13).

In the revised manuscript, we now also examine additional potential benefits of Tuned networks and discuss them in more detail (see new Figure 5D-F and text p.11). One hypothesis is that continuous representations provide a distance metric between a given input and relevant (learned) stimuli. To address this hypothesis, we (1) performed regression analysis and (2) trained support vector machines (SVMs) to predict the concentration of a given odor in a mixture based on population activity. In both cases, Tuned E+I networks outperformed Scaled and _rand n_etworks in predicting the concentration of learned odors across a wide range mixtures (Figure 5D-F).  E/I assemblies therefore support the quantification of learned odors within mixtures or, more generally, assessments of how strongly a (potentially complex) input is related to relevant odors stored in memory. Such a metric assessment of stimulus quality is not well supported by discrete attractor networks because inputs are mapped onto discrete network states.

The observation that Tuned networks do not map inputs onto discrete outputs indicates that such networks do not classify inputs as distinct items. Nonetheless, the observed geometrical modifications of continuous representations support the classification of learned inputs or the assessment of metric relationships by hypothetical readout neurons. Geometrical modifications of odor representations may therefore serve as one of multiple steps in multi-layer computations for pattern classification (and/or other computations). In this scenario, the transformation of odor representations in Dp may be seen as related to transformations of representations between different layers in artificial networks, which collectively perform a given task (notwithstanding obvious structural and mechanistic differences between artificial and biological networks). In other words, geometrical transformations of representations in Tuned networks may overrepresent learned (relevant) information at the expense of other information and thereby support further learning processes in other brain areas. An obvious corollary of this scenario is that Dp does not perform odor classification per se based on inputs from the olfactory bulb but reformats representations of odor space based on experience to support computational tasks as part of a larger system. This scenario is now explicitly discussed (p.14).

Reviewer #2 (Public Review): 

Summary: 

The authors conducted a comparative analysis of four networks, varying in the presence of excitatory assemblies and the architecture of inhibitory cell assembly connectivity. They found that co-tuned E-I assemblies provide network stability and a continuous representation of input patterns (on locally constrained manifolds), contrasting with networks with global inhibition that result in attractor networks. 

Strengths: 

The findings presented in this paper are very interesting and cutting-edge. The manuscript effectively conveys the message and presents a creative way to represent high-dimensional inputs and network responses. Particularly, the result regarding the projection of input patterns onto local manifolds and continuous representation of input/memory is very Intriguing and novel. Both computational and experimental neuroscientists would find value in reading the paper. 

Weaknesses: 

that have continuous representations. This could also be shown in Figure 5B, along with the performance of the random and tuned E-I networks. The latter networks have the advantage of providing network stability compared to the Scaled I network, but at the cost of reduced network salience and, therefore, reduced input decodability. The authors may consider designing a decoder to quantify and compare the classification performance of all four networks. 

We have now quantified classification by networks with discrete attractor dynamics (Scaled) along with other networks. However, because the neuronal covariance matrix for such networks is low rank and not invertible, pattern classification cannot be analyzed by QDA as in Figure 5B. We therefore classified patterns from the odor subspace by template matching, assigning test patterns to one of the four classes based on correlations (see Supplementary Figure 8). As expected, Scaled networks performed well, but they did not outperform Tuned networks. Moreover, the performance of Scaled networks, but not Tuned networks, depended on the order in which odors were presented to the network. This hysteresis effect is a direct consequence of persistent attractor states and decreased the general classification performance of Scaled networks (see Supplementary Figure 8 for details). These results confirm the prediction that networks with discrete attractor states can efficiently classify inputs, but also reveal disadvantages arising from attractor dynamics. Moreover, the results indicate that the classification performance of Tuned networks is also high under the given task conditions, which simulate a biologically realistic scenario.

We would also like to emphasize that classification may not be the only task, and perhaps not even a main task, of Dp/piriform cortex or other memory networks with E/I assemblies. Conceivably, other computations could include metric assessments of inputs relative to learned inputs or additional learning-related computations. Please see our response to comment (3) of reviewer 1 for a further discussion of this issue. 

Networks featuring E/I assemblies could potentially represent multistable attractors by exploring the parameter space for their reciprocal connectivity and connectivity with the rest of the network. However, for co-tuned E-I networks, the scope for achieving multistability is relatively constrained compared to networks employing global or lateral inhibition between assemblies. It would be good if the authors mentioned this in the discussion. Also, the fact that reciprocal inhibition increases network stability has been shown before and should be cited in the statements addressing network stability (e.g., some of the citations in the manuscript, including Rost et al. 2018, Lagzi & Fairhall 2022, and Vogels et al. 2011 have shown this).  

We thank the reviewer for this comment. We now explicitly discuss multistability (see p. 12) and refer to additional references in the statements addressing network stability.

Providing raster plots of the pDp network for familiar and novel inputs would help with understanding the claims regarding continuous versus discrete representation of inputs, allowing readers to visualize the activity patterns of the four different networks. (similar to Figure 1B). 

We thank the reviewer for this suggestion. We have added raster plots of responses to both familiar and novel inputs in the revised manuscript (Figure 2D and Supplementary Figure 4A).

Reviewer #3 (Public Review): 

Summary: 

This work investigates the computational consequences of assemblies containing both excitatory and inhibitory neurons (E/I assembly) in a model with parameters constrained by experimental data from the telencephalic area Dp of zebrafish. The authors show how this precise E/I balance shapes the geometry of neuronal dynamics in comparison to unstructured networks and networks with more global inhibitory balance. Specifically, E/I assemblies lead to the activity being locally restricted onto manifolds - a dynamical structure in between high-dimensional representations in unstructured networks and discrete attractors in networks with global inhibitory balance. Furthermore, E/I assemblies lead to smoother representations of mixtures of stimuli while those stimuli can still be reliably classified, and allow for more robust learning of additional stimuli. 

Strengths: 

Since experimental studies do suggest that E/I balance is very precise and E/I assemblies exist, it is important to study the consequences of those connectivity structures on network dynamics. The authors convincingly show that E/I assemblies lead to different geometries of stimulus representation compared to unstructured networks and networks with global inhibition. This finding might open the door for future studies for exploring the functional advantage of these locally defined manifolds, and how other network properties allow to shape those manifolds. 

The authors also make sure that their spiking model is well-constrained by experimental data from the zebrafish pDp. Both spontaneous and odor stimulus triggered spiking activity is within the range of experimental measurements. But the model is also general enough to be potentially applied to findings in other animal models and brain regions. 

Weaknesses: 

I find the point about pattern completion a bit confusing. In Fig. 3 the authors argue that only the Scaled I network can lead to pattern completion for morphed inputs since the output correlations are higher than the input correlations. For me, this sounds less like the network can perform pattern completion but it can nonlinearly increase the output correlations. Furthermore, in Suppl. Fig. 3 the authors show that activating half the assembly does lead to pattern completion in the sense that also non-activated assembly cells become highly active and that this pattern completion can be seen for Scaled I, Tuned E+I, and Tuned I networks. These two results seem a bit contradictory to me and require further clarification, and the authors might want to clarify how exactly they define pattern completion. 

We believe that this comment concerns a semantic misunderstanding and apologize for any lack of clarity. We added a definition of pattern completion in the text: “…the retrieval of the whole memory from noisy or corrupted versions of the learned input.”. Pattern completion may be assessed using different procedures. In computational studies, it is often analyzed by delivering input to a subset of the assembly neurons which store a given memory (partial activation). Under these conditions, we find recruitment of the entire assembly in all structured networks, as demonstrated in Supplementary Figure 3. However, these conditions are unlikely to occur during odor presentation because the majority of neurons do not receive any input.

Another more biologically motivated approach to assess pattern completion is to gradually modify a realistic odor input into a learned input, thereby gradually increasing the overlap between the two inputs. This approach had been used previously in experimental studies (references added to the text p.6). In the presence of assemblies, recurrent connectivity is expected to recruit assembly neurons (and thus retrieve the stored pattern) more efficiently as the learned pattern is approached. This should result in a nonlinear increase in the similarity between the evoked and the learned activity pattern. This signature was prominent in Scaled networks but not in Tuned or rand networks. Obviously, the underlying procedure is different from the partial activation of the assembly described above because input patterns target many neurons (including neurons outside assemblies) and exhibit a biologically realistic distribution of activity. However, this approach has also been referred to as “pattern completion” in the neuroscience literature, which may be the source of semantic confusion here. To clarify the difference between these approaches we have now revised the text and explicitly described each procedure in more detail (see p.6). 

The authors argue that Tuned E+I networks have several advantages over Scaled I networks. While I agree with the authors that in some cases adding this localized E/I balance is beneficial, I believe that a more rigorous comparison between Tuned E+I networks and Scaled I networks is needed: quantification of variance (Fig. 4G) and angle distributions (Fig. 4H) should also be shown for the Scaled I network. Similarly in Fig. 5, what is the Mahalanobis distance for Scaled I networks and how well can the Scaled I network be classified compared to the Tuned E+I network? I suspect that the Scaled I network will actually be better at classifying odors compared to the E+I network. The authors might want to speculate about the benefit of having networks with both sources of inhibition (local and global) and hence being able to switch between locally defined manifolds and discrete attractor states. 

We agree that a more rigorous comparison of Tuned and Scaled networks would be of interest. We have added the variance analysis (Fig 4G) and angle distributions (Fig. 4H) for both Tuned I and Scaled networks. However, the Mahalanobis distances and Quadratic Discriminant Analysis cannot be applied to Scaled networks because their neuronal covariance matrix is low rank and not invertible_. To nevertheless compare these networks, we performed template matching by assigning test patterns to one of the four odor classes based on correlations to template patterns (Supplementary Figure 8; see also response to the first comment of reviewer 2). Interestingly, _Scaled networks performed well at classification but did not outperform Tuned networks, and exhibited disadvantages arising from attractor dynamics (Supplementary Figure 8; see also response to the first comment of reviewer 2). Furthermore, in further analyses we found that continuous representational manifolds support metric assessments of inputs relative to learned odors, which cannot be achieved by discrete representations. These results are now shown in Figure 5D-E and discussed explicitly in the text on p.11 (see also response to comment 3 of reviewer 1).

We preferred not to add a sentence in the Discussion about benefits of networks having both sources of inhibition_,_ as we find this a bit too speculative.

At a few points in the manuscript, the authors use statements without actually providing evidence in terms of a Figure. Often the authors themselves acknowledge this, by adding the term "not shown" to the end of the sentence. I believe it will be helpful to the reader to be provided with figures or panels in support of the statements.  

Thank you for this comment. We have provided additional data figures to support the following statements:

“d_M was again increased upon learning, particularly between learned odors and reference classes representing other odors (Supplementary Figure 9)”

“decreasing amplification in assemblies of Scaled networks changed transformations towards the intermediate behavior, albeit with broader firing rate distributions than in Tuned networks (Supplementary Figure 6 B)”  

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Meissner-Bernard et al present a biologically constrained model of telencephalic area of adult zebrafish, a homologous area to the piriform cortex, and argue for the role of precisely balanced memory networks in olfactory processing. 

This is interesting as it can add to recent evidence on the presence of functional subnetworks in multiple sensory cortices. It is also important in deviating from traditional accounts of memory systems as attractor networks. Evidence for attractor networks has been found in some systems, like in the head direction circuits in the flies. However, the presence of attractor dynamics in other modalities, like sensory systems, and their role in computation has been more contentious. This work contributes to this active line of research in experimental and computational neuroscience by suggesting that, rather than being represented in attractor networks and persistent activity, olfactory memories might be coded by balanced excitation-inhibitory subnetworks. 

The paper is generally well-written, the figures are informative and of good quality, and multiple approaches and metrics have been used to test and support the main results of the paper. 

The main strength of the work is in: (1) direct link to biological parameters and measurements, (2) good controls and quantification of the results, and (3) comparison across multiple models. 

(1) The authors have done a good job of gathering the current experimental information to inform a biological-constrained spiking model of the telencephalic area of adult zebrafish. The results are compared to previous experimental measurements to choose the right regimes of operation. 

(2) Multiple quantification metrics and controls are used to support the main conclusions and to ensure that the key parameters are controlled for - e.g. when comparing across multiple models.   (3) Four specific models (random, scaled I / attractor, and two variant of specific E-I networks - tuned I and tuned E+I) are compared with different metrics, helping to pinpoint which features emerge in which model. 

Major problems with the work are: (1) mechanistic explanation of the results in specific E-I networks, (2) parameter exploration, and (3) the functional significance of the specific E-I model. 

(1) The main problem with the paper is a lack of mechanistic analysis of the models. The models are treated like biological entities and only tested with different assays and metrics to describe their different features (e.g. different geometry of representation in Fig. 4). Given that all the key parameters of the models are known and can be changed (unlike biological networks), it is expected to provide a more analytical account of why specific networks show the reported results. For instance, what is the key mechanism for medium amplification in specific E/I network models (Fig. 3)? How does the specific geometry of representation/manifolds (in Fig. 4) emerge in terms of excitatory-inhibitory interactions, and what are the main mechanisms/parameters? Mechanistic account and analysis of these results are missing in the current version of the paper. 

Precise balancing of excitation and inhibition in subnetworks would lead to the cancellation of specific dynamical modes responsible for the amplification of responses (hence, deviating from the attractor dynamics with an unstable specific mode). What is the key difference in the specific E/I networks here (tuned I or/and tuned E+I) which make them stand between random and attractor networks? Excitatory and inhibitory neurons have different parameters in the model (Table 1). Time constants of inhibitory and excitatory synapses are also different (P. 13). Are these parameters causing networks to be effectively more excitation dominated (hence deviating from a random spectrum which would be expected from a precisely balanced E/I network, with exactly the same parameters of E and I neurons)? It is necessary to analyse the network models, describe the key mechanism for their amplification, and pinpoint the key differences between E and I neurons which are crucial for this. 

To address these comments we performed additional simulations and analyses at different levels. Please see our reply to comment (1) of the public review (reviewer 1) for a detailed description. We thank the reviewer for these constructive comments.

(2) The second major issue with the study is a lack of systematic exploration and analysis of the parameter space. Some parameters are biologically constrained, but not all the parameters. For instance, it is not clear what the justification for the choice of synaptic time scales are (with E synaptic time constants being larger than inhibition: tau_syn_i = 10 ms, tau_syn_E = 30 ms). How would the results change if they are varying these - and other unconstrained - parameters? It is important to show how the main results, especially the manifold localisation, would change by doing a systematic exploration of the key parameters and performing some sensitivity analysis. This would also help to see how robust the results are, which parameters are more important and which parameters are less relevant, and to shed light on the key mechanisms.  

We thank the reviewer for this comment. We have now carried out additional simulations with equal time constants for all neurons. Please see our reply to the public review for more details (comment 2 of reviewer 1).

(3) It is not clear what the main functional advantage of the specific E-I network model is compared to random networks. In terms of activity, they show that specific E-I networks amplify the input more than random networks (Fig. 3). But when it comes to classification, the effect seems to be very small (Fig. 5c). Description of different geometry of representation and manifold localization in specific networks compared to random networks is good, but it is more of an illustration of different activity patterns than proving a functional benefit for the network. The reader is still left with the question of what major functional benefits (in terms of computational/biological processing) should be expected from these networks, if they are to be a good model for olfactory processing and learning. 

One possibility for instance might be that the tasks used here are too easy to reveal the main benefits of the specific models - and more complex tasks would be needed to assess the functional enhancement (e.g. more noisy conditions or more combination of odours). It would be good to show this more clearly - or at least discuss it in relation to computation and function.

Please see our reply to the public review (comment 3 of reviewer 1).

Specific comments: 

Abstract: "resulting in continuous representations that reflected both relatedness of inputs and *an individual's experience*" 

It didn't become apparent from the text or the model where the role of "individual's experience" component (or "internal representations" - in the next line) was introduced or shown (apart from a couple of lines in the Discussion) 

We consider the scenario that that assemblies are the outcome of an experience-dependent plasticity process. To clarify this, we have now made a small addition to the text: “Biological memory networks are thought to store information by experience-dependent changes in the synaptic connectivity between assemblies of neurons.”.

P. 2: "The resulting state of "precise" synaptic balance stabilizes firing rates because inhomogeneities or fluctuations in excitation are tracked by correlated inhibition" 

It is not clear what the "inhomogeneities" specifically refers to - they can be temporal, or they can refer to the quenched noise of connectivity, for instance. Please clarify what you mean. 

The statement has been modified to be more precise: “…“precise” synaptic balance stabilizes firing rates because inhomogeneities in excitation across the population or temporal variations in excitation are tracked by correlated inhibition…”.

P. 3 (and Methods): When odour stimulus is simulated in the OB, the activity of a fraction of mitral cells is increased (10% to 15 Hz) - but also a fraction of mitral cells is suppressed (5% to 2 Hz). What is the biological motivation or reference for this? It is not provided. Is it needed for the results? Also, it is not explained how the suppressed 5% are chosen (e.g. randomly, without any relation to the increased cells?). 

We thank the reviewer for this comment. These changes in activity directly reflect experimental observations. We apologize that we forgot to include the references reporting these observations (Friedrich and Laurent, 2001 and 2004); this is now fixed.

In our simulation, OB neurons do not interact with each other, and the suppressed 5% were indeed randomly selected. We changed the text in Methods accordingly to read: “An additional 75 randomly selected mitral cells were inhibited” 

P. 4, L. 1-2: "... sparsely connected integrate-and-fire neurons with conductance-based synapses (connection probability {less than or equal to}5%)." 

Specify the connection probability of specific subtypes (EE, EI, IE, II).  

We now refer to the Methods section, where this information can be found. 

“... conductance-based synapses (connection probability ≤5%, Methods)”  

P. 4, L. 6-7: "Population activity was odor-specific and activity patterns evoked by uncorrelated OB inputs remained uncorrelated in Dp (Figure 1H)" 

What would happen to correlated OB inputs (e.g. as a result of mixture of two overlapping odours) in this baseline state of the network (before memories being introduced to it)? It would be good to know this, as it sheds light on the initial operating regime of the network in terms of E/I balance and decorrelation of inputs.  

This information was present in the original manuscript at (Figure 3) but we improved the writing to further clarify this issue: “ (…) we morphed a novel odor into a learned odor (Figure 3A), or a learned odor into another learned odor (Supplementary Figure 3B), and quantified the similarity between morphed and learned odors by the Pearson correlation of the OB activity patterns (input correlation). We then compared input correlations to the corresponding pattern correlations among E neurons in Dp (output correlation). In rand networks, output correlations increased linearly with input correlations but did not exceed them (Figure 3B and Supplementary Figure 3B)”

P. 4, L. 12-13: "Shuffling spike times of inhibitory neurons resulted in runaway activity with a probability of ~80%, .."   Where is this shown? 

(There are other occasions too in the paper where references to the supporting figures are missing). 

We now provide the statistics: “Shuffling spike times of inhibitory neurons resulted in runaway activity with a probability of 0.79 ± 0.20”

P. 4: "In each network, we created 15 assemblies representing uncorrelated odors. As a consequence, ~30% of E neurons were part of an assembly ..." 

15 x 100 / 4000 = 37.5% - so it's closer to 40% than 30%. Unless there is some overlap? 

Yes: despite odors being uncorrelated and connectivity being random, some neurons (6 % of E neurons) belong to more than one assembly.

P. 4: "When a reached a critical value of ~6, networks became unstable and generated runaway activity (Figure 2B)." 

Can this transition point be calculated or estimated from the network parameters, and linked to the underlying mechanisms causing it? 

We thank the reviewer for this interesting question. The unstability arises when inhibitions fails to counterbalance efficiently the increased recurrent excitation within Dp. The transition point is difficult to estimate, as it can depend on several parameters, including the probability of E to E connections, their strength, assembly size, and others. We have therefore not attempted to estimate it analytically.

P. 4: "Hence, non-specific scaling of inhibition resulted in a divergence of firing rates that exhausted the dynamic range of individual neurons in the population, implying that homeostatic   global inhibition is insufficient to maintain a stable firing rate distribution." 

I don't think this is justified based on the results and figures presented here (Fig. 2E) - the interpretation is a bit strong and biased towards the conclusions the authors want to draw. 

To more clearly illustrate the finding that in Scaled networks, assembly neurons are highly active (close to maximal realistic firing rates) whereas non-assembly neurons are nearly silent we have now added Supplementary Fig. 2B. Moreover, we have toned down the text: “Hence, non-specific scaling of inhibition resulted in a large and biologically unrealistic divergence of firing rates (Supplementary Figure 2B) that nearly exhausted the dynamic range of individual neurons in the population, indicating that homeostatic global inhibition is insufficient to maintain a stable firing rate distribution”

P. 5, third paragraph: Description of Figure 2I, inset is needed, either in the text or caption. 

The inset is now referred to in the text: ”we projected synaptic conductances of each neuron onto a line representing the E/I ratio expected in a balanced network (“balanced axis”) and onto an orthogonal line (“counter-balanced axis”; Figure 2I inset, Methods).”

P. 5, last paragraph: another example of writing about results without showing/referring to the corresponding figures: 

"In rand networks, firing rates increased after stimulus onset and rapidly returned to a low baseline after stimulus offset. Correlations between activity patterns evoked by the same odor at different time points and in different trials were positive but substantially lower than unity, indicating high variability ..." 

And the continuation with similar lack of references on P. 6: 

"Scaled networks responded to learned odors with persistent firing of assembly neurons and high pattern correlations across trials and time, implying attractor dynamics (Hopfield, 1982; Khona and Fiete, 2022), whereas Tuned networks exhibited transient responses and modest pattern correlations similar to rand networks." 

Please go through the Results and fix the references to the corresponding figures on all instances. 

We thank the reviewer for pointing out these overlooked figure references, which are now fixed.

P. 8: "These observations further support the conclusion that E/I assemblies locally constrain neuronal dynamics onto manifolds." 

As discussed in the general major points, mechanistic explanation in terms of how the interaction of E/I dynamics leads to this is missing. 

As discussed in the reply to the public review (comment 3 of reviewer 1), we have now provided more mechanistic analyses of our observations.

P. 9: "Hence, E/I assemblies enhanced the classification of inputs related to learned patterns."   The effect seems to be very small. Also, any explanation for why for low test-target correlation the effect is negative (random doing better than tuned E/I)? 

The size of the effect (plearned – pnovel = 0.074; difference of means; Figure 5C) may appear small in terms of absolute probability, but it is substantial relative to the maximum possible increase (1 – p_novel =  0.133; Figure 5C). The fact that for low test-target correlations the effect is negative is a direct consequence of the positive effect for high test-target correlations and the presence of 2 learned odors in the 4-way forced choice task. 

P. 9: "In Scaled I networks, creating two additional memories resulted in a substantial increase   in firing rates, particularly in response to the learned and related odors"   Where is this shown? Please refer to the figure. 

We thank the reviewer again for pointing this out. We forgot to include a reference to the relevant figure which has now been added in the revised manuscript (Figure 6C).

P. 10: "The resulting Tuned networks reproduced additional experimental observations that were not used as constraints including irregular firing patterns, lower output than input correlations, and the absence of persistent activity" 

It is difficult to present these as "additional experimental observations", as all of them are negative, and can exist in random networks too - hence cannot be used as biological evidence in favour of specific E/I networks when compared to random networks. 

We agree with the reviewer that these additional experimental observations cannot be used as biological evidence favouring Tuned E+I networks over random networks. We here just wanted to point out that additional observations which we did not take into account to fit the model are not invalidating the existence of E-I assemblies in biological networks. As assemblies tend to result in persistent activity in other types of networks, we feel that this observation is worth pointing out.

Methods: 

P. 13: Describe the parameters of Eq. 2 after the equation. 

Done.

P. 13: "The time constants of inhibitory and excitatory synapses were 10 ms and 30 ms, respectively." 

What is the (biological) justification for the choice of these parameters? 

How would varying them affect the main results (e.g. local manifolds)? 

We chose a relatively slow time constant for excitatory synapses because experimental data indicate that excitatory synaptic currents in Dp and piriform cortex contain a prominent NMDA component. We have now also simulated networks with equal time constants for excitatory and inhibitory synapses and equal biophysical parameters for excitatory and inhibitory neurons, which did not affect the main results (see also reply to the public review: comment 2 of reviewer 1).

P. 14: "Care was also taken to ensure that the variation in the number of output connections was low across neurons"   How exactly?

More detailed explanations have now been added in the Methods section: “connections of a presynaptic neuron y to postsynaptic neurons x were randomly deleted when their total number exceeded the average number of output connections by ≥5%, or added when they were lower by ≥5%.“

Reviewer #2 (Recommendations For The Authors): 

Congratulations on the great and interesting work! The results were nicely presented and the idea of continuous encoding on manifolds is very interesting. To improve the quality of the paper, in addition to the major points raised in the public review, here are some more detailed comments for the paper: 

(1) Generally, citations have to improve. Spiking networks with excitatory assemblies and different architectures of inhibitory populations have been studied before, and the claim about improved network stability in co-tuned E-I networks has been made in the following papers that need to be correctly cited: 

• Vogels TP, Sprekeler H, Zenke F, Clopath C, Gerstner W. 2011. Inhibitory Plasticity Balances Excitation and Inhibition in Sensory Pathways and Memory Networks. Science 334:1-7. doi:10.1126/science.1212991 (mentions that emerging precise balance on the synaptic weights can result in the overall network stability) 

• Lagzi F, Bustos MC, Oswald AM, Doiron B. 2021. Assembly formation is stabilized by Parvalbumin neurons and accelerated by Somatostatin neurons. bioRxiv doi: https://doi.org/10.1101/2021.09.06.459211 (among other things, contrasts stability and competition which arises from multistable networks with global inhibition and reciprocal inhibition)   • Rost T, Deger M, Nawrot MP. 2018. Winnerless competition in clustered balanced networks: inhibitory assemblies do the trick. Biol Cybern 112:81-98. doi:10.1007/s00422-017-0737-7 (compares different architectures of inhibition and their effects on network dynamics) 

• Lagzi F, Fairhall A. 2022. Tuned inhibitory firing rate and connection weights as emergent network properties. bioRxiv 2022.04.12.488114. doi:10.1101/2022.04.12.488114 (here, see the eigenvalue and UMAP analysis for a network with global inhibition and E/I assemblies) 

Additionally, there are lots of pioneering work about tracking of excitatory synaptic inputs by inhibitory populations, that are missing in references. Also, experimental work that show existence of cell assemblies in the brain are largely missing. On the other hand, some references that do not fit the focus of the statements have been incorrectly cited. 

The authors may consider referencing the following more pertinent studies on spiking networks to support the statement regarding attractor dynamics in the first paragraph in the Introduction (the current citations of Hopfield and Kohonen are for rate-based networks): 

• Wong, K.-F., & Wang, X.-J. (2006). A recurrent network mechanism of time integration in perceptual decisions. Journal of Neuroscience, 26(4), 1314-1328. https://doi.org/10.1523/JNEUROSCI.3733-05.2006 

• Wang, X.-J. (2008). Decision making in recurrent neuronal circuits. Neuron, 60(2), 215-234. https://doi.org/10.1016/j.neuron.2008.09.034  

• F. Lagzi, & S. Rotter. (2015). Dynamics of competition between subnetworks of spiking neuronal networks in the balanced state. PloS One. 

• Goldman-Rakic, P. S. (1995). Cellular basis of working memory. Neuron, 14(3), 477-485. 

• Rost T, Deger M, Nawrot MP. 2018. Winnerless competition in clustered balanced networks: inhibitory assemblies do the trick. Biol Cybern 112:81-98. doi:10.1007/s00422-017-0737-7. 

• Amit DJ, Tsodyks M (1991) Quantitative study of attractor neural network retrieving at low spike rates: I. substrate-spikes, rates and neuronal gain. Network 2:259-273. 

• Mazzucato, L., Fontanini, A., & La Camera, G. (2015). Dynamics of Multistable States during Ongoing and Evoked Cortical Activity. Journal of Neuroscience, 35(21), 8214-8231. 

We thank the reviewer for the references suggestions. We have carefully reviewed the reference list and made the following changes, which we hope address the reviewer’s concerns:

(1) We adjusted References about network stability in co-tuned E-I networks.

(2) We added the Lagzi & Rotter (2015), Amit et al. (1991), Mazzucato et al. (2015) and GoldmanRakic (1995) papers in the Introduction as studies on attractor dynamics in spiking neural networks. We preferred to omit the two X.J Wang papers, as they describe attractors in decision making rather than memory processes.

(3) We added the Ko et al. 2011 paper as experimental evidence for assemblies in the brain. In our view, there are few experimental studies showing the existence of cell assemblies in the brain, which we distinguish from cell ensembles, group of coactive neurons. 

(4) We also included Hennequin 2018, Brunel 2000, Lagzi et al. 2021 and Eckmann et al. 2024, which we had not cited in the initial manuscript.

(5) We removed the Wiechert et al. 2010 reference as it does not support the statement about geometry-preserving transformation by random networks.

(2) The gist of the paper is about how the architecture of inhibition (reciprocal vs. global in this case) can determine network stability and salient responses (related to multistable attractors and variations) for classification purposes. It would improve the narrative of the paper if this point is raised in the Introduction and Discussion section. Also see a relevant paper that addresses this point here: 

Lagzi F, Bustos MC, Oswald AM, Doiron B. 2021. Assembly formation is stabilized by Parvalbumin neurons and accelerated by Somatostatin neurons. bioRxiv doi: https://doi.org/10.1101/2021.09.06.459211 

Classification has long been proposed to be a function of piriform cortex and autoassociative memory networks in general, and we consider it important. However, the computational function of Dp or piriform cortex is still poorly understood, and we do not focus only on odor classification as a possibility. In fact, continuous representational manifolds also support other functions such as the quantification of distance relationships of an input to previously memorized stimuli, or multi-layer network computations (including classification). In the revised manuscript, we have performed additional analyses to explore these notions in more detail, as explained above (response to public reviews, comment 3 of reviewer 1). Furthermore, we have now expanded the discussion of potential computational functions of Tuned networks and explicitly discuss classification but also other potential functions. 

(3) A plot for the values of the inhibitory conductances in Figure 1 would complete the analysis for that section. 

In Figure 1, we decided to only show the conductances that we use to fit our model, namely the afferent and total synaptic conductances. As the values of the inhibitory conductances can be derived from panel E, we refrained from plotting them separately for the sake of simplicity. 

(4) How did the authors calculate correlations between activity patterns as a function of time in Figure 2E, bottom row? Does the color represent correlation coefficient (which should not be time dependent) or is it a correlation function? This should be explained in the Methods section. 

The color represents the Pearson correlation coefficient between activity patterns within a narrow time window (100 ms). We updated the Figure legend to clarify this: “Mean correlation between activity patterns evoked by a learned odor at different time points during odor presentation. Correlation coefficients were calculated between pairs of activity vectors composed of the mean firing rates of E neurons in 100 ms time bins. Activity vectors were taken from the same or different trials, except for the diagonal, where only patterns from different trials were considered.”

(5) Figure 3 needs more clarification (both in the main text and the figure caption). It is not clear what the axes are exactly, and why the network responses for familiar and novel inputs are different. The gray shaded area in panel B needs more explanation as well.  

We thank the reviewer for the comment. We have improved Figure 3A, the figure caption, as well as the text (see p.6). We hope that the figure is now clearer.

(6) The "scaled I" network, known for representing input patterns in discrete attractors, should exhibit clear separation between network responses in the 2D PC space in the PCA plots. However, Figure 4D and Figure 6D do not reflect this, as all network responses are overlapped. Can the authors explain the overlap in Figure 4D? 

In Figure 4D, activity of Scaled networks is distributed between three subregions in state space that are separated by the first 2 PCs. Two of them indeed correspond to attractor states representing the two learned odors while the third represents inputs that are not associated with these attractor states. To clarify this, please see also the density plot in Figure 4E. The few datapoints between these three subregions are likely outliers generated by the sequential change in inputs, as described in Supplementary Figure 8C.

(7) The reason for writing about the ISN networks is not clear. Co-tuned E-I assemblies do not necessarily have to operate in this regime. Also, the results of the paper do not rely on any of the properties of ISNs, but they are more general. Authors should either show the paradoxical effect associated with ISN (i.e., if increasing input to I neurons decreases their responses) or show ISN properties using stability analysis (See computational research conducted at the Allen Institute, namely Millman et al. 2020, eLife ). Currently, the paper reads as if being in the ISN regime is a necessary requirement, which is not true. Also, the arguments do not connect with the rest of the paper and never show up again. Since we know it is not a requirement, there is no need to have those few sentences in the Results section. Also, the choice of alpha=5.0 is extreme, and therefore, it would help to judge the biological realism if the raster plots for Figs 2-6 are shown.

We have toned down the part on ISN and reduced it to one sentence for readers who might be interested in knowing whether activity is inhibition-stabilized or not. We have also added the reference to the Tsodyks et al. 1997 paper from which we derive our stability analysis. The text now reads “Hence, pDp_sim entered a balanced state during odor stimulation (Figure 1D, E) with recurrent input dominating over afferent input, as observed in pDp (Rupprecht and Friedrich, 2018). Shuffling spike times of inhibitory neurons resulted in runaway activity with a probability of 0.79 ± 0.20, demonstrating that activity was inhibition-stabilized (Sadeh and Clopath, 2020b, Tsodyks et al., 1997).”  

We have now also added the raster plots as suggested by the reviewer (see Figure 2D, Supplementary Figure 1 G, Supplementary Figure 4). We thank the reviewer for this comment.

(8) In the abstract, authors mention "fast pattern classification" and "continual learning," but in the paper, those issues have not been addressed. The study does not include any synaptic plasticity. 

Concerning “continual learning” we agree that we do not simulate the learning process itself. However, Figure 6 show results of a simulation where two additional patterns were stored in a network that already contained assemblies representing other odors. We consider this a crude way of exploring the end result of a “continual learning” process. “Fast pattern classification” is mentioned because activity in balanced networks can follow fluctuating inputs with high temporal resolution, while networks with stable attractor states tend to be slow. This is likely to account for the occurrence of hysteresis effects in Scaled but not Tuned networks as shown in Supplementary

Fig. 8.

(9) In the Introduction, the first sentence in the second paragraph reads: "... when neurons receive strong excitatory and inhibitory synaptic input ...". The word strong should be changed to "weak".

Also, see the pioneering work of Brunel 2000. 

In classical balanced networks, strong excitatory inputs are counterbalanced by strong inhibitory inputs, leading to a fluctuation-driven regime. We have added Brunel 2000.

(10) In the second paragraph of the introduction, the authors refer to studies about structural co-tuning (e.g., where "precise" synaptic balance is mentioned, and Vogels et al. 2011 should be cited there) and functional co-tuning (which is, in fact, different than tracking of excitation by inhibition, but the authors refer to that as co-tuning). It makes it easier to understand which studies talk about structural co-tuning and which ones are about functional co-tuning. The paper by Znamenski 2018, which showed both structural and functional tuning in experiments, is missing here. 

We added the citation to the now published paper by Znamenskyi et al. (2024).  

(11) The third paragraph in the Introduction misses some references that address network dynamics that are shaped by the inhibitory architecture in E/I assemblies in spiking networks, like Rost et al 2018 and Lagzi et al 2021. 

These references have been added.

(12) The last sentence of the fourth paragraph in the Introduction implies that functional co-tuning is due to structural co-tuning, which is not necessarily true. While structural co-tuning results in functional co-tuning, functional co-tuning does not require structural co-tuning because it could arise from shared correlated input or heterogeneity in synaptic connections from E to I cells.  

We generally agree with the reviewer, but we are uncertain which sentence the reviewer refers to.

We assume the reviewer refers to the last sentence of the second (rather than the fourth paragraph), which explicitly mentions the “…structural basis of E/I co-tuning…”. If so, we consider this sentence still correct because the “structural basis” refers not specifically to E/I assemblies, but also includes any other connectivity that may produce co-tuning, including the connectivity underlying the alternative possibilities mentioned by the reviewer (shared correlated input or heterogeneity of synaptic connections).

(13) In order to ensure that the comparison between network dynamics is legit, authors should mention up front that for all networks, the average firing rates for the excitatory cells were kept at 1 Hz, and the background input was identical for all E and I cells across different networks.

We slightly revised the text to make this more clear “We (…) uniformly scaled I-to-E connection weights by a factor of χ until E population firing rates in response to learned odors matched the corresponding firing rates in rand networks, i.e., 1 Hz”

(14) In the last paragraph on page 5, my understanding was that an individual odor could target different cells within an assembly in different trials to generate trial to trail variability. If this is correct, this needs to be mentioned clearly. 

This is not correct, an odor consists of 150 activated mitral cells with defined firing rates. As now mentioned in the Methods, “Spikes were then generated from a Poisson distribution, and this process was repeated to create trial-to-trial variability.”

(15) The last paragraph on page 6 mentions that the four OB activity patterns were uncorrelated but if they were designed as in Figure 4A, dues to the existing overlap between the patterns, they cannot be uncorrelated. 

This appears to be a misunderstanding. We mention in the text (and show in Figure 4B) that the four odors which “… were assigned to the corners of a square…” are uncorrelated.  The intermediate odors are of course not uncorrelated. We slightly modified the corresponding paragraph (now on page 7) to clarify this: “The subspace consisted of a set of OB activity patterns representing four uncorrelated pure odors and mixtures of these pure odors. Pure odors were assigned to the corners of a square and mixtures were generated by selecting active mitral cells from each of the pure odors with probabilities depending on the relative distances from the corners (Figure 4A, Methods).”

(16) The notion of "learned" and "novel" odors may be misleading as there was no plasticity in the network to acquire an input representation. It would be beneficial for the authors to clarify that by "learned," they imply the presence of the corresponding E assembly for the odor in the network, with the input solely impacting that assembly. Conversely, for "novel" inputs, the input does not target a predefined assembly. In Figure 2 and Figure 4, it would be especially helpful to have the spiking raster plots of some sample E and I cells.  

As suggested by the reviewer, we have modified the existing spiking raster plots in Figure 2, such that they include examples of responses to both learned and novel odors. We added spiking raster plots showing responses of I neurons to the same odors in Supplementary Figure 1F, as well as spiking raster plots of E neurons in Supplementary Figure 4A. To clarify the usage of “learned” and “novel”, we have added a sentence in the Results section: “We thus refer to an odor as “learned” when a network contains a corresponding assembly, and as “novel” when no such assembly is present.”.

(17) In the last paragraph of page 8, can the authors explain where the asymmetry comes from? 

As mentioned in the text, the asymmetry comes from the difference in the covariance structure of different classes. To clarify, we have rephrased the sentence defining the Mahalanobis distance: 

“This measure quantifies the distance between the pattern and the class center, taking into account covariation of neuronal activity within the class. In bidirectional comparisons between patterns from different classes, the mean dM may be asymmetric if neural covariance differs between classes.”

(18) The first paragraph of page 9: random networks are not expected to perform pattern classification, but just pattern representation. It would have been better if the authors compared Scaled I network with E/I co-tuned network. Regardless of the expected poorer performance of the E/I co-tuned networks, the result would have been interesting. 

Please see our reply to the public review (reviewer 2).

(19) Second paragraph on page 9, the authors should provide statistical significance test analysis for the statement "... was significantly higher ...". 

We have performed a Wilcoxon signed-rank test, and reported the p-value in the revised manuscript (p < 0.01). 

(20) The last sentence in the first paragraph on page 11 is not clear. What do the authors mean by "linearize input-output functions", and how does it support their claim? 

We have now amended this sentence to clarify what we mean: “…linearize the relationship between the mean input and output firing rates of neuronal populations…”.

(21) In the first sentence of the last paragraph on page 11, the authors mentioned “high variability”, but it is not clear compared with which of the other 3 networks they observed high variability.

Structurally co-tuned E/I networks are expected to diminish network-level variability. 

“High variability” refers to the variability of spike trains, which is now mentioned explicity in the text. We hope this more precise statement clarifies this point.

(22) Methods section, page 14: "firing rates decreased with a time constant of 1, 2 or 4 s". How did they decrease? Was it an implementation algorithm? The time scale of input presentation is 2 s and it overlaps with the decay time constant (particularly with the one with 4 s decrease).  

Firing rates decreased exponentially. We have added this information in the Methods section.

Reviewer #3 (Recommendations For The Authors): 

In the following, I suggest minor corrections to each section which I believe can improve the manuscript. 

- There was no github link to the code in the manuscript. The code should be made available with a link to github in the final manuscript. 

The code can be found here: https://github.com/clairemb90/pDp-model. The link has been added in the Methods section.

Figure 1: 

- Fig. 1A: call it pDp not Dp. Please check if this name is consistent in every figure and the text. 

Thank you for catching this. Now corrected in Figure 1, Figure 2 and in the text.

- The authors write: "Hence, pDpsim entered an inhibition-stabilized balanced state (Sadeh and Clopath, 2020b) during odor stimulation (Figure 1D, E)." and then later "Shuffling spike times of inhibitory neurons resulted in runaway activity with a probability of ~80%, demonstrating that activity was indeed inhibition-stabilized. These results were robust against parameter variations (Methods)." I would suggest moving the second sentence before the first sentence, because the fact that the network is in the ISN regime follows from the shuffled spike timing result. 

Also, I'd suggest showing this as a supplementary figure. 

We thank the reviewer for this comment. We have removed “inhibition-stabilized” in the first sentence as there is no strong evidence of this in Rupprecht and Friedrich, 2018. And removed “indeed” in the second sentence. We also provided more detailed statistics. The text now reads “Hence, pDpsim entered a balanced state during odor stimulation (Figure 1D, E) with recurrent input dominating over afferent input, as observed in pDp (Rupprecht and Friedrich, 2018). Shuffling spike times of inhibitory neurons resulted in runaway activity with a probability of 0.79 ± 0.20, demonstrating that activity was inhibition-stabilized (Sadeh and Clopath, 2020b).”

Figure 2: 

- "... Scaled I networks (Figure 2H." Missing ) 

Corrected.

- The authors write "Unlike in Scaled I networks, mean firing rates evoked by novel odors were indistinguishable from those evoked by learned odors and from mean firing rates in rand networks (Figure 2F)." 

Why is this something you want to see? Isn't it that novel stimuli usually lead to high responses? Eg in the paper Schulz et al., 2021 (eLife) which is also cited by the authors it is shown that novel responses have high onset firing rates. I suggest clarifying this (same in the context of Fig. 3C). 

In Dp and piriform cortex, firing rates evoked by learned odors are not substantially different from firing rates evoked by novel odors. While small differences between responses to learned versus novel odors cannot be excluded, substantial learning-related differences in firing rates, as observed in other brain areas, have not been described in Dp or piriform cortex. We added references in the last paragraph of p.5. Note that the paper by Schulz et al. (2021) models a different type of circuit.  

- Fig. 2B: Indicate in figure caption that this is the case "Scaled I" 

This is not exactly the case “Scaled I”, as the parameter 𝝌𝝌 (increased I to E strength) is set to 1.

- Suppl Fig. 2I: Is E&F ever used in the manuscript? I couldn't find a reference. I suggest removing it if not needed. 

Suppl. Fig 2I E&F is now Suppl Fig.1G&H. We now refer to it in the text: “Activity of networks with E assemblies could not be stabilized around 1 Hz by increasing connectivity from subsets of I neurons receiving dense feed-forward input from activated mitral cells (Supplementary Figure 1GH; Sadeh and Clopath, 2020).”

Figure 3: 

- As mentioned in my comment in the public review section, I find the arguments about pattern completion a little bit confusing. For me it's not clear why an increase of output correlations over input correlations is considered "pattern completion" (this is not to say that I don't find the nonlinear increase of output correlations interesting). For me, to test pattern completion with second-order statistics one would need to do a similar separation as in Suppl Fig. 3, ie measuring the pairwise correlation at cells in the assembly L that get direct input from L OB with cells in the assembly L that do not get direct input from OB. If the pairwise correlations of assembly cells which do not get direct input from OB increase in correlations, I would consider this as pattern completion (similar to the argument that increase in firing rate in cells which are not directly driven by OB are considered a sign of pattern completion). 

Also, for me it now seems like that there are contradictory results, in Fig. 3 only Scaled I can lead to pattern completion while in the context of Suppl. Fig. 3 the authors write "We found that assemblies were recruited by partial inputs in all structured pDpsim networks (Scaled and Tuned) without a significant increase in the overall population activity (Supplementary Figure 3A)."   I suggest clarifying what the authors exactly mean by pattern completion, why the increase of output correlations above input correlations can be considered as pattern completion, and why the results differs when looking at firing rates versus correlations. 

Please see our reply to the public review (reviewer 3).

- I actually would suggest adding Suppl. Fig. 3 to the main figure. It shows a more intuitive form of pattern completion and in the text there is a lot of back and forth between Fig. 3 and Suppl. Fig. 3 

We feel that the additional explanations and panels in Fig.3 should clarify this issue and therefore prefer to keep Supplementary Figure 3 as part of the Supplementary Figures for simplicity.  

- In the whole section "We next explored effects of assemblies ... prevented strong recurrent amplification within E/I assemblies." the authors could provide a link to the respective panel in Fig. 2 after each statement. This would help the reader follow your arguments. 

We thank the reviewer for pointing this out. The references to the appropriate panels have been added. 

- Fig. 3A: I guess the x-axis has been shifted upwards? Should be at zero. 

We have modified the x-axis to make it consistent with panels B and C.  

- Fig. 3B: In the figure caption, the dotted line is described as the novel odor but it is actually the unit line. The dashed lines represent the reference to the novel odor. 

Fixed.

- Fig. 3C: The " is missing for Pseudo-Assembly N

Fixed.

- "...or a learned odor into another learned odor." Have here a ref to the Supplementary Figure 3B.

Added.

Figure 4:   

- "This geometry was largely maintained in the output of rand networks, consistent with the notion that random networks tend to preserve similarity relationships between input patterns (Babadi and Sompolinsky, 2014; Marr, 1969; Schaffer et al., 2018; Wiechert et al., 2010)." I suggest adding here reference to Fig. 4D (left). 

Added.

- Please add a definition of E/I assemblies. How do the authors define E/I assemblies? I think they consider both, Tuned I and Tuned E+I as E/I assemblies? In Suppl. Fig. 2I E it looks like tuned feedforward input is defined as E/I assemblies. 

We thank the reviewer for pointing this out. E/I assemblies are groups of E and I neurons with enhanced connectivity. In other words, in E/I assemblies, connectivity is enhanced not only between subsets of E neurons, but also between these E neurons and a subset of I neurons. This is now clarified in the text: “We first selected the 25 I neurons that received the largest number of connections from the 100 E neurons of an assembly. To generate E/I assemblies, the connectivity between these two sets of neurons was then enhanced by two procedures.”. We removed “E/I assemblies” in Suppl. Fig.2, where the term was not used correctly, and apologize for the confusion.

- Suppl. Fig. 4: Could the authors please define what they mean by "Loadings" 

The loadings indicate the contribution of each neuron to each principal component, see adjusted legend of Suppl. Fig. 4: “G. Loading plot: contribution of neurons to the first two PCs of a rand and a Tuned E+I network (Figure 4D).”

- Fig. 4F: The authors might want to normalize the participation ratio by the number of neurons (see e.g. Dahmen et al., 2023 bioRxiv, "relative PR"), so the PR is bound between 0 and 1 and the dependence on N is removed. 

We thank the reviewer for the suggestion, but we prefer to use the non-normalized PR as we find it more easily interpretable (e.g. number of attractor states in Scaled networks).

- Fig. 4G&H: as mentioned in the public review, I'd add the case of Scaled I to be able to compare it to the Tuned E+I case. 

As already mentioned in the public review, we thank the reviewer for this suggestion, which we have implemented.

- Figure caption Fig. 4H "Similar results were obtained in the full-dimensional space." I suggest showing this as a supplemental panel. 

Since this only adds little information, we have chosen not to include it as a supplemental panel to avoid overloading the paper with figures.

Figure 5: 

- As mentioned in the public review, I suggest that the authors add the Scaled I case to Fig. 5 (it's shown in all figures and also in Fig. 6 again). I guess for Scaled I the separation between L and M will be very good? 

Please see our reply to the public review (reviewer 3).

- Fig. 5A&B: I am a bit confused about which neurons are drawn to calculate the Mahalanobis distance. In Fig. 5A, the schematic indicates that the vector B from which the neurons are drawn is distinct from the distribution Q. For the example of odor L, the distribution Q consists of pure odor L with odors that have little mixtures with the other odors. But the vector v for odor L seems to be drawn only from odors that have slightly higher mixtures (as shown in the schematic in Fig. 5A). Is there a reason to choose the vector v from different odors than the distribution Q? 

The distribution Q and the vector v consist of activity patterns across the same neurons in response to different odors. The reason to choose a different odor for v was to avoid having this test datapoint being included in the distribution Q. We also wanted Q to be the same for all test datapoints. 

What does "drawn from whole population" mean? Does this mean that the vectors are drawn from any neuron in pDp? If yes, then I don't understand how the authors can distinguish between different odors (L,M,O,N) on the y-axis. Or does "whole population" mean that the vector is drawn across all assemblies as shown in the schematic in Fig. 5A and the case "neurons drawn from (pseudo-) assembly" means that the authors choose only one specific assembly? In any case, the description here is a bit confusing, I think it would help the reader to clarify those terms better.  

Yes, “drawn from whole population” means that we randomly draw 80 neurons from the 4000 E neurons in pDp. The y-axis means that we use the activity patterns of these neurons evoked by one of the 4 odors (L, M, N, O) as reference. We have modified the Figure legend to clarify this: “d_M was computed based on the activity patterns of 80 E neurons drawn from the four (pseudo-) assemblies (top) or from the whole population of 4000 E neurons (bottom). Average of 50 draws.”

- Suppl Fig. 5A: In the schematic the distance is called d_E(\bar{Q},\bar{V}) while the colorbar has d_E(\bar{Q},\bar{Q}) with the Qs in different color. The green Q should be a V. 

We thank the reviewer for spotting this mistake, it is now fixed.

- Fig. 5: Could the authors comment on the fact that a random network seems to be very good in classifying patterns on it's own. Maybe in the Discussion? 

The task shown in Figure 5 is a relatively easy one, a forced-choice between four classes which are uncorrelated. In Supplementary Figure 9, we now show classification for correlated classes, which is already much harder.

Figure 6: 

- Is the correlation induced by creating mixtures like in the other Figures? Please clarify how the correlations were induced. 

We clarified this point in the Methods section: “The pixel at each vertex corresponded to one pure odor with 150 activated and 75 inhibited mitral cells (…) and the remaining pixels corresponded to mixtures. In the case of correlated pure odors (Figure 6), adjacent pure odors shared half of their activated and half of their inhibited cells.”. An explicit reference to the Methods section has also been added to the figure legend.

- Fig. 6C (right): why don't we see the clear separation in PC space as shown in Fig. 4? Is this related to the existence of correlations? Please clarify. 

Yes. The assemblies corresponding to the correlated odors X and Y overlap significantly, and therefore responses to these odors cannot be well separated, especially for Scaled networks. We added the overlap quantification in the Results section to make this clear. “These two additional assemblies had on average 16% of neurons in common due to the similarity of the odors.”

- "Furthermore, in this regime of higher pattern similarity, dM was again increased upon learning, particularly between learned odors and reference classes representing other odors (not shown)." Please show this (maybe as a supplemental figure). 

We now show the data in Supplementary Figure 9.

Discussion: 

- The authors write: "We found that transformations became more discrete map-like when amplification within assemblies was increased and precision of synaptic balance was reduced. Likewise, decreasing amplification in assemblies of Scaled networks changed transformations towards the intermediate behavior, albeit with broader firing rate distributions than in Tuned networks (not shown)." 

Where do I see the first point? I guess when I compare in Fig. 4D the case of Scaled I vs Tuned E+I, but the sentence above sounds like the authors showed this in a more step-wise way eg by changing the strength of \alpha or \beta (as defined in Fig. 1). 

Also I think if the authors want to make the point that decreasing amplification in assemblies changes transformation with a different rate distribution in scaled vs tuned networks, the authors should show it (eg adding a supplemental figure). 

The first point is indeed supported by data from different figures. Please note that the revised manuscript now contains further simulations that reinforce this statement, particularly those shown in Supplementary Figure 6, and that this point is now discussed more extensively in the Discussion. We hope that these revisions clarify this general point.

The data showing effects of decreasing amplification in assemblies is now shown in Supplementary Figure 6 (Scaled[adjust])

- I suggest adding the citation Znamenskiy et al., 2024 (Neuron; https://doi.org/10.1016/j.neuron.2023.12.013), which shows that excitatory and inhibitory (PV) neurons with functional similarities are indeed strongly connected in mouse V1, suggesting the existence of E/I assembly structure also in mammals.

Done.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors intended to investigate the earliest mechanisms enabling self-prioritization, especially in the attention. Combining a temporal order judgement task with computational modelling based on the Theory of Visual Attention (TVA), the authors suggested that the shapes associated with the self can fundamentally alter the attentional selection of sensory information into awareness. This self-prioritization in attentional selection occurs automatically at early perceptual stages. Furthermore, the processing benefits obtained from attentional selection via self-relatedness and physical salience were separated from each other.

Strengths:

The manuscript is written in a way that is easy to follow. The methods of the paper are very clear and appropriate.

Thank you for your valuable feedback and helpful suggestions. Please see specific answers below.

Weaknesses:

There are two main concerns:

(1) The authors had a too strong pre-hypothesis that self-prioritization was associated with attention. They used the prior entry to consciousness (awareness) as an index of attention, which is not appropriate. There may be other processing that makes the stimulus prior to entry to consciousness (e.g. high arousal, high sensitivity), but not attention. The self-related/associated stimulus may be involved in such processing but not attention to make the stimulus easily caught. Perhaps the authors could include other methods such as EEG or MEG to answer this question.

We found the possibility of other mechanisms to be responsible for “prior entry” interesting too, but believe there are solid grounds for the hypothesis that it is indicative of attention:

First, prior entry has a long-standing history as in index of attention (e.g., Titchener, 1903; Shore et al., 2001; Yates and Nicholls, 2009; Olivers et al. 2011; see Spence & Parise, 2010, for a review.) Of course, other factors (like the ones mentioned) can contribute to encoding speed. However, for the perceptual condition, we systematically varied a stimulus feature that is associated with selective attention (salience, see e.g. Wolfe, 2021) and kept other features that are known to be associated with other factors such as arousal and sensitivity constant across the two variants (e.g. clear over threshold visibility) or varied them between participants (e.g. the colours / shapes used).

Second, in the social salience condition we used a manipulation that has repeatedly been used to establish social salience effects in other paradigms (e.g., Li et al., 2022; Liu & Sui, 2016; Scheller et al., 2024; Sui et al., 2015; see Humphreys & Sui, 2016, for a review). We assume that the reviewer’s comment suggests that changes in arousal or sensitivity may be responsible for social salience effects, specifically. We have several reasons to interpret the social salience effects as an alteration in attentional selection, rather than a result of arousal or sensitivity:

Arousal and attention are closely linked. However, within the present model, arousal is more likely linked to the availability of processing resources (capacity parameter C). That is, enhanced arousal is typically not stimulus-specific, and therefore unlikely affects the *relative* advantage in processing weights/rates of the self-associated (vs other-associated) stimuli. Indeed, a recent study showed that arousal does not modulate the relative division of attentional resources (as modelled by the Theory of Visual Attention; Asgeirsson & Nieuwenhuis, 2017). As such, it is unlikely that arousal can explain the observed results in relative processing changes for the self and other identities.

Further, there is little reason to assume that presenting a different shape enhances perceptual sensitivity. Firstly, all stimuli were presented well above threshold, which would shrink any effects that were resulting from increases in sensitivity alone. Secondly, shape-associations were counterbalanced across participants, reducing the possibility that specific features, present in the stimulus display, lead to the measurable change in processing rates as a result of enhanced shape-sensitivity.

Taken together, both, the wealth of literature that suggests prior entry to index attention and the specific design choices within our study, strongly support the notion that the observed changes in processing rates are indicative of changes in attentional selection, rather than other mechanisms (e.g. arousal, sensitivity).

(2) The authors suggested that there are two independent attention processes. I suspect that the brain needs two attention systems. Is there a probability that the social and perceptual (physical properties of the stimulus) salience fired the same attention processing through different processing?

We appreciate this thought-provoking comment. We conceptualize attention as a process that can facilitate different levels of representation, rather than as separate systems tuned to specific types of information. Different forms of representation, such as the perceptual shape, or the associated social identity, may be impacted by the same attentional process at different levels of representation. Indeed, our findings suggest that both social and perceptual salience effects may result from the same attentional system, albeit at different levels of representation. This is further supported by the additivity of perceptual and social salience effects and the negative correlation of processing facilitations between perceptually and socially salient cues. These results may reflect a trade-off in how attentional resources are distributed between either perceptually or socially salient stimuli.

Reviewer #2 (Public review):

Summary:

The main aim of this research was to explore whether and how self-associations (as opposed to other associations) bias early attentional selection, and whether this can explain well-known self-prioritization phenomena, such as the self-advantage in perceptual matching tasks. The authors adopted the Visual Attention Theory (VAT) by estimating VAT parameters using a hierarchical Bayesian model from the field of attention and applied it to investigate the mechanisms underlying self-prioritization. They also discussed the constraints on the self-prioritization effect in attentional selection. The key conclusions reported were:

(1) Self-association enhances both attentional weights and processing capacity

(2) Self-prioritization in attentional selection occurs automatically but diminishes when active social decoding is required, and

(3) Social and perceptual salience capture attention through distinct mechanisms.

Strengths:

Transferring the Theory of Visual Attention parameters estimated by a hierarchical Bayesian model to investigate self-prioritization in attentional selection was a smart approach. This method provides a valuable tool for accessing the very early stages of self-processing, i.e., attention selection. The authors conclude that self-associations can bias visual attention by enhancing both attentional weights and processing capacity and that this process occurs automatically. These findings offer new insights into self-prioritization from the perspective of the early stage of attentional selection.

Thank you for your valuable feedback and helpful suggestions. Please see specific answers below.

Weaknesses:

(1) The results are not convincing enough to definitively support their conclusions. This is due to inconsistent findings (e.g., the model selection suggested condition-specific c parameters, but the increase in processing capacity was only slight; the correlations between attentional selection bias and SPE were inconsistent across experiments), unexpected results (e.g., when examining the impact of social association on processing rates, the other-associated stimuli were processed faster after social association, while the self-associated stimuli were processed more slowly), and weak correlations between attentional bias and behavioral SPE, which were reported without any p-value corrections. Additionally, the reasons why the attentional bias of self-association occurs automatically but disappears during active social decoding remain difficult to explain. It is also possible that the self-association with shapes was not strong enough to demonstrate attention bias, rather than the automatic processes as the authors suggest. Although these inconsistencies and unexpected results were discussed, all were post hoc explanations. To convince readers, empirical evidence is needed to support these unexpected findings.

Thank you for outlining the specific points that raise your concern. We were happy to address these points as follows:

a. Replications and Consistency: In our study, we consistently observed trends (relative reduction in processing speed of the self-associated stimulus) in the social salience conditions across experiments. While Experiment 2 demonstrated a significant reduction in processing rate towards self-stimuli, there was a notable trend in Experiment 1 as well.

b. Condition-specific parameters: The condition-specific C parameters, though presenting a small effect size, significantly improved model fit. Inspecting the HDI ranges of our estimated C parameters indicates a high probability (85-89%) that processing capacity increased due to social associations, suggesting that even small changes (~2Hz) can hold meaningful implications within the context attentional selection.

Please also note that the main conclusions about relative salience (self/other, salient/non-salient) are based on the relative processing rates. Processing rates are the product of the processing capacity (condition- but not stimulus dependent) and the attentional weight (condition and stimulus dependent). The latter is crucial to judge the *relative* advantage of the salient stimulus. Hence, the self-/salient stimulus advantage that is reflected in the ‘processing rate difference’ is automatically also reflected in the relative attentional weights attributed to the self/other and salient/non-salient stimuli. As such, the overall results of an automatic relative advantage of self-associated stimuli hold, independently of the change in overall processing capacity.

c. Correlations: Regarding the correlations the reviewer noted, we wish to clarify that these were exploratory, and not the primary focus of our research. The aim of these exploratory analyses was to gauge the contribution of attentional selection to matching-based SPEs. As SPEs measured via the matching task are typically based on multiple different levels of processing, the contribution of early attentional selection to their overall magnitude was unclear. Without being able to gauge the possible effect sizes, corrected analyses may prevent detecting small but meaningful effects. As such, the effect sizes reported serve future studies to estimate power a priori and conduct well-powered replications of such exploratory effects. Additionally, Bayes factors were provided to give an appreciation of the strength of the evidence, all suggesting at least moderate evidence in favour of a correlation. Lastly, please note that effects that were measured within individuals and task (processing rate increase in social and perceptual decision dimensions in the TOJ task) showed consistent patterns, suggesting that the modulations within tasks were highly predictive of each other, while the modulations between tasks were not as clearly linked. We will add this clarification to the revised manuscript.

d. Unexpected results: The unexpected results concerning the processing rates of other-associated versus self-associated stimuli certainly warrant further discussion. We believe that the additional processing steps required for social judgments, reflected in enhanced reaction times, may explain the slower processing of self-associated stimuli in that dimension. We agree that not all findings will align with initial hypotheses, and this variability presents avenues for further research. We have added this to the discussion of social salience effects.

e. Whether association strength can account for the findings: We appreciate the scepticism regarding the strength of self-association with shapes. However, our within-participant design and control matching task indicate that the relative processing advantage for self-associated stimuli holds across conditions. This makes the scenario that “the self-association with shapes was not strong enough to demonstrate attention bias” very unlikely. Firstly, the relative processing advantage of self-associated stimuli in the perceptual decision condition, and the absence of such advantage in the social decision condition, were evidenced in the same participants. Hence, the strength of association between shapes and social identities was the same for both conditions. However, we only find an advantage for the self-associated shape when participants make perceptual (shape) judgements. It is therefore highly unlikely that the “association strength” can account for the difference in the outcomes between the conditions in experiment 1. Also, note that the order in which these conditions were presented was counter-balanced across participants, reducing the possibility that the automatic self-advantage was merely a result of learning or fatigue. Secondly, all participants completed the standard matching task to ascertain that the association between shapes and identities did indeed lead to processing advantages (across different levels).

In summary, we believe that the evidence we provide supports the final conclusions. We do, of course, welcome any further empirical evidence that could enhance our understanding of the contribution of different processing levels to the SPE and are committed to exploring these areas in future work.

(2) The generalization of the findings needs further examination. The current results seem to rely heavily on the perceptual matching task. Whether this attentional selection mechanism of self-prioritization can be generalized to other stimuli, such as self-name, self-face, or other domains of self-association advantages, remains to be tested. In other words, more converging evidence is needed.

The reviewer indicates that the current findings heavily rely on the perceptual matching task, and it would be more convincing to include other paradigm(s) and different types of stimuli. We are happy to address these points here: first, we specifically used a temporal order paradigm to tap into specific processes, rather than merely relying on the matching task. Attentional selection is, along with other processes, involved in matching, but the TOJ-TVA approach allows tapping into attentional selection specifically.  Second, self-prioritization effects have been replicated across a wide range of stimuli (e.g. faces: Wozniak et al., 2018; names or owned objects: Scheller & Sui, 2022a, or even fully unfamiliar stimuli: Wozniak & Knoblich, 2019) and paradigms (e.g. matching task: Sui et al., 2012; cross-modal cue integration: e.g. Scheller & Sui, 2022b; Scheller et al., 2023; continuous flash suppression: Macrae et al., 2017; temporal order judgment: Constable et al., 2019; Truong et al., 2017). Using neutral geometric shapes, rather than faces and names, addresses a key challenge in self research: mitigating the influence of stimulus familiarity on results. In addition, these newly learned, simple stimuli can be combined with other paradigms, such as the TOJ paradigm in the current study, to investigate the broader impact of self-processing on perception and cognition.

To the best of our knowledge, this is the first study showing evidence about the mechanisms that are involved in early attentional selection of socially salient stimuli. Future replications and extensions would certainly be useful, as with any experimental paradigm.

(3) The comparison between the "social" and "perceptual" tasks remains debatable, as it is challenging to equate the levels of social salience and perceptual salience. In addition, these two tasks differ not only in terms of social decoding processes but also in other aspects such as task difficulty. Whether the observed differences between the tasks can definitively suggest the specificity of social decoding, as the authors claim, needs further confirmation.

Equating the levels of social and perceptual salience is indeed challenging, but not an aim of the present study. Instead, the present study directly compares the mechanisms and effects of social and perceptual salience, specifically experiment 2. By manipulating perceptual salience (relative colour) and social salience (relative shape association) independently and jointly, and quantifying the effects on processing rates, our study allows to directly delineate the contributions of each of these types of salience. The results suggest additive effects (see also Figure 7). Indeed, the possibility remains that these effects are additive because of the use of different perceptual features, so it would be helpful for future studies to explore whether similar perceptual features lead to (supra-/sub-) additive effects. In either case, the study design allows to directly compare the effects and mechanisms of social and perceptual salience.

Regarding the social and perceptual decision dimensions, they were not expected to be equated. Indeed, the social decision dimension requires additional retrieval of the associated identity, making it likely more challenging. This additional retrieval is also likely responsible for the slower responses towards the social association compared to the shape itself. However, the motivation to compare the effects of these two decisional dimensions lies in the assumption that the self needs to be task relevant. Some evidence suggests that the self needs to be task-relevant to induce self-prioritization effects (e.g., Woźniak & Knoblich, 2022). However, these studies typically used matching tasks and were powered to detect large effects only (e.g. f = 0.4, n = 18). As it is likely that lacking contribution of decisional processing levels (which interact with task-relevance) will reduce the SPE, smaller self-prioritization effects that result from earlier processing levels may not be detected with sufficient statistical power. Targeting specific processing levels, especially those with relatively early contributions or small effect sizes, requires larger samples (here: n = 70) to provide sufficient power. Indeed, by contrasting the relative attentional selection effects in the present study we find that the self does not need to be task-relevant to produce self-prioritization effects. This is in line with recent findings of prior entry of self-faces (Jubile & Kumar, 2021)

Reviewer #2 (Recommendations for the authors):

Suggestions:

(1) The research questions should be revised to better align with the conclusions. For example, Q2 is phrased as "Does self-relatedness bias attentional selection at the level of the perceptual feature representation (shape) or at the level of the associated identity (social association)," which is unclear in its reference to "levels." A more appropriate phrasing would be whether the self-association bias occurs automatically or whether it depends on explicit social decoding.

Thank you for this suggestion – we have revised the phrasing accordingly: “Does self-relatedness bias attentional selection automatically or does it require explicit social decoding?”

(2) After presenting the data, it would be helpful to include one or two sentences summarizing the conclusions drawn from the data and how they relate to the research questions. Currently, readers are left to guess whether the results are consistent with the hypotheses.

Thank you for this suggestion, which we think will enhance the clarity of the manuscript – we have added summary sentences when presenting the results:<br /> “This cross-experimental parameter inspection revealed that participants exhibited an attentional selection bias towards socially associated information. Interestingly, enhanced processing speed was observed for other-associated rather than self-associated information, a pattern that diverged from our prediction.”

(1) “Results from experiment 2 demonstrated a faster, more automatic attentional selection for self-associated information when the decision did not require explicit social decoding. When the social identity had to be judged, processing speed for self-associated information decreased. Contrary to the hypothesis that social decoding is necessary for self-prioritization to emerge, these findings suggest that attentional selection can operate automatically to prioritize self-associated information. “

(2) “Taken together, as also confirmed in the cross-experimental analysis, attentional selection favoured the other-related information when social identity had to be judged. In contrast, perceptual salience, as predicted, led to increased processing speed for the more salient stimulus. “

(3) The identity of the "other" used in the experiments is unclear, making it uncertain whether the results are self-specific. It would be beneficial to compare the self condition with a control condition, such as a close friend vs. an unfamiliar other. Alternatively, the results may reflect attentional bias for familiar vs. unfamiliar individuals rather than self-specific bias.

Thank you for this comment. Firstly, we would like to clarify that we have provided participants with a description of who the “other” is (see methods: “At the beginning of this task, participants were told that one of the two geometric shapes that was used in the TOJ task has been assigned to them, and the other shape has been assigned to another participant in the experiment – someone they did not know, but who was of similar age and gender”). We aimed to make the ‘other’ as concrete as possible, while maintaining a ‘stranger’ identity.

Secondly, this specification is in line with the vast majority of the literature, which typically measures the effects of self-prioritization relative to the association with an unfamiliar other (stranger), or an unfamiliar and familiar other (e.g. friend, family member). They find that processing advantages that affect friend-related stimuli (friend-stimuli being processed faster than stranger-associated stimuli) are likely mediated by self-extension, that is, an association of the friend with the self. As such, SPEs, relative to familiar others, are typically smaller in size (see, e.g., Sui et al., 2012). They, however, are less stable and more variable than the self-prioritization effects measured relative to a stranger (see Scheller & Sui, 2022 JEP:HPP). Importantly, this is driven by the variability of the friend-associated stimulus, rather than the self or other-associated stimulus (see Figure 4 in main text and S5 in supplementary material in Scheller & Sui, 2022: https://durham-repository.worktribe.com/output/1210478/the-power-of-the-self-anchoring-information-processing-across-contexts). Effectively, this would suggest that choosing a familiar other as a reference would not only (a) lead to a smaller effect size, but also (b) be a less stable effect, which likely depends on the association the individual has to the other familiar person. In contrast, by associating the other shape with another participant in this experiment, we provide participants not only with a concrete representation of a stranger, but also maximise our ability to detect true effects, as these are likely to be larger and more stable.

(4) The key aspects of the procedure (e.g., the order of different conditions) and its rationale need to be clearly explained before or during the presentation of the results. Currently, readers are left to infer certain details.

Thank you for pointing this out. The methods that provide these details are outlined at the end of the document, however, we agree it would be useful to bring some of these details up. We have therefore revised the methods figure (Figure 3) to include an outline of the task type, order, and trial numbers. Task boxes are colour coded by the conditions that are listed in the results figures of the manuscript. We also added these details to the caption of Figure 3.

“Task structures of Experiments 1 and 2. Both experiments started with a TOJ baseline task. In Experiment 1, only non-salient targets were presented, while in Experiment 2, perceptually salient and non-salient trials were included. These were presented in randomly intermixed order. Next, targets were associated with social identities. Associations were practiced using the matching task. Following association learning, which attaches social salience to the shapes, participants completed the same TOJ task as before. In Experiment 1, they completed one block using a social decision dimension, and one block using a perceptual decision dimension. The order of these blocks was counterbalanced across participants to reduce the influence of order effects in the results. In Experiment 2, perceptually salient and non-salient stimuli were presented in an intermixed fashion, and participants responded within the social decision dimension. Each task block was preceded by 8 (matching) to 14 (TOJ) practice trials.”

(5) Certain imprecise terms used to describe the results, such as "slightly," "roughly," and "loosely," create confusion for the readers. The authors should take a clearer stance on the results and provide an explanation for why the data only "slightly," "roughly," or "loosely" support the findings.

Thank you for highlighting this. We have provided a more concrete wording and details throughout (e.g., “target shapes’ were 30% bigger than the ‘background shapes”).

Lastly, we have updated the formatting of the manuscript to provide higher fidelity figures, which were previously compromised by file conversion.

Author response:

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

eLife Assessment

This provocative manuscript from presents valuable comparisons of the morphologies of Archaean bacterial microfossils to those of microbes transformed under environmental conditions that mimic those present on Earth during the same Eon, although the evidence in support of the conclusions is currently incomplete. The reasons include that taphonomy is not presently considered, and a greater diversity of experimental environmental conditions is not evaluated -- which is important because we ultimately do not know much about Earth's early environments. The authors may want to reframe their conclusions to reflect this work as a first step towards an interpretation of some microfossils as 'proto-cells,' and less so as providing strong support for this hypothesis. 

Regarding the taphonomic alterations: The editor and reviewers are correct in pointing out this issue. Taphonomic alteration of the microfossils attains special significance in the case of microorganisms, as they lack rigid structures and are prone to morphological alterations during or after their fossilization. We are acutely aware of this issue and have conducted long-term experiments (lasting two years) to observe how cells die, decay, and get preserved. A large section of the manuscript (pages 11 to 20) and a substantial portion of the supplementary information is dedicated to understanding the taphonomic alterations. To the best of our knowledge, these are among the longest experiments done to understand the taphonomic alterations of the cells within laboratory conditions. 

Recent reports by Orange et al. (1,2)  showed that under favorable environmental conditions, cells could be fossilized rather rapidly with little morphological modifications. We observed a similar phenomenon in this work. Cells in our study underwent rapid encrustation with cations from the growth media. We have analyzed the morphological changes over a period of 18 months. After 18 months, the softer biofilms got encrusted entirely in salt and turned solid (Fig. ). Despite this transformation, morphologically intact cells could still be observed within these structures. This suggests that the cells inhabiting Archaean coastal marine environments could undergo rather rapid encrustation, and their morphological features could be preserved in the geological record with little taphonomic alteration.    

Regarding the environmental conditions: We are in total agreement with the reviewers that much is unknown about Archaean geology and its environmental conditions. Like the present-day Earth, Archaean Earth certainly had regions that greatly differed in their environmental conditions—volcanic freshwater ponds, brines, mildly halophilic coastal marine environments, and geothermal and hydrothermal vents, to name a few. Our experimental design focuses on one environment we have a relatively good understanding of rather than the rest of the planet, of which we know little. Below, we list our reasons for restricting to coastal marine environments and studying cells under mildly halophilic experimental conditions.  

(1) Very little continental crust from Haden and early Archaean Eon exists on the presentday Earth. Much of our geochemical understanding of this time period was a result of studying the Pilbara Iron Formations and the Barberton Greenstone Belt. Geological investigations suggest that these sites were coastal marine environments. The salinity of coastal marine environments is higher than that of open oceans due to the greater water evaporation within these environments. Moreover, brines were discovered within pillow basalts within the Barberton greenstone belt, suggesting that the salinity within these sites is higher or similar to marine environments. 

(2) We are not certain about the environmental conditions that could have supported the origin of life. However, all currently known Archaean microfossils were reported from coastal marine environments (3.8-2.4Ga). This suggests that proto-life likely flourished in mildly halophilic environments, similar to the experimental conditions employed in our study. 

(3) The chemical analysis of Archaean microfossils also suggests that they lived in saltrich environments, as most, if not all, microfossils are closely associated, often encrusted in a thin layer of salt.  

However, we concur with the reviewers that our interpretations should be reassessed if Archaean microfossils that greatly differ from the currently known microfossils are to be discovered or if new microfossils are to be reported from environments other than coastal marine sites.

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

Microfossils from the Paleoarchean Eon represent the oldest evidence of life, but their nature has been strongly debated among scientists. To resolve this, the authors reconstructed the lifecycles of Archaean organisms by transforming a Gram-positive bacterium into a primitive lipid vesicle-like state and simulating early Earth conditions. They successfully replicated all morphologies and life cycles of Archaean microfossils and studied cell degradation processes over several years, finding that encrustation with minerals like salt preserved these cells as fossilized organic carbon. Their findings suggest that microfossils from 3.8 to 2.5 billion years ago were likely liposome-like protocells with energy conservation pathways but without regulated morphology. 

Strengths: 

The authors have crafted a compelling narrative about the morphological similarities between microfossils from various sites and proliferating wall-deficient bacterial cells, providing detailed comparisons that have never been demonstrated in this detail before. The extensive number of supporting figures is impressive, highlighting numerous similarities. While conclusively proving that these microfossils are proliferating protocells morphologically akin to those studied here is challenging, we applaud this effort as the first detailed comparison between microfossils and morphologically primitive cells. 

Weaknesses: 

Although the species used in this study closely resembles the fossils morphologically, it would be beneficial to provide a clearer explanation for its selection. The literature indicates that many bacteria, if not all, can be rendered cell wall-deficient, making the rationale for choosing this specific species somewhat unclear. While this manuscript includes clear morphological comparisons, we believe the authors do not adequately address the limitations of using modern bacterial species in their study. All contemporary bacteria have undergone extensive evolutionary changes, developing complex and intertwined genetic pathways unlike those of early life forms. Consequently, comparing existing bacteria with fossilized life forms is largely hypothetical, a point that should be more thoroughly emphasized in the discussion. 

Another weak aspect of the study is the absence of any quantitative data. While we understand that obtaining such data for microfossils may be challenging, it would be helpful to present the frequencies of different proliferative events observed in the bacterium used. Additionally, reflecting on the chemical factors in early life that might cause these distinct proliferation modes would provide valuable context. 

Regarding our choice of using modern organisms or this particular bacterial species: 

Based on current scientific knowledge, it is logical to infer that cellular life originated as protocells; nevertheless, there has been no direct geological evidence for the existence of such cells on early Earth. Hence, protocells remain an entirely theoretical concept. Moreover, protocells are considered to have been far more primitive than present-day cells. Surprisingly, this lack of sophistication was the biggest challenge in understanding protocells. Designing experiments in which cells are primitive (but not as primitive as non-living lipid vesicles) and still retain a functional resemblance to a living cell does pose some practical challenges. Laboratory experiments with substitute (proxy) protocells almost always come with some limitations. Although not a perfect proxy, we believe protocells and protoplasts share certain characteristics. Having said that, we would like to reemphasize that protoplasts are not protocells. Our reasons for using protoplasts as model organisms and working with this bacterial species (Exiguobacterium Strain-Molly) are based on several scientific and practical criteria listed below.

(1) Irrespective of cell physiology and intracellular complexity, we believe that protoplasts and protocells share certain similarities in the biophysical properties of their cytoplasm. We explained our reasoning in the manuscript introduction and in our previous manuscripts (Kanaparthi et al., 2024 & Kanaparthi et al., 2023). In short, to be classified as a cell, even a protocell should possess minimal biosynthetic pathways, a physiological mechanism of harvesting free energy from the surrounding (energy-yielding pathways), and a means of replicating its genetic material and transferring it to the daughter cells. These minimal physiological processes could incorporate considerable cytoplasmic complexity. Hence, the biophysical properties of the protocell cytoplasm could have resembled those of the cytoplasm of protoplasts, irrespective of the genomic complexity. 

(2) Irrespective of their physiology, protoplasts exhibit several key similarities to protocells, such as their inherent inability to regulate their morphology or reproduction. This similarity was pointed out in previous studies (3). Despite possessing all the necessary genetic information, protoplasts undergo reproduction through simple physiochemical processes independent of canonical molecular biological processes. This method of reproduction is considered to have been erratic and rather primitive, akin to the theoretical propositions on protocells. Although protoplasts are fully evolved cells with considerable physiological complexity, the above-mentioned biophysical similarities suggest that the protoplast life cycle could morphologically resemble that of protocells (in no other aspect except for their morphology and reproduction).  

(3) Physiologically or genomically different species of Gram-positive protoplasts are shown to exhibit similar morphologies. This suggests that when Gram-positive bacteria lose their cell wall and turn into a protoplast,  they reproduce in a similar manner independent of physiological or genome-based differences. As morphology and only morphology is key to our study, at least from the scope of this study, intracellular complexity is not a key consideration. 

(4) This specific strain was isolated from submerged freshwater springs in the Dead Sea. This isolate and members of this bacterial genus are known to have been well acclimatized to growing in a wide range of salt concentrations and in different salt species. This is important for our study (this and previous manuscript), in which cells must be grown not only at high salt concentrations (1-15%) but in different salts like NaCl, MgCl₂, and KCl. 

(5) Our initial interest in this isolate was due to its ability to reduce iron at high salt concentrations. Given that most spherical microfossils are found in Archaean-banded iron formations covered in pyrite, this suggests that these microfossils could have been reducing oxidized iron species like Fe(III). Nevertheless, over the course of our study, we realized the complexities of live cell staining and imaging under anoxic conditions. Given that the scope of the manuscript is restricted only to comparing the morphologies, not the physiology, we abandoned the idea of growing cells under anoxic conditions.  

Based on these observations, cell physiology may not be a key consideration, at least within the scope of studying microfossil morphology. However, we want to emphasize again that “We do not claim present-day protoplasts are protocells.”  

Regarding the absence of quantitative data:

We are unsure what the reviewer meant by the absence of quantitative data. Is it from the cell size/reproductive pathways perspective or from a microfossil/ecological perspective? At the risk of being portrayed in a bad light, we admit that we did not present quantitative data from either of these perspectives. In our defense, this was not due to our lack of effort but due to the practical limitations imposed by our model organism. 

If the reviewer means the quantitative data regarding cell sizes and morphology: In our previous work, we studied the relationship between protoplast morphology, growth rate, and environmental conditions. In that study, we proposed that the growth rate is one factor that regulates protoplast morphology. Nevertheless, we did not observe uniformity in the sizes of the cells. This lack of uniformity was not just between the replicates but even among the cells grown within the same culture flask or the cells within the same microscopic field. Moreover, cells are often observed to be reproducing either by forming internal or external or by both these processes at the same time. The size and morphological differences among cells within a growth stage could be explained by the physiological and growth rate heterogenicity among cells. 

Bacterial growth curves and their partition into different stages (lag, log & stationary), in general, represent the growth dynamics of an entire bacterial population. Nevertheless, averaging the data obscures the behavior of individual cells (4,5). It is known that genetically identical cells within a single bacterial population could exhibit considerable cell-to-cell variation in gene expression (6,7) and growth rates (8). The reason for such stochastic behavior among monoclonal cells has not been well understood. In the case of normal cells, morphological manifestation of these variations is restricted by a rigid cell wall. Given the absence of a cell wall in protoplasts, we assume such cell-to-cell variations in growth rate is manifested in cell morphology. This makes it challenging to quantitatively determine variations in cell sizes or the size increase in a statically robust manner, even in monoclonal cells. 

Although this lack of uniformity in cell sizes should not be perceived as a limitation, this behavior is consistently observed among microfossils. Spherical microfossils of similar morphology but different sizes were reported from different microfossil sites (9,10). In this regard, both protoplasts and microfossils are very similar. 

If the reviewer means the quantitative data from an ecological perspective: 

Based on the elemental composition and the isotopic signatures of the organic carbon, we can deduce if these structures are of biological origin or not. However, any further interpretation of this data to annotate these microfossils to a particular physiology group is fraught with errors. Hence, we refrain from making any inferences about the physiology and ecological function of these microfossils. This lack of clarity on the physiology of microfossils reduces the chance of quantitative studies on their ecological functions. Moreover, we would like to re-emphasize that the scope of this work is restricted to morphological comparison and is not targeted at understanding the ecological function of these microfossils. This narrow objective also limits the nature of the quantitative data we could present.

Moreover, developing a quantitative understanding of some phenomena could be technically challenging. Many theories on the origin of life, like chemical evolution, started with the qualitative observation that lightning could mediate the synthesis of biologically relevant organic carbon. Our quantitative understanding of this process is still being explored and debated even to this day.     

Reviewer #2 (Public Review): 

Summary: 

In summary, the manuscript describes life-cycle-related morphologies of primitive vesiclelike states (Em-P) produced in the laboratory from the Gram-positive bacterium Exiguobacterium Strain-Molly) under assumed Archean environmental conditions. Em-P morphologies (life cycles) are controlled by the "native environment". In order to mimic Archean environmental conditions, soy broth supplemented with Dead Sea salt was used to cultivate Em-Ps. The manuscript compares Archean microfossils and biofilms from selected photos with those laboratory morphologies. The photos derive from publications on various stratigraphic sections of Paleo- to Neoarchean ages. Based on the similarity of morphologies of microfossils and Em-Ps, the manuscript concludes that all Archean microfossils are in fact not prokaryotes, but merely "sacks of cytoplasm". 

Strengths: 

The approach of the authors to recognize the possibility that "real" cells were not around in the Archean time is appealing. The manuscript reflects the very hard work by the authors composing the Em-Ps used for comparison and selecting the appropriate photo material of fossils. 

Weaknesses: 

While the basic idea is very interesting, the manuscript includes flaws and falls short in presenting supportive data. The manuscript makes too simplistic assumptions on the "Archean paleoenvironment". First, like in our modern world, the environmental conditions during the Archean time were not globally the same. Second, we do not know much about the Archean paleoenvironment due to the immense lack of rock records. More so, the Archean stratigraphic sections from where the fossil material derived record different paleoenvironments: shelf to tidal flat and lacustrine settings, so differences must have been significant. Finally, the Archean spanned 2.500 billion years and it is unlikely that environmental conditions remained the same. Diurnal or seasonal variations are not considered. Sediment types are not considered. Due to these reasons, the laboratory model of an Archean paleoenvironment and the life therein is too simplistic. Another aspect is that eucaryote cells are described from Archean rocks, so it seems unlikely that prokaryotes were not around at the same time. Considering other fossil evidence preserved in Archean rocks except for microfossils, the many early Archean microbialites that show baffling and trapping cannot be explained without the presence of "real cells". With respect to lithology: chert is a rock predominantly composed of silica, not salt. The formation of Em-Ps in the "salty" laboratory set-up seems therefore not a good fit to evaluate chert fossils. Formation of structures in sediment is one step. The second step is their preservation. However, the second aspect of taphonomy is largely excluded in the manuscript, and the role of fossilization (lithification) of Em-Ps is not discussed. This is important because Archean rock successions are known for their tectonic and hydrothermal overprint, as well as recrystallization over time. Some of the comparisons of laboratory morphologies with fossil microfossils and biofilms are incorrect because scales differ by magnitudes. In general, one has to recognize that prokaryote cell morphologies do not offer many variations. It is possible to arrive at the morphologies described in various ways including abiotic ones. 

Regarding the simplistic presumptions on the Archaean Eon environmental conditions, we provided a detailed explanation of this issue in our response to the eLife evaluation. In short, we agree with the reviewer that little is known about the Archaean Eon environmental conditions at a planetary scale. Hence, we restricted our study to one particular environment of which we had a comparatively good understanding. The Archaean Eon spanned 2.5 billion years. However, most of the microfossil sites we discussed in the manuscript are older than 3 billion years, with one exception (2.4 billion years old Turee Creek microfossils). We presume that conditions within this niche (coastal marine) environment could not have changed greatly until 2Ga, after which there have been major changes in the ocean salt composition and salinities.

In the manuscript, we discussed extensively the reasons for restricting our study to these particular environmental conditions. Further explanations of these choices are presented in our response to the eLife evaluation (also see our previous manuscript). In short, the fact that all known microfossils are restricted to coastal marine environments justifies the experimental conditions employed in our study. Nevertheless, we agree with the reviewer that all lab-based studies involve some extent of simplification. This gap/mismatch is even wider when it comes to studies involving origin or early life on Earth.

We are not arguing that prokaryotes are not around at this time. The key message of the manuscript is that they are present, but they have not developed intracellular mechanisms to regulate their morphology and remained primitive in this aspect.  

The sizes of the microfossils and cells from our study were similar in most cases. However, we agree with the reviewer that they deviated considerably in some cases, for example, S70, S73, and S83. These size variations are limited to sedimentary structures like laminations rather than cells. These differences should be expected as we try to replicate the real-life morphologies of biofilms that could have extended over large swats of natural environments in a 2ml volume chamber slide. More specifically, in Fig. S70, there is a considerable size mismatch. But, in Fig. S73, the sizes were comparable between A & C (of course, the size of our reproduction did not match B). In the case of Fig. S83, we do not see a huge size mismatch.      

Reviewer #1 (Recommendations For The Authors): 

We would like to provide several suggestions for changes in text and additions to data analysis. 

39-41: It has been stated that reconstructing the lifecycle is the only way of understanding the nature of these microfossils. First of all, I would rephrase this to 'the most promising way', as there are always multiple approaches to comparing phenomena. 

We agree with the reviewer's suggestion. The suggested changes have been made (line 41). 

125: Please rephrase "under the environmental condition of early Earth" to "under experimental conditions possibly resembling the conditions of the Paleoarchean Eon". Now it sounds like the exact environmental conditions have been produced, which has already been debated in the discussion. 

We agree with the reviewer's suggestion. The suggested changes have been made (line 127). 

125: Please mention the fold change in size, the original size in numbers, and whether this change is statistically significant. 

In the above sections of this document, we explained our reservations about presenting the exact number.

128: Have you found a difference in the relative percentages of modes of reproduction? In other words, is there a difference in percentage between forming internal daughter cells or a string of external daughter cells? 

We explained our reservations about presenting the exact number above. But this has been extensively discussed in our accompaining manuscript. We want to reemphasize that the scope of this manuscript is restricted to comparing morphologies rather than providing a mechanistic explanation of the reproduction process. 

151: A similar model for endocytosis has already been described in proliferating wall-less cells (Kapteijn et al., 2023). In the discussion, please compare your results with the observations made in that paper. 

This is an oversight on our part. The manuscript suggested by the reviewer has now been added (line 154 & 155).  

163: Please use another word for uncanny. We suggest using 'strong resemblance'. 

We changed this according to the reviewers' suggestion (line 168). 

433: Please elaborate on why the results are not shown. This sounds like a statement that should be substantiated further. 

To observe growth and simultaneously image the cells, we conducted these experiments in chamber slides (2ml volume). Over time, we observed cells growing and breaking out of the salt crust (Fig. S86, S87 & Movie 22) and a gradual increase in the turbidity of the media. Although not quantitative, this is a qualitative indication of growth. We did not take precise measurements for several reasons. This sample is precious; it took us almost two years to solidify the biofilm completely, as shown in Fig. S84A. Hence, it was in limited supply, which prevented us from inoculating these salt crusts into large volumes of fresh media. Given a long period of starvation, these cells often exhibited a long lag phase (several days), and there wasn't enough volume to do OD measurements over time. 

We also crushed the solidified biofilm with a sterile spatula before transferring it into the chamber slide with growth media. This resulted in debris in the form of small solid particles, which interfered with our OD measurements. These practical considerations made it challenging to determine the growth precisely. Despite these challenges, we measured an OD of 4 in some chamber slides after two weeks of incubation. Given that these measurements were done haphazardly, we chose not to present this data. 

456: Could you please double-check whether the description is correct for the figure? 8C and 8D are part of Figure 8B, but this is stated otherwise in the description. 

We thank the reviewer for pointing it out. It has now been rectified (line 461-472).

Reviewer #2 (Recommendations For The Authors): 

We thank Reviewer #2  for carefully reading the manuscript and such an elaborate list of questions. The revisions suggested have definitely improved the quality of the manuscript. Here, we would like to address some of the questions that came up repeatedly below. One frequently asked question is regarding the letters denoting the individual figures within the images. For comparison purposes, we often reproduced previously published images. To maintain a consistent figure style, we often have to block the previous denotations with an opaque square and give a new letter. 

The second question that appeared repeatedly below is the missing scale bars in some of the images within a figure. We often did not include a scale bar in the images when this image is an enlarged section of another image within the same figure.     

Title: Please consider being more precise in the title. Microfossils are only one fossil group of "oldest life". Perhaps better: "On the nature of some microfossils in Archean rocks". (see also Line 37).  

Authors’ response: The title conveys a broader message without quantitative insinuations. If our manuscript had been titled "On the nature of all known Archaean microfossils,” we should have agreed with the reviewer's suggestion and changed it to "On the nature of some microfossils in Archean rocks". As it is not, we respectfully decline to make this modification.     

Abstract:  

Line 41: "one way", not "the only way" 

We agree with the reviewer’s comment, and necessary changes have been made (line 41).  

Introduction: 

Line 58f: "oldest sedimentary rock successions", not "oldest known rock formations". There are rocks of much older ages, but those are not well preserved due to metamorphic overprint, or the rocks are igneous to begin with. Minor issue: please note that "formations" are used as stratigraphic units, not so much to describe a rock succession in the field. 

We agree with the reviewer’s comment and have made necessary changes (line 58).

Line 67: Microfossils are widely accepted as evidence of life. Please rephrase. 

We agree with the reviewer’s comment, and necessary changes have been made.

Line 71 - 74: perhaps add a sentence of information here.

We agree with the reviewer’s comment, and necessary changes have been made (line 71).

Line 76: which "chemical and mineralogical considerations"? 

This has been rephrased to “Apart from the chemical and δ¹³C-biomass composition” (line 76).

Line 84ff: This is a somewhat sweeping statement. Please remember that there are microbialites in such rocks that require already a high level of biofilm organization. The existence of cyanobacteria-type microbes in the Archean is also increasingly considered. 

We are aware of literature that labeled the clusters of Archaean microfossils as biofilms and layered structures as microbialites or stromatolite-like structures. However, the use of these terms is increasingly being discouraged. A more recent consensus among researchers suggests annotating these structures simply as sedimentary structures, as microbially induced sedimentary structures (MISS). 

We respectfully disagree with the reviewer’s comment that Archaean microfossils exhibit a high level of biofilm organization. We are not aware of any studies that have conducted such comprehensive research on the architecture of Archaean biofilms. We are not even certain if these clusters of Archaean cells could even be labeled as biofilms in the true sense of the term. We presently lack an exact definition of a biofilm. In our study, we do see sedimentation and bacteria and their encapsulation in cell debris. From a broader perspective, any such aggregation of cells enclosed in cell debris could be annotated as a biofilm. However, more in-depth studies show that biofilm is not a random but a highly organized structure. Different bacterial species have different biofilm architectures and chemical composition. The multispecies biofilms in natural environments are even more complex. We do agree with the reviewer that these structures could broadly be labeled as biofilms, but we presently lack a good, if any, understanding of the Archaean biofilm architecture. 

Regarding the annotation of microfossils as cyanobacteria, we respectfully disagree with the reviewer. This is not a new concept. Many of the Archaean microfossils were annotated as cyanobacteria at the time of their discovery. This annotation is not without controversy. With the advent of genome-based studies, researchers are increasingly moving away from this school of thought.  

Line 101ff: The conditions on early Earth are unknown - there are many varying opinions. Perhaps simply state that this laboratory model simulates an Archean Earth environment of these conditions outlined. 

This is a good idea. We thank the reviewer for this suggestion, and we made appropriate changes. 

Line 112: manuscript to be replaced by "paper"? 

This change has been made (line 114).

Line 116: "spanned years" - how many years? 

We now added the number of years in the brackets (line 118).

Results: 

Line 125: see comment for 101ff. 

we made appropriate changes. 

Figure 1: Caption: Please write out ICV the first time this abbreviation is used. Images: Note that some lettering appears to not fit their white labels underneath. (G, H, I, J0, and M). 

We apologize; this is an oversight on our part. We now spell complete expansion of ICV, the first time we used this abbreviation. 

We took these images from previously published work (references in the figure legend), so we must block out the previous figure captions. This is necessary to maintain a uniform style throughout the manuscript. 

Line 152ff.: here would be a great opportunity to show in a graph the size variations of modern ICVs and to compare the variations with those in the fossil material. 

In the above sections of this document, we explained our reservations about presenting the exact number.

Line 159f.: Fig.1K - what is to see here? Maybe a close-up or - better - a small sketch would help? 

Fig. 1K shows the surface depressions formed during the vesicle formation. The surface characteristics of EM-P and microfossils is very similar.   

Line 161f.: reference?  

The paragraph spanning lines 159 to 172 discusses the morphological similarities between EM-P and SPF microfossils. We rechecked the reference no 35 (Delarue 2019). This is the correct reference. We do not see a mistake if the reviewer meant the reference to the figures.    

Line 164ff.: A question may be asked, how many fossils of the Strelley Pool population would look similar to the "modeled" ones. Questions may rise in which way the environmental conditions control such morphology variations. Perhaps more details? 

This relationship between the environmental conditions and the morphology is discussed extensively in our previous work (11).  

Line 193: what is meant by "similar discontinuous distribution of organic carbon"?

This statement highlights similarities between EM-P and microfossils. The distribution of cytoplasm within the cells is not uniform. There are regions with and devoid of cytoplasm, which is quite unusual for bacteria. Some previous studies argued that this could indicate that these organic structures are of abiotic origin. Here, we show that EMP-like cells could exhibit such a patchy distribution of cytoplasm within the cell.    

Line 218 - 291: The observations are very nice, however, the figures of fossil material in Figures 3 A, B, and C appear not to conform. Perhaps use D, E and I to K. Also, S48 does not show features as described here (see below).  

We did not completely understand the reviewer’s question. As mentioned in the figure legend, both the microfossils and the cells exhibit string with spherical daughter cells within them. Moreover, there are also other similarities like the presence of hollow spherical structures devoid of organic carbon. We also saw several mistakes in the Fig. S48 legend. We have rectified them, and we thank the reviewer for pointing them out.   

Line 293f: Title with "." at end?

This change has been made.

Line 298: predominantly in chert. In clastic material preservation of cells and pores is unlikely due to the common lack of in situ entombment by silica. 

We rephrased this entire paragraph to better convey our message. Either way, we are not arguing that hollow pore spaces exist. As the reviewer mentioned, they will, of course, be filled up with silica. In this entire paragraph, we did not refer to hollow spaces. So, we are not entirely sure what the question was.     

Line 324, 328-349: Please see below comments on the supplementary figures 51-62. Some of the interpretations of morphologies may be incorrect. 

Please find our response to the reviewer’s comments on individual figures below.  

Figure 5 A to D look interesting, however E to J appear to be unconvincing. What is the grey frame in D (not the white insert). 

The grey color is just the background that was added during the 3D rendering process.  

Figure 6 does not appear to be convincing. - Erase? 

We did not understand the reviewer’s reservations regarding this figure. Images A-F within the figure show the gradual transformation of cells into honeycomb-like structures, and images G-J show such structures from the Archaean that are closely associated with microfossils. Moreover, we did not come up with this terminology (honeycomb-like). Previous manuscripts proposed it.  

Line 379ff: S66 and 69, please see my comments below. Microfossils "were often discovered" in layers of organic carbon. 

Please see our response below.   

Line 393-403: Laminae? There are many ways to arrive at C-rich laminae, especially, if the material was compressed during burial. Basically, any type of biofilm would appear as laminae, if compressed. The appearance of thin layers is a mere coincidence. Note that the scale difference in S70, S73, as well as S83, is way too high (cm versus μm!) to allow any such sweeping conclusions. What are α- and β- laminations, the one described by Tice et al.? The arguments are not convincing.

We propose that cells be compressed to form laminae. We answered this question above about the differences in the scale bars. Yes, we are referring to α- and β- laminations described by Tice et al.       

Figure 7: This is an interesting figure, but what are the arguments for B and C, the fossil material, being a membrane? Debris cannot be distinguished with certainty at this scale in the insert of C. B could also be a shriveled-up set of trichomes.  

We agree with the reviewer that debris cannot be definitely differentiated. Traditionally, annotations given to microfossil structures such as biofilm, intact cells, or laminations were all based on morphological similarities with existing structures observed in microorganisms. Given that the structures observed in our study are very similar to the microfossil structures, it is logical to make such inferences. Scales in A & B match perfectly well. The structure in C is much larger, but, as we mentioned in reply to one of the reviewer’s earlier questions, some of the structures from natural environments could not be reproduced at scale in lab experiments. Working in a 2 ml chamber slides does impose some restrictions.   

Figure 8: The figure does not show any honeycomb patterns. The "gaps" in the Moodies laminae are known as lenticular particles in biofilms. They form by desiccated and shriveledup biofilm that mineralizes in situ. Sometimes also entrapped gases induce precipitation. Note also that the modelled material shows a kind of skin around the blobs that are not present in the Moodies material.  

We agree that entrapped gas bubbles could have formed lenticular gaps. In the manuscript, we did not discount this possibility. However, if that is the case, one should explain why we often find clumps of organic carbon within these gaps. As we presented a step-by-step transformation of parallel layers of cells into laminations, which also had similar lenticular gaps, we believe this is a more plausible way such structures could have formed. In the end, there could have been more than one way such structures could have been formed. 

We do see the honeycomb pattern in the hollow gaps. Often, the 3D-rendering of the STED images obscures some details. Hence, in the figure legend, we referred to the supplementary figures also show the sequence of steps involved in the formation of such a pattern.      

Line 405-417: During deposition of clastic sediment any hollow space would be compressed during burial and settling. It is rare that additional pore space (except between the graingrain-contacts) remains visible, especially after consolidation. The exception would be if very early silicification took place filling in any pore space. What about EPS being replaced by mineralic substance? The arguments are not convincing. 

We are suggesting that EPS or cell debris is rapidly encrusted by cations from the surrounding environment and gets solidified into rigid structures. This makes it possible for the structures to be preserved in the fossil record. We believe that hollow structures like the lenticular gaps will be filled up with silica. 

We do not agree with the reviewer’s comment that all biological structures will be compressed. If this is true, there should be no intact microfossils in the Archaean sedimentary structures, which is definitely not the case.      

Line 419-430: Lithification takes place within the sediment and therefore is commonly controlled by the chemistry of pore water and chemical compounds that derive from the dissolution of minerals close by. Another aspect to consider is whether "desiccation cracks" on that small scale may be artefacts related to sample preparation (?).  

We agree that desiccation cracks could have formed during the sample preparation for SEM imaging, as this involves drying the biofilms. However, we observed that the sample we used for SEM is a completely solidified biofilm (Fig. S84), so we expect little change in its morphology during drying. Moreover, visible cracks and pointy edges were also observed in wet samples, as shown in Fig. S87.        

Line 432 - 439: Please see comments on the supplementary material below.

Please find our response to the reviewer’s comments on individual figures below.  

Discussion:  

Line 477f: "all known microfossil morphologies" - is this a correct statement? Also, would the Archean world provide only one kind of "EM-P type"? Morphologies of prokaryote cells (spherical, rod-shaped, filamentous) in general are very simple, and any researcher of Precambrian material will appreciate the difficulties in concluding on taxonomy. There are papers that investigate putative microfossils in chert as features related to life cycles. Microfossil-papers commonly appear not to be controversial give and take some specific cases.  

We made a mistake in using the term “all known microfossil morphologies.” We have now changed it to “all known spherical microfossils” from this statement (line 483). However, we do not agree with the statement that microfossil manuscripts tend not to be controversial. Assigning taxonomy to microfossils is anything but controversial. This has been intensely debated among the scientific community.     

Line 494-496: This statement should be in the Introduction.

We agree with the reviewer’s comment. In an earlier version of the manuscript this statement was in the introduction. To put this statement in its proper context, it needs to be associated with a discussion about the importance of morphology in the identification of microfossils. The present version of the manuscript do not permit moving an entire paragraph into the introduction. Hence, we think making this statement in the discussion section is appropriate. 

Line 484ff. The discussion on biogenicity of microfossils is long-standing (e.g., biogenicity criteria by Buick 1990 and other papers), and nothing new. In paleontology, modern prokaryotes may serve as models but everyone working on Archean microfossils will agree that these cannot correspond to modern groups. An example is fossil "cyanobacteria" that is thought to have been around already in the early Archean. While morphologically very similar to modern cyanobacteria, their genetic information certainly differed - how much will perhaps remain undisclosed by material of that high age.  

Yes, we agree with the reviewer that there has been a longstanding conflict on the topic of biogenicity of microfossils. However, we have never come across manuscripts suggesting that modern microorganisms should only be used as models. If at all, there have been numerous manuscripts suggesting that these microfossils represent cyanobacteria, streptomycetes, and methanotrophs. Regarding the annotation of microfossils as cyanobacteria, we addressed this issue in one of the previous questions raised by the reviewer.    

Line 498ff: Can the variation of morphology and sizes of the EM-Ps be demonstrated statistically? Line 505ff are very speculative statements. Relabeling of what could be vesicles as "microfossils" appears inappropriate. Contrary to what is stated in the manuscript, the morphologies of the Dresser Formation vesicles do not resemble the S3 to S14 spheroids from the Strelley Pool, the Waterfall, and Mt Goldsworthy sites listed in the manuscript. The spindle-shaped vesicles in Wacey et al are not addressed by this manuscript. What roles in mineral and element composition would have played diagenetic alteration and the extreme hydrothermal overprint and weathering typical for Dresser material? S59, S60 do not show what is stated, and the material derives from the Barberton Greenstone Belt, not the Pilbara.

Please see the comments below regarding the supplementary images. 

We did not observe huge variations in the cell morphology. Morphologies, in most cases, were restricted to spherical cells with intracellular vesicles or filamentous extensions. Regarding the sizes of the cells, we see some variations. However, we are reluctant to provide exact numbers. We have presented our reasons above.

We respectfully disagree with the reviewer’s comments. We see quite some similarities between Dresser formation microfossils and our cells. Not just the similarities, we have provided step-by-step transformation of cells that resulted in these morphologies. We fail to see what exactly is the speculation here. The argument that they should be classified as abiotic structures is based on the opinion that cells do form such structures. We clearly show here that they can, and these biological structures resemble Dresser formation microfossils more closely than the abiotic structures. 

Regarding the figures S3-S14. We think they are morphologically very similar. Often, it's not just comparing both images or making exact reproductions (which is not possible). We should focus on reproducing the distinctive morphological features of these microfossils.  

We agree with the reviewer that we did not reproduce all the structures reported by Wacey’s original manuscript, such as spherical structures. We are currently preparing another manuscript to address the filamentous microfossils. These spindle-like structures will be addressed in this subsequent work. 

We agree with the reviewer, we often have difficulties differentiating between cells and vesicles. This is not a problem in the early stages of growth. During the log phase, a significant volume of the cell consists of the cytoplasm, with hollow vesicles constituting only a minor volume (Fig. 1B or S1A). During the later growth stages (Fig. 1E7F or S11), cells were almost hollow, with numerous daughter cells within them. These cells often resemble hollow vesicles rather than cells. However, given these are biologically formed structures, and one could argue that these vesicles are still alive as there is still a minimal amount of cytoplasm (Fig. S27). Hence, we should consider them as cells until they break apart to release daughter cells. 

Regarding Figures S59 and S60, we did not claim either of these microfossils is from Pilbara Iron Formations. The legend of Figure S59 clearly states that these structures are from Buck Reef Chert, originally reported by Tice et al., 2006 (Figure 16 in the original manuscript). The legend of Figure S60 says these structures were originally reported by Barlow et al., 2018, from the Turee Creek Formation. 

Line 546f and 552: The sites including microfossils in the Archean represent different paleoenvironments ranging from marine to terrestrial to lacustrine. References 6 and 66 are well-developed studies focusing on specific stratigraphic successions, but cannot include information covering other Archean worlds of the over 2.5 Ga years Archean time.  

All the Archaean microfossils reported to date are from volcanic coastal marine environments. We are aware that there are rocky terrestrial environments, but no microfossils have been reported from these sites. We are unaware of any Archaean microfossils reported from freshwater environments. 

Line 570ff: The statements may represent a hypothesis, but the data presented are too preliminary to substantiate the assumptions.

We believe this is a correct inference from an evolutionary, genomic, and now from a morphological perspective. 

Figures:  

Please check all text and supplementary figures, whether scale bars are of different styles within the figure (minor quibble). 

S3 (no scale in C, D); S4, S5: Note that scale bars are of different styles. 

We believe we addressed this issue above. 

S6 D: depressions here are well visible - perhaps exchange with a photo in the main text? Note that scale bars are of different styles.  

We agree that depressions are well visible in E. The same image of EM-P cell in E is also present in Fig. 1D in the main text.   

S7: Scale bars should all be of the same style, if anyhow possible. Scale in D? 

We believe we addressed this issue above. 

S9: F appears to be distorted. Is the fossil like this? The figure would need additional indicators (arrows) pointing toward what the reader needs to see - not clear in this version. More explanation in the figure caption could be offered. 

We rechecked the figure from the original publication to check if by mistake the figure was distorted during the assembly of this image. We can assure you that this is not the case. We are not sure what further could be said in the figure legend.     

S13: What is shown in the inserts of D and E that is also visible in A and B? Here a sketch of the steps would help. 

We did not understand the question.  

S14: Scale in A, B? 

We believe we addressed this issue above. 

S15: Scales in A, E, C, D 

We believe we addressed this issue above. 

S16: scales in D, E, G, H, I, J?  

We believe we addressed this issue above. 

S17: "I" appears squeezed, is that so? If morphology is an important message, perhaps reduce the entire figure so it fits the layout. Note that labels A, B, C, and D are displaced. 

As shown in several subsequent figures, the hollow spherical vesicles are compressed first into honeycomb-like structures, and they often undergo further compression to form lamination-like structures. Such images often give the impression that the entire figure is squashed, but this is not the case. If one examines the figure closely, you could see perfectly spherical vesicles together with laterally sqeezed structures. Regarding the figure labels, we addressed this issue above. 

S18: The filamentous feature in C could also be the grain boundaries of the crystals. Can this be excluded as an interpretation? Are there microfossils with the cell membranes? That would be an excellent contribution to this figure. Note that scale bars are of different styles.

If this is a one-off observation, we could have arrived at the reviewer's opinion. But spherical cells in a “string of beads” configuration were frequently reported from several sites, to be discounted as mere interpretation.    

S19: The morphologies in A - insert appear to be similar to E - insert in the lower left corner. The chain of cells in A may look similar to the morphologies in E - insert upper right of the image. B - what is to see here? D - the inclusions do not appear spherical (?). Does C look similar to the cluster with the arrow in the lower part of image E? Note that scale bars are of different styles (minor quibble). A, B, C, and D appear compressed. Perhaps reduce the size of the overall image?  

The structures highlighted (yellow box) in C are similar to the highlighted regions in E—the agglomeration of hollow vesicles. It is hard to get understand this similarity in one figure. The similarities are apparent when one sees the Movie 4 and Fig. S12, clearly showing the spherical daughter cells within the hollow vesicle. We now added the movie reference to the figure legend.    

S20: A appears not to contribute much. The lineations in B appear to be diagenetic. However, C is suitable. Perhaps use only C, D, E? 

We believe too many unrecognizable structures are being labeled as diagenetic. Nevertheless, we do not subscribe to the notion that these are too lenient interpretations. These interpretations are justified as such structures have not been reported from live cells. This is the first study to report that cells could form such structures. As we now reproduced these structures, an alternate interpretation that these are organic structures derived from microfossils should be entertained. 

S 21: Note that scale bars are of different styles.  

We believe we addressed this issue above. 

S22: Perhaps add an arrow in F, where the cell opened, and add "see arrow" in the caption? Is this the same situation as shown in C (white arrow)? What is shown by the white arrow in A? Note that scale bars are of different styles.

We did the necessary changes.  

S23: In the caption and main text, please replace "&" with "and" (please check also the other figure captions, e.g. S24). Note that scale bars are of different styles. What is shown in F? A, D - what is shown here?

We replaced “&” with “and.”  

S24: Note that scale bars are of different styles. Note that Wacey et al. describe the vesicles as abiotic not as "microfossils"; please correct in figure caption [same also S26; 25; 28].

We are aware of Prof. Dr. Wacey’s interpretations. We discuss it at length in the discussion section our manuscript. Based on the similarities between the Dresser formation structures and structures formed by EM-P, we contest that these are abiotic structures.  

S25: Appears compressed; note different scale bars. 

We believe we addressed this issue above. 

S28: The label in B is still in the upper right corner; scale in D? What is to see in rectangles (blue and red) in A, B? In fossil material, this could be anything. 

These figures are taken from a previous manuscript cited in the figure legend. We could not erase or modify these figures.  

S33: "L"ewis; G appears a bit too diffuse - erase? Note that scale bars are of different styles.

We believe we addressed this issue above. 

S34: This figure appears unconvincing. Erase? 

There are considerable similarities between the microfossils and structures formed by EM-P. If the reviewer expands a bit on what he finds unconvincing, we can address his reservations.    

S35: It would be more convincing to show only the morphological similarities between the cell clusters. B and C are too blurry to distinguish much. Scales in D to F and in sketches? A appears compressed (?). 

We rechecked the original manuscript to see if image A was distorted while making this figure, but this is not the case. Regarding B & C, cells in this image are faint as they are hollow vesicles and, by nature, do not generate too much contrast when imaged with a phase-contrast microscope. There are some limitations on how much we can improve the contrast. We now added scale bars for D-I. Similarly, faint hollow vesicles can be seen in Fig. S21 C & D, and Fig. 3H.  

S36: Very nice; in B no purple arrow is visible. Note that scale bars are of different styles. S37 and S36 are very much the same - fuse, perhaps?  

We are sorry for the confusion. There are purple arrows in Fig. S37B-D. 

S38: this is a more unconvincing figure - erase? 

Unconvincing in wahy sense. There are considerable similarities between the microfossils and structures formed by EM-P. If the reviewer expands a bit on what he finds unconvincing, we can address his reservations.

S39: white rectangle in A? Arrow in A? Note that scale bars are of different styles.

These are some of the unavoidable remnants from the image from the original publication. 

S40: in F: CM, V = ?; Note that scale bars are of different style. 

It’s an oversite on our part. We now added the definitions to the figure legaend. We thank the reviewer for pointing it out.  

S41: Rectangles in D, E, F, G can be deleted? Scales and labels missing in photos lower right. 

Those rectangles are added by the image processing software to the 3Drendered images. Regarding the missing scale bars in H & I they are the magnified regions of F. The scale bar is already present in F.   

S42: appears compressed. G could be trimmed. Labels too small; scale in G? 

This is a curled-up folded membrane. We needed to lower the resolution of some images to restrict the size of the supplement to journal size restrictions. It is not possible to present 85 figures in high resolution. But we assure you that the image is not laterally compressed in any manner.   

S43: This figure appears to be unconvincing. Reducing to pairing B, C, D with L, K? Spherical inclusions in B? Scales in E to G? Similar in S44: A, B, E only? Note that scale bars are of different styles. 

Figures I to K are important. They show not just the morphological similarities but also the sequence of steps through which such structures are formed. We addressed the issue of the scale bars above.  

S45: A, B, and C appear to show live or subrecent material. How was this isolated of a rock? Note that scale bars are of different styles.  

It is common to treat rocks with acids to dissolve them and then retrieve organic structures within them. This technique is becoming increasingly common. The procedure is quite extensively discussed in the original manuscript. We don’t see much differences in the scale bars of microfossils and EM-P cells, they are quite similar. 

S46: A: what is to see here? Note that scale bars are of different styles. 

There are considerable similarities between the folded fabric like organic structures with spherical inclusions and structures formed by EM-P. If the reviewer expands a bit on what he finds unconvincing, we can address his reservations.    

S47: Perhaps enlarge B and erase A. Note that scale bars are of different styles. 

S48: Image B appears to show the fossil material - is the figure caption inconsistent? There are no aggregations visible in the boxes in A. H is described in the figure caption but missing in the figure. Overall, F and G do not appear to mirror anything in A to E (which may be fossil material?). 

S51; S52 B, C, E; S53: these figures appear unconvincing - erase? 

Unconvincing in what sense? The structures from our study are very similar to the microfossils.   

S54: North "Pole; scale bars in A to C =? 

These figures were borrowed from an earlier publication referenced in the figure legend. That is the reason for the differences in the styles of scale bars.  

S55: D and E appear not to contribute anything. Perhaps add arrow(s) and more explanation? Check the spelling in the caption, please. 

D & E show morphological similarities between cells from our study and microfossils (A).   

S56: Hexagonal morphologies may also be a consequence of diagenesis. Overall, perhaps erase this figure?  

I certainly agree that could be one of the reasons for the hexagonal morphologies. Such geometric polygonal morphologies have not been observed in living organisms. Nevertheless, as you can see from the figure, such morphologies could also be formed by living organisms. Hence, this alternate interpretation should not be discounted.   

S57: The figure caption needs improvement. Please add more description. What show arrows in A, what are the numbers in A? What is the relation between the image attached to the right side of A? Is this a close-up? Note that scale bars are of different styles. 

We expanded a bit on our original description of the figure. However, we request the reviewer to keep in mind that the parts of the figure are taken from previous publication. We are not at liberty to modifiy them, like removing the arrows. This imposes some constrains. 

S58: There are no honeycomb-shaped features visible. What is to see here? Erase this figure? 

Clearly, one can see spherical and polygonal shapes within the Archaean organic structures and mat-like structures formed by EM-P.  

S59 and S60: What is to see here? - Erase? 

Clearly, one can see spherical and polygonal shapes within the Archaean organic structures and mat-like structures formed by EM-P in Fig. S59. Further disintegration of these honeycomb shaped mats into filamentous struructures with spherical cells attached to them can be seen in both Archaean organic structures and structures formed by EM-P.   

S61: This figure appears to be unconvincing. B and F may be a good pairing. Note that scale bars are of different styles.  

There are considerable similarities between the microfossils and structures formed by EM-P. If the reviewer expands a bit on what he finds unconvincing, we might be able to address his reservations.     

S62: This figure appears to be unconvincing - erase?

There are considerable similarities between the microfossils and structures formed by EM-P. If the reviewer expands a bit on what he finds unconvincing, we might be able to address his reservations.     

S66: This figure is unconvincing - erase? 

There are considerable similarities between the microfossils and structures formed by EM-P. If the reviewer expands a bit on what he finds unconvincing, we might be able to address his reservations.    

S68: Scale in B, D, and E? 

Image B is just a magnified image of a small portion of image A. Hence, there is no need for an additional scale bar. The same is true for images D and E. 

S69: This figure appears to be unconvincing, at least the fossil part. Filamentous features are visible in fossil material as well, but nothing else. 

We are not sure what filamentous features the reviewer is referring to. Both the figures show morphologically similar spherical cells covered in membrane debris.    

S70 [as well as S82]: Good thinking here, but scales differ by magnitudes (cm to μm). Erase this figure? Very similar to Figure S73: Insert in C has which scale in comparison to B? Note that scale bars are of different styles.  

We realize the scale bars are of different sizes. In our defense, our experiments are conducted in 1ml volume chamber slides. We don’t have the luxury of doing these experiments on a scale similar to the natural environments. The size differences are to be expected. 

S71: Scale in E? 

Image E is just a magnified image of a small portion of image D. Hence, we believe a scale bar is unnecessary. 

S72: Scale in insert?  

The insert is just a magnified region of A & C

S75: This figure appears to be unconvincing. This is clastic sediment, not chert. Lenticular gaps would collapse during burial by subsequent sediment. - Erase? 

Regarding the similarities, we see similar lenticular gaps within the parallel layers of organic carbon in both microfossils, and structures formed by EM-P.

S76: A, C, D do not look similar to B - erase? Similar to S79, also with respect to the differences in scale. Erase? 

Regarding the similarities, we see similar lenticular gaps within the parallel layers of organic carbon in both microfossils, and structures formed by EM-P. We believe we addressed the issue of scale bars above. 

S80: A appears to be diagenetic, not primary. Erase? 

These two structures share too many resemblances to ignore or discount just as diagenic structures - Raised filamentous structures originate out of parallel layers of organic carbon (laminations), with spherical cells within this filamentous organic carbon.  

S85: What role would diagenesis play here? This figure appears unconvincing. Erase?

We do believe that diagenesis plays a major role in microfossil preservation. However, we also do not suscribe to the notion that we should by default assign diagenesis to all microfossil features. Our study shows that there could be an alternate explanation to some of the observations.  

S86 and S87: These appear unconvincing. What is to see here? Erase? 

The morphological similarities between these two structures. Stellarshaped organic structures with strings of spherical daughter cells growing out of them.  

S88: Does this image suggest the preservation of "salt" in organic material once preserved in chert?  

That is one inference we conclude from this observation. Crystaline NaCl was previously reported from within the microfossil cells.    

S89: What is to see here? Spherical phenomena in different materials? 

At present, the presence of honeycomb-like structures is often considered to have been an indication of volcanic pumice. We meant to show that biofilms of living organisms could result in honeycomb-shaped patterns similar to volcanic pumice.

References 

Please check the spelling in the references. 

We found a few references that required corrention. We now rectified them. 

References  

(1) Orange F, Westall F, Disnar JR, Prieur D, Bienvenu N, Le Romancer M, et al. Experimental silicification of the extremophilic archaea pyrococcus abyssi and methanocaldococcus jannaschii: Applications in the search for evidence of life in early earth and extraterrestrial rocks. Geobiology. 2009;7(4). 

(2) Orange F, Disnar JR, Westall F, Prieur D, Baillif P. Metal cation binding by the hyperthermophilic microorganism, Archaea Methanocaldococcus Jannaschii, and its effects on silicification. Palaeontology. 2011;54(5). 

(3) Errington J. L-form bacteria, cell walls and the origins of life. Open Biol. 2013;3(1):120143. 

(4) Cooper S. Distinguishing between linear and exponential cell growth during the division cycle: Single-cell studies, cell-culture studies, and the object of cell-cycle research. Theor Biol Med Model. 2006; 

(5) Mitchison JM. Single cell studies of the cell cycle and some models. Theor Biol Med Model. 2005; 

(6) Kærn M, Elston TC, Blake WJ, Collins JJ. Stochasticity in gene expression: From theories to phenotypes. Nat Rev Genet. 2005; 

(7) Elowitz MB, Levine AJ, Siggia ED, Swain PS. Stochastic gene expression in a single cell. Science. 2002; 

(8) Strovas TJ, Sauter LM, Guo X, Lidstrom ME. Cell-to-cell heterogeneity in growth rate and gene expression in Methylobacterium extorquens AM1. J Bacteriol. 2007; 

(9) Knoll AH, Barghoorn ES. Archean microfossils showing cell division from the Swaziland System of South Africa. Science. 1977;198(4315):396–8. 

(10) Sugitani K, Grey K, Allwood A, Nagaoka T, Mimura K, Minami M, et al. Diverse microstructures from Archaean chert from the Mount Goldsworthy–Mount Grant area, Pilbara Craton, Western Australia: microfossils, dubiofossils, or pseudofossils? Precambrian Res. 2007;158(3–4):228–62. 

(11) Kanaparthi D, Lampe M, Krohn JH, Zhu B, Hildebrand F, Boesen T, et al. The reproduction process of Gram-positive protocells. Sci Rep. 2024 Mar 25;14(1):7075.

Author response:

Reviewer #1 (Public review):

This manuscript presents an interesting exploration of the potential activation mechanisms of DLK following axonal injury. While the experiments are beautifully conducted and the data are solid, I feel that there is insufficient evidence to fully support the conclusions made by the authors.

In this manuscript, the authors exclusively use the puc-lacZ reporter to determine the activation of DLK. This reporter has been shown to be induced when DLK is activated. However, there is insufficient evidence to confirm that the absence of reporter activation necessarily indicates that DLK is inactive. As with many MAP kinase pathways, the DLK pathway can be locally or globally activated in neurons, and the level of DLK activation may depend on the strength of the stimulation. This reporter might only reflect strong DLK activation and may not be turned on if DLK is weakly activated. The results presented in this manuscript support this interpretation. Strong stimulation, such as axotomy of all synaptic branches, caused robust DLK activation, as indicated by puc-lacZ expression. In contrast, weak stimulation, such as axotomy of some synaptic branches, resulted in weaker DLK activation, which did not induce the puc-lacZ reporter. This suggests that the strength of DLK activation depends on the severity of the injury rather than the presence of intact synapses. Given that this is a central conclusion of the study, it may be worthwhile to confirm this further. Alternatively, the authors may consider refining their conclusion to better align with the evidence presented.

We wish to further clarify a striking aspect of puc-lacZ induction following injury: it is bimodal. It is either induced (in various injuries that remove all synaptic boutons), or not induced, including in injuries that spared only 1-2 remaining boutons. This was particularly evident for injuries that spared the NMJ on muscle 29, which is comprised of only a few boutons. In some instances, only a single bouton was evident on muscle 29. While our injuries varied enormously in the number of branches and boutons that were lost, we did not see a comparable variability in puc-lacZ induction.  In the revision we will include additional images to better demonstrate this observation.

The reviewer (and others) fairly point out that our current study focuses on puc-lacZ as a reporter of Wnd signaling in the cell body. We consider this to be a downstream integration of events in axons that are more challenging to detect. It is striking that this integration appears strongly sensitized to the presence of spared synaptic boutons. Examination of Wnd’s activation in axons and synapses is a goal for our future work.

As noted by the authors, DLK has been implicated in both axon regeneration and degeneration. Following axotomy, DLK activation can lead to the degeneration of distal axons, where synapses are located. This raises an important question: how is DLK activated in distal axons? The authors might consider discussing the significance of this "synapse connection-dependent" DLK activation in the broader context of DLK function and activation mechanisms.

While it has been noted that inhibition of DLK can mildly delay Wallerian degeneration (Miller et al., 2009), this does not appear to be the case for retinal ganglion cell axons following optic nerve crush (Fernandes et al., 2014). It is also not the case for Drosophila motoneurons and NMJ terminals following peripheral nerve injury (Xiong et al., 2012; Xiong and Collins, 2012). Instead, overexpression of Wnd or activation of Wnd by a conditioning injury leads to an opposite phenotype - an increase in resiliency to Wallerian degeneration for axons that have been previously injured (Xiong et al., 2012; Xiong and Collins, 2012). The downstream outcome of Wnd activation is highly dependent on the context; it may be an integration of the outcomes of local Wnd/DLK activation in axons with downstream consequences of nuclear/cell body signaling.  The current study suggests some rules for the cell body signaling, however, how Wnd is regulated at synapses and why it promotes degeneration in some circumstances but not others are important future questions.

For the reviewer’s suggestion, it is interesting to consider DLK’s potential contributions to the loss of NMJ synapses in a mouse model of ALS (Le Pichon et al., 2017; Wlaschin et al., 2023). Our findings suggest that the synaptic terminal is an important locus of DLK regulation, while dysfunction of NMJ terminals is an important feature of the ‘dying back’ hypothesis of disease etiology (Dadon-Nachum et al., 2011; Verma et al., 2022). We propose that the regulation of DLK at synaptic terminals is an important area for future study, and may reveal how DLK might be modulated to curtail disease progression. Of note, DLK inhibitors are in clinical trials (Katz et al., 2022; Le et al., 2023; Siu et al., 2018), but at least some have been paused due to safety concerns (Katz et al., 2022). Further understanding of the mechanisms that regulate DLK are needed to understand whether and how DLK and its downstream signaling can be tuned for therapeutic benefit.

Reviewer #2 (Public review):

Summary:

The authors study a panel of sparsely labeled neuronal lines in Drosophila that each form multiple synapses. Critically, each axonal branch can be injured without affecting the others, allowing the authors to differentiate between injuries that affect all axonal branches versus those that do not, creating spared branches. Axonal injuries are known to cause Wnd (mammalian DLK)-dependent retrograde signals to the cell body, culminating in a transcriptional response. This work identifies a fascinating new phenomenon that this injury response is not all-or-none. If even a single branch remains uninjured, the injury signal is not activated in the cell body. The authors rule out that this could be due to changes in the abundance of Wnd (perhaps if incrementally activated at each injured branch) by Wnd, Hiw's known negative regulator. Thus there is both a yet-undiscovered mechanism to regulate Wnd signaling, and more broadly a mechanism by which the neuron can integrate the degree of injury it has sustained. It will now be important to tease apart the mechanism(s) of this fascinating phenomenon. But even absent a clear mechanism, this is a new biology that will inform the interpretation of injury signaling studies across species.

Strengths:

(1) A conceptually beautiful series of experiments that reveal a fascinating new phenomenon is described, with clear implications (as the authors discuss in their Discussion) for injury signaling in mammals.

(2) Suggests a new mode of Wnd regulation, independent of Hiw.

Weaknesses:

(1) The use of a somatic transcriptional reporter for Wnd activity is powerful, however, the reporter indicates whether the transcriptional response was activated, not whether the injury signal was received. It remains possible that Wnd is still activated in the case of a spared branch, but that this activation is either local within the axons (impossible to determine in the absence of a local reporter) or that the retrograde signal was indeed generated but it was somehow insufficient to activate transcription when it entered the cell body. This is more of a mechanistic detail and should not detract from the overall importance of the study

We agree. The puc-lacZ reporter tells us about signaling in the cell body, but whether and how Wnd is regulated in axons and synaptic branches, which we think occurs upstream of the cell body response, remains to be addressed in future studies.

(2) That the protective effect of a spared branch is independent of Hiw, the known negative regulator of Wnd, is fascinating. But this leaves open a key question: what is the signal?

This is indeed an important future question, and would still be a question even if Hiw were part of the protective mechanism by the spared synaptic branch. Our current hypothesis (outlined in Figure 4) is that regulation of Wnd is tied to the retrograde trafficking of a signaling organelle in axons. The Hiw-independent regulation complements other observations in the literature that multiple pathways regulate Wnd/DLK (Collins et al., 2006; Feoktistov and Herman, 2016; Klinedinst et al., 2013; Li et al., 2017; Russo and DiAntonio, 2019; Valakh et al., 2013). It is logical for this critical stress response pathway to have multiple modes of regulation that may act in parallel to tune and restrain its activation.

Reviewer #3 (Public review):

Summary:

This manuscript seeks to understand how nerve injury-induced signaling to the nucleus is influenced, and it establishes a new location where these principles can be studied. By identifying and mapping specific bifurcated neuronal innervations in the Drosophila larvae, and using laser axotomy to localize the injury, the authors find that sparing a branch of a complex muscular innervation is enough to impair Wallenda-puc (analogous to DLK-JNK-cJun) signaling that is known to promote regeneration. It is only when all connections to the target are disconnected that cJun-transcriptional activation occurs.

Overall, this is a thorough and well-performed investigation of the mechanism of spared-branch influence on axon injury signaling. The findings on control of wnd are important because this is a very widely used injury signaling pathway across species and injury models. The authors present detailed and carefully executed experiments to support their conclusions. Their effort to identify the control mechanism is admirable and will be of aid to the field as they continue to try to understand how to promote better regeneration of axons.

Strengths:

The paper does a very comprehensive job of investigating this phenomenon at multiple locations and through both pinpoint laser injury as well as larger crush models. They identify a non-hiw based restraint mechanism of the wnd-puc signaling axis that presumably originates from the spared terminal. They also present a large list of tests they performed to identify the actual restraint mechanism from the spared branch, which has ruled out many of the most likely explanations. This is an extremely important set of information to report, to guide future investigators in this and other model organisms on mechanisms by which regeneration signaling is controlled (or not).

Weaknesses:

The weakest data presented by this manuscript is the study of the actual amounts of Wallenda protein in the axon. The authors argue that increased Wnd protein is being anterogradely delivered from the soma, but no support for this is given. Whether this change is due to transcription/translation, protein stability, transport, or other means is not investigated in this work. However, because this point is not central to the arguments in the paper, it is only a minor critique.

We agree and are glad that the reviewer considers this a minor critique; this is an area for future study. In Supplemental Figure 1 we present differences in the levels of an ectopically expressed GFP-Wnd-kinase-dead transgene, which is strikingly increased in axons that have received a full but not partial axotomy. We suspect this accumulation occurs downstream of the cell body response because of the timing. We observed the accumulations after 24 hours (Figure S1F) but not at early (1-4 hour) time points following axotomy (data not shown). Further study of the local regulation of Wnd protein and its kinase activity in axons is an important future direction.

As far as the scope of impact: because the conclusions of the paper are focused on a single (albeit well-validated) reporter in different types of motor neurons, it is hard to determine whether the mechanism of spared branch inhibition of regeneration requires wnd-puc (DLK/cJun) signaling in all contexts (for example, sensory axons or interneurons). Is the nerve-muscle connection the rule or the exception in terms of regeneration program activation?

DLK signaling is strongly activated in DRG sensory neurons following peripheral nerve injury (Shin et al., 2012), despite the fact that sensory neurons have bifurcated axons and their projections in the dorsal spinal cord are not directly damaged by injuries to the peripheral nerve. Therefore it is unlikely that protection by a spared synapse is a universal rule for all neuron types. However the molecular mechanisms that underlie this regulation may indeed be shared across different types of neurons but utilized in different ways. For instance, nerve growth factor withdrawal can lead to activation of DLK (Ghosh et al., 2011), however neurotrophins and their receptors are regulated and implemented differently in different cell types. We suspect that the restraint of Wnd signaling by the spared synaptic branch shares a common underlying mechanism with the restraint of DLK signaling by neurotrophin signaling. Further elucidation of the molecular mechanism is an important next step towards addressing this question.

Because changes in puc-lacZ intensity are the major readout, it would be helpful to better explain the significance of the amount of puc-lacZ in the nucleus with respect to the activation of regeneration. Is it known that scaling up the amount of puc-lacZ transcription scales functional responses (regeneration or others)? The alternative would be that only a small amount of puc-lacZ is sufficient to efficiently induce relevant pathways (threshold response).

While induction of puc-lacZ expression correlates with Wnd-mediated phenotypes, including sprouting of injured axons (Xiong et al., 2010), protection from Wallerian degeneration (Xiong et al., 2012; Xiong and Collins, 2012) and synaptic overgrowth (Collins et al., 2006), we have not observed any correlation between the degree of puc-lacZ induction (eg modest, medium or high) and the phenotypic outcomes (sprouting, overgrowth, etc). Rather, there appears to be a striking all-or-none difference in whether puc-lacZ is induced or not induced. There may indeed be a threshold that can be restrained through multiple mechanisms. We posit in figure 4 that restraint may take place in the cell body, where it can be influenced by the spared bifurcation.

References Cited:

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Fernandes KA, Harder JM, John SW, Shrager P, Libby RT. 2014. DLK-dependent signaling is important for somal but not axonal degeneration of retinal ganglion cells following axonal injury. Neurobiol Dis 69:108–116.

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Huntwork-Rodriguez S, Wang B, Watkins T, Ghosh AS, Pozniak CD, Bustos D, Newton K, Kirkpatrick DS, Lewcock JW. 2013. JNK-mediated phosphorylation of DLK suppresses its ubiquitination to promote neuronal apoptosis. J Cell Biol 202:747–763.

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Klinedinst S, Wang X, Xiong X, Haenfler JM, Collins CA. 2013. Independent pathways downstream of the Wnd/DLK MAPKKK regulate synaptic structure, axonal transport, and injury signaling. J Neurosci 33:12764–12778.

Le K, Soth MJ, Cross JB, Liu G, Ray WJ, Ma J, Goodwani SG, Acton PJ, Buggia-Prevot V, Akkermans O, Barker J, Conner ML, Jiang Y, Liu Z, McEwan P, Warner-Schmidt J, Xu A, Zebisch M, Heijnen CJ, Abrahams B, Jones P. 2023. Discovery of IACS-52825, a potent and selective DLK inhibitor for treatment of chemotherapy-induced peripheral neuropathy. J Med Chem 66:9954–9971.

Le Pichon CE, Meilandt WJ, Dominguez S, Solanoy H, Lin H, Ngu H, Gogineni A, Sengupta Ghosh A, Jiang Z, Lee S-H, Maloney J, Gandham VD, Pozniak CD, Wang B, Lee S, Siu M, Patel S, Modrusan Z, Liu X, Rudhard Y, Baca M, Gustafson A, Kaminker J, Carano RAD, Huang EJ, Foreman O, Weimer R, Scearce-Levie K, Lewcock JW. 2017. Loss of dual leucine zipper kinase signaling is protective in animal models of neurodegenerative disease. Sci Transl Med 9. doi:10.1126/scitranslmed.aag0394

Li J, Zhang YV, Asghari Adib E, Stanchev DT, Xiong X, Klinedinst S, Soppina P, Jahn TR, Hume RI, Rasse TM, Collins CA. 2017. Restraint of presynaptic protein levels by Wnd/DLK signaling mediates synaptic defects associated with the kinesin-3 motor Unc-104. Elife 6. doi:10.7554/eLife.24271

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Nihalani D, Merritt S, Holzman LB. 2000. Identification of structural and functional domains in mixed lineage kinase dual leucine zipper-bearing kinase required for complex formation and stress-activated protein kinase activation. J Biol Chem 275:7273–7279.

Russo A, DiAntonio A. 2019. Wnd/DLK is a critical target of FMRP responsible for neurodevelopmental and behavior defects in the Drosophila model of fragile X syndrome. Cell Rep 28:2581–2593.e5.

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Siu M, Sengupta Ghosh A, Lewcock JW. 2018. Dual Leucine Zipper Kinase Inhibitors for the Treatment of Neurodegeneration. J Med Chem 61:8078–8087.

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Reviewer #1 (Public review):

Summary:

Zhang et al. addressed the question of whether advantageous and disadvantageous inequality aversion can be vicariously learned and generalized. Using an adapted version of the ultimatum game (UG), in three phases, participants first gave their own preference (baseline phase), then interacted with a "teacher" to learn their preference (learning phase), and finally were tested again on their own (transfer phase). The key measure is whether participants exhibited similar choice preferences (i.e., rejection rate and fairness rating) influenced by the learning phase, by contrasting their transfer phase and baseline phase. Through a series of statistical modeling and computational modeling, the authors reported that both advantageous and disadvantageous inequality aversion can indeed be learned (Study 1), and even be generalised (Study 2).

Strengths:

This study is very interesting, it directly adapted the lab's previous work on the observational learning effect on disadvantageous inequality aversion, to test both advantageous and disadvantageous inequality aversion in the current study. Social transmission of action, emotion, and attitude have started to be looked at recently, hence this research is timely. The use of computational modeling is mostly appropriate and motivated. Study 2, which examined the vicarious inequality aversion in conditions where feedback was never provided, is interesting and important to strengthen the reported effects. Both studies have proper justifications to determine the sample size.

Weaknesses:

Despite the strengths, a few conceptual aspects and analytical decisions have to be explained, justified, or clarified.

INTRODUCTION/CONCEPTUALIZATION<br /> (1) Two terms seem to be interchangeable, which should not, in this work: vicarious/observational learning vs preference learning. For vicarious learning, individuals observe others' actions (and optionally also the corresponding consequence resulting directly from their own actions), whereas, for preference learning, individuals predict, or act on behalf of, the others' actions, and then receive feedback if that prediction is correct or not. For the current work, it seems that the experiment is more about preference learning and prediction, and less so about vicarious learning. The intro and set are heavily around vicarious learning, and later the use of vicarious learning and preference learning is rather mixed in the text. I think either tone down the focus on vicarious learning, or discuss how they are different. Some of the references here may be helpful: Charpentier et al., Neuron, 2020; Olsson et al., Nature Reviews Neuroscience, 2020; Zhang & Glascher, Science Advances, 2020

EXPERIMENTAL DESIGN<br /> (2) For each offer type, the experiment "added a uniformly distributed noise in the range of (-10 ,10)". I wonder what this looks like? With only integers such as 25:75, or even with decimal points? More importantly, is it possible to have either 70:30 or 90:10 option, after adding the noise, to have generated an 80:20 split shown to the participants? If so, for the analyses later, when participants saw the 80:20 split, which condition did this trial belong to? 70:30 or 90:10? And is such noise added only to the learning phase, or also to the baseline/transfer phases? This requires some clarification.

(3) For the offer conditions (90:10, 70:30, 50:50, 30:70, 10:90) - are they randomized? If so, how is it done? Is it randomized within each participant, and/or also across participants (such that each participant experienced different trial sequences)? This is important, as the order especially for the learning phase can largely impact the preference learning of the participants.

STATISTICAL ANALYSIS & COMPUTATIONAL MODELING<br /> (4) In Study 1 DI offer types (90:10, 70:30), the rejection rate for DI-AI averse looks consistently higher than that for DI averse (ie, the blue line is above the yellow line). Is this significant? If so, how come? Since this is a between-subject design, I would not anticipate such a result (especially for the baseline). Also, for the LME results (eg, Table S3), only interactions were reported but not the main results.

(5) I do not particularly find this analysis appealing: "we examined whether participants' changes in rejection rates between Transfer and Baseline, could be explained by the degree to which they vicariously learned, defined as the change in punishment rates between the first and last 5 trials of the Learning phase." Naturally, the participants' behavior in the first 5 trials in the learning phase will be similar to those in the baseline; and their behavior in the last 5 trials in the learning phase would echo those at the transfer phase. I think it would be stronger to link the preference learning results to the change between the baseline and transfer phase, eg, by looking at the difference between alpha (beta) at the end of the learning phase and the initial alpha (beta).

(6) I wonder if data from the baseline and transfer phases can also be modeled, using a simple Fehr-Schimdt model. This way, the change in alpha/beta can also be examined between the baseline and transfer phase.

(7) I quite liked Study 2 which tests the generalization effect, and I expected to see an adapted computational modeling to directly reflect this idea. Indeed, the authors wrote, "[...] given that this model [...] assumes the sort of generalization of preferences between offer types [...]". But where exactly did the preference learning model assume the generalization? In the methods, the modeling seems to be only about Study 1; did the authors advise their model to accommodate Study 2? The authors also ran simulation for the learning phase in Study 2 (Figure 6), and how did the preference update (if at all) for offers (90:10 and 10:90) where feedback was not given? Extending/Unpacking the computational modeling results for Study 2 will be very helpful for the paper.

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Reply to the reviewers

Reviewer #1

General Comment. *Using ubiquitous and targeted heterologous expression of the honeybee venom peptide Apamin in Drosophila, the authors find that apamin has antimicrobial activity that is enhanced by membrane-tethering and dependent on the Drosophila pattern-recognition receptors PGRP-LA and PGRP-SC2. Expression of apamin in the Drosophila gut or ingestion of Apamin by honeybees has positive effects on gut health as shown by a number of metrics. *

__ Answer: __We thank the reviewer for their insightful comments. We agree that the findings of this study are significant and have broad implications for understanding the antimicrobial properties of apamin. As suggested, we have further delved into the molecular mechanisms underlying apamin's antimicrobial activity, providing additional details on its interactions with target bacteria. We have also expanded our discussion on the role of membrane-tethering in enhancing apamin's activity and its potential impact on its localization. We believe that these additional illustrations strengthen our conclusions and provide a more comprehensive understanding of apamin's biological functions.

Major comments:

Comment 1. *The key conclusions are convincing and largely supported by the data as shown. The data is presented clearly, save for some areas in the results where the authors should be more explicit about the methods that were used as they affect the reader's interpretation of the results (see minor comments). *

__ Answer: __We would like to express our gratitude to the reviewer for their constructive feedback and positive remarks regarding our manuscript. We are pleased to note that the reviewer found our key conclusions convincing and largely supported by the data presented. This affirmation encourages us as we strive to contribute meaningful insights to the field. We acknowledge the reviewer's suggestion to enhance clarity in certain areas of the Results section, particularly concerning the methods employed. We appreciate this guidance and have taken it into account. In our revised manuscript, we have made explicit revisions to ensure that the methodology is clearly articulated, thereby improving the reader's interpretation of our results. Thank you once again for your valuable feedback, which has undoubtedly strengthened our work. We look forward to your continued guidance as we finalize our manuscript.

Comment 2. *If the authors wish to conclude that PGRP-LE and PGRP-LC are not required for the demonstrated functions of Apamin, the authors should do a double knock-down of PGRP-LC and LE together, as these pattern recognition receptors function partially redundantly in activation of the Imd pathway (e.g. doi: 10.1038/ni1356). *

__ Answer:__ We appreciate reviewer's interesting suggestion to know PGRP-LE and LC's functions are redundant to activate Imd pathway or Apamin is totally independent of Imd pathway. As reviewer suggested, we have conducted double knockdown of PGRP-LE and PGRP-LC and showed that apamin still suppress bacterial infection regardless of these double knockdowns of these genes. This data suggests that apamin's antimicrobial function is totally not dependent on PGRP-LE or LC and open new questions about apamin's unique function as AMP. We added new data in Fig. 5d and described in main text as below:

"Knockdown of PGRP-LC or LE, as well as their combined knockdown, did not affect the antimicrobial efficacy of apamin (Fig. 5b-d), suggesting that the antimicrobial properties of apamin are independent of PGRP-LC and LE functions (Fig. 5a)."

Comment 3. *The Introduction and Discussion would benefit from providing more context that helps the reader understand the significance of the research. Where is apamin expressed in the honeybee? Is it likely to be ingested and have effects on gut health in natural conditions? Do honeybees have homologs of PGRP-LA and PGRP-SC2? Do these findings translate to the honeybee system in any way or are they restricted to heterologous expression in Drosophila? *

__Answer: __We thank the reviewer for valuable suggestions. We agree that providing additional context on the natural role of apamin in honeybees and the relevance of our findings to the honeybee system is crucial.

Natural expression and function of apamin: While apamin is primarily known for its neurotoxic effects, studies have suggested that it may also play a role in antimicrobial defense. While its specific expression pattern in honeybees is not fully understood, it is conceivable that it is mainly expressed in venom sacs according to research on biochemistry and pharmacology of apamin (Habermann, 1972; Schumacher et al, 1994; INOUE et al, 1987) . We have outlined this information in the Introduction section as follows:

"Apamin, an 18 amino acid peptide neurotoxin, is one of the bioactive components of bee venom, making up 2%-3% of its total dry weight, naturally expressed in bee venom sacs (RIETSCHOTEN et al, 1975; E.H., 1976; Son et al, 2007; Zhou et al, 2010; Habermann, 1972)."

Potential for ingestion and gut effects: Although direct evidence for apamin ingestion and its impact on gut health in natural conditions is limited, it is plausible that honeybees could be exposed to apamin through various means, including foraging and social interactions. However, artificial interference is the potential application method that we are more focusing on. We have included additional details regarding the function of apamin in the Introduction section as follows:

"It is the smallest known neurotoxic polypeptide and exhibits elevated basicity and sulfur content, demonstrating prolonged action relative to other pharmacological agents influencing the central or peripheral nervous systems(Habermann, 1972)."

Honeybee homologs of PGRPs: Concerning the honeybee PGRPs and their homologs in Drosophila, we have provided an explanation as follows:

"While honeybees possess homologs of PGRP family, including PGRP-LC and PGRP-S2, their specific roles in response to apamin and other antimicrobial peptides remain to be elucidated(Larsen et al, 2019a)."

Relevance to the honeybee system: While our study primarily utilized Drosophila as a model system, the conserved nature of innate immune pathways suggests that the findings may have broader implications for honeybee health. Future studies aimed at directly investigating the effects of apamin in honeybees will be essential to fully understand its role in their physiology and behavior. We have incorporated these points into the Discussion sections to provide a more comprehensive and informative overview of our research as below:

"In conclusion, it is important to note that much of our understanding of the honeybee immune system is derived from studies conducted on the Drosophila model, owing to the evolutionary proximity of these two species (Larsen et al, 2019b). This close relationship allows for valuable insights into immune mechanisms that are conserved across species (Evans et al, 2006; Morfin et al, 2021). Research has demonstrated that the fruit fly Drosophila melanogaster serves as an effective model for studying the effects of insecticides on honeybees, particularly in understanding the sub-lethal impacts of neonicotinoids, which are known to affect pollinators significantly (Tasman et al, 2021).

By investigating the function of honeybee AMPs within the Drosophila platform, we can further enhance our knowledge of immune responses and their implications. Just as research on Drosophila has significantly advanced our understanding of human genetic diseases (Bellen et al, 2010; Casci & Pandey, 2015; Bier, 2005; Perrimon et al, 2016; Rieder & Larschan, 2014; Bilder et al, 2021), studying honeybee AMPs in this context holds the potential to uncover novel therapeutic avenues and deepen our comprehension of immune function across taxa."

Comment 4. *It is surprising that there is no speculation or hypothesis provided about why PGRP-LA and -SC2 may enhance apamin activity whereas other components are nonessential. It was a significant part of the paper but receives almost no discussion. *

Answer: We thank the reviewer for highlighting this important point. The specific mechanism by which PGRP-LA and PGRP-SC2 enhance apamin's activity is an intriguing question that warrants further investigation. Our findings indicate that both PGRP-LA and PGRP-SC2 are crucial for the antimicrobial action of apamin, as their knockdown abolishes this effect, suggesting a specific functional relationship between these peptidoglycan recognition proteins and apamin's mechanism of action in the gut environment.

PGRP-LA is known to play a significant regulatory role as positive regulator of immune responses, while PGRP-SC2 has been shown to promote gut immune homeostasis and prevent dysbiosis, which is essential for maintaining a balanced microbiome in Drosophila (Guo et al, 2014). The enhancement of apamin activity by these proteins could be attributed to their ability to modulate the immune response and facilitate a more effective antimicrobial environment, thereby allowing apamin to exert its effects more efficiently.

Furthermore, our study aligns with previous research indicating that PGRP-SC2 can limit commensal dysbiosis and promote tissue homeostasis, which may enhance the overall efficacy of antimicrobial peptides like apamin in combating pathogenic bacteria (Guo et al, 2014). By leveraging the evolutionary insights gained from Drosophila, we can better understand how these mechanisms operate in honeybees, ultimately contributing to our knowledge of immune function across species. We have provided a detailed explanation of the potential roles of PGRP-LA and PGRP-SC2 in the action of apamin, as outlined below:

"The PGRP-LA gene is located in a cluster with PGRP-LC and PGRP-LF, which encode a receptor and a negative regulator of the Imd pathway, respectively; structural predictions suggest that PGRP-LA may not directly bind to peptidoglycan, indicating a potential regulatory role for this PGRP in modulating immune responses (Gendrin et al, 2013). PGRP-SC2 possesses amidase activity, which means it can cleave the peptidoglycan layer of bacterial cell walls, rendering them susceptible to further degradation and ultimately leading to bacterial cell death. This amidase activity contributes to the insect's innate immune response by directly targeting and neutralizing bacterial threats (Takehana et al, 2002; Park et al, 2007; Paredes et al, 2011)."

Comment 5. *Line 264: The fact that Rel knockdown did not impair antimicrobial activity of Apamin is a bit odd since upregulation of PGRP-SC2 upon infection is at least partially dependent on Rel (de Gregorio 2002, EMBO J), and the authors find that PGRP-SC2 is required for apamin activity. This is somewhat incongruous. *

__Answer: __We thank the reviewer for highlighting this important point. The observation that Rel knockdown did not impair apamin's antimicrobial activity, despite its role in upregulating PGRP-SC2, is indeed intriguing.

Several factors may contribute to this discrepancy:

Redundancy in PGRP-SC2 regulation: It is possible that other transcription factors, in addition to Rel, may regulate PGRP-SC2 expression. Therefore, even in the absence of Rel, sufficient levels of PGRP-SC2 may be maintained to support apamin's activity(Bischoff et al, 2006) . Direct effects of apamin: Apamin may directly interact with bacterial cells or host immune cells and contribute to its antimicrobial activity, even in the absence of optimal PGRP-SC2 levels.

We cited (de Gregorio 2002, EMBO J) paper and added explanation for this result as below:

"It is known that the upregulation of PGRP-SC during infection is partially reliant on the Rel pathway (Gregorio et al, 2002). Our findings indicate that apamin can exert its antimicrobial activity independently of Rel's transcriptional activation function. This observation can be attributed to two key factors. First, there may be redundancy in the regulation of PGRP-SC2 expression, as other transcription factors could compensate for the absence of Rel, allowing sufficient levels of PGRP-SC2 to be maintained to support apamin's activity. Second, apamin may have direct interactions with bacterial cells or host immune cells, contributing to its antimicrobial effects even when optimal levels of PGRP-SC2 are not present. These mechanisms suggest that apamin can function effectively in the immune response, highlighting its potential as a versatile antimicrobial agent."

Comment 6. *I cannot comment on the adequacy of the statistical analyses. Some recommendations to improve the methods: *

*- Be specific about the kind of medium used to rear flies (provide or cite recipe). Different cornmeal-yeast media have very different compositions and can affect fly physiology and microbiome characteristics. *

*- Specify flipping schedule (every 2-3 days?) - this also affects microbiome. *

__Answer: __We thank the reviewer for their valuable comments. We agree that precise experimental details are crucial for reproducibility and accurate interpretation of results.

To address the reviewer's specific concerns:

Culture medium: We used a standard cornmeal-molasses-agar medium. The specific recipe for this medium is as follows: water add up to 5 L，agar 47g, inactive yeast 65.5g, corn flour 232.5g, soy flour 30g, molasses 350 ml, tegosept sol. 35g, propionic acid 12.5ml, phosphoric acid 2.5ml. Flipping schedule: Flies were flipped every 2-3 days to prevent overcrowding and maintain optimal culture conditions.

We have included these details in the Methods section to enhance the clarity and reproducibility of our experiments.

Minor comments:

*- Line 90: Be specific about how the constructs differ from endogenous Melittin and Apamin. Do the endogenous versions have signal peptides? *

Answer: The endogenous versions do not have signal peptides we have used, we have specified this in the manuscript for readers to have a better understanding as below:

"To assess the functionality of genetically encoded honeybee VPs in the Drosophila model, we developed UAS-Melittin, and UAS-Apamin constructs that incorporate a previously characterized signal peptide at their N-termini (Choi et al, 2009), which original AMP and VP sequences do not have (Fig. 1a)."

- Line 92: What is 'broad expression'? Ubiquitous? Specify driver or extent of expression.

Answer: We have added "by tub-GAL4 driver"

*- Line 93: Was this oral or septic P. aeruginosa infection? *

Answer: We have added "oral"

*- Lines 97-98: Melittin expressed genetically did not show activity against the one pathogen that was tested; making a broad statement without qualification about activity seems excessive. *

Answer: We have added "against P. aeruginosa"

*- Line 105: Various Gal4 drivers that express in different tissues or a similar subset of tissues? *

Answer: We utilized tub-GAL4 and da-GAL4 in this part of screening, they both drive expression in ubiquitous tissues. Daughterless (da) involves in the transcriptional regulation of various processes, including oogenesis, neurogenesis, myogenesis, and cell proliferation. While tub-GAL4 is ubiquitous expression throughout most tissues and cell types in the Drosophila body. We have added "various ubiquitously expressing"

*- Line 134: Present as a commensal? Pathobiont? Pathogen? *

Answer: Apibacter raozihei is generally considered a commensal bacterium in the honeybee gut. We have added to manuscript "which is present as a commensal bacterium in the guts of".

*- Line 149: Are Cyanobacteria naturally present in gut microbiota? What are photosynthetic bacteria doing as part of a gut microbiome? *

Answer: While cyanobacteria are not typically found in the gut, cyanobacterial 16S rRNA-like sequences have been previously detected in human gut samples, bovine rumen, termite gut, and other animal intestines, suggesting the presence of a non-photosynthetic cyanobacterial lineage in these aphotic environments(Hu & Rzymski, 2022; Hongoh et al, 2003).

*- Line 171: Where is apamin endogenously expressed in the honeybee? Only in the venom gland? Or in gut cells as done here in Drosophila? *

Answer: Natural expression and function of apamin: While apamin is primarily known for its neurotoxic effects, studies have suggested that it may also play a role in antimicrobial defense. While its specific expression pattern in honeybees is not fully understood, it is conceivable that it is mainly expressed in venom sacs according to research on biochemistry and pharmacology of apamin (Habermann, 1972; Schumacher et al, 1994; INOUE et al, 1987) .

*- Line 252: -LC and -LE work in a complementary/semi-redundant fashion, so single knockdown is not an effective method of indicating that they are not required for antimicrobial function. *

Answer: We appreciate reviewer's interesting suggestion to know PGRP-LE and LC's functions are redundant to activate Imd pathway or Apamin is totally independent of Imd pathway. As reviewer suggested, we have conducted double knockdown of PGRP-LE and PGRP-LC and showed that apamin still suppress bacterial infection regardless of these double knockdowns of these genes. This data suggests that apamin's antimicrobial function is totally not dependent on PGRP-LE or LC and open new questions about apamin's unique function as AMP. We added new data in Fig. 5d and described in main text as below:

"Knockdown of PGRP-LC or LE, as well as their combined knockdown, did not affect the antimicrobial efficacy of apamin (Fig. 5b-d), suggesting that the antimicrobial properties of apamin are independent of PGRP-LC and LE functions (Fig. 5a)."

*- Lines 279-283: The bacterial infections that expression of these AMPs were tested against should be mentioned in the text, as all bacteria are not equivalent. *

Answer: Added with "P. aeruginosa"

*- Line 296: Challenged with which bacteria? *

Answer: Added with "P. aeruginosa"

*- Line 328: Provide brief explanation of what Ttk depletion is for reader context. *

Answer: Added with short explanation as below:

"which refers to the reduction or elimination of a protein called TTK (Monopolar Spindle 1 Kinase) that plays a crucial role in cell division, specifically in ensuring accurate chromosome segregation during mitosis (Mason et al, 2017)."

*- Line 719: This should say, '5 days after eclosion'. *

Answer: Corrected

*- General comment on figures: The little icons used to denote what the figure is depicting (gut health, climbing, aging, etc.) are very effective. *

Answer: We thank the reviewer for their appreciation on figures.

*- General comment on figure titles: Use of the term 'infectious dose' throughout does not make sense. I think what the authors mean is 'pathogen load' as they are testing using CFUs. 'Infectious dose' should only be used to refer to the amount/OD of pathogen that was initially administered to establish an infection. Also, 'oral feeding' should be used throughout instead of 'orally feeding'. *

Answer: We thank the reviewer for their insightful comment. We agree that the use of the term 'infectious dose' was inaccurate in certain contexts. We have revised the manuscript to use 'pathogen load' to refer to the number of CFUs administered or recovered, as this more accurately reflects the bacterial burden.

We have also replaced 'orally feeding' with 'oral feeding' throughout the manuscript to improve clarity and consistency.

We appreciate the reviewer's attention to detail and believe that these changes have significantly enhanced the clarity and accuracy of the manuscript.

*- Figure 1O: Abrupt die-offs at 1000hrs and 2800hrs in the UAS-Melittin line suggest that lifespan experiment was only performed once and that die-offs may have been exacerbated due to infrequent flipping. This is perhaps not an issue as the lifespans appear to be quite different between the active line and control regardless. *

Answer: We thank the reviewer for their careful observation. The abrupt die-offs in the UAS-Melittin line at 1000 hours and 2800 hours were unexpected. While we cannot definitively rule out the possibility that infrequent flipping might have contributed to these events, we believe that the overall lifespan difference between the experimental and control groups is substantial and likely reflects a genuine biological effect of Melittin overexpression.

*- Figure 2F would be improved by putting the legend in the same descending order that the genotypes are displayed on the graph (tApamin infected, GFP infected, tApamin, GFP) *

Answer: We have corrected error.

*- Figure 3I: Unclear what small image inserted in the graph depicts. *

Answer: This is an image of fly stem cells that is available for free licensing.

- Figures 3N and 3O are verry low resolution and difficult to identify the differences that the authors *intend to show. *

Answer: We have utilized a higher resolution image and revised the figure accordingly.

- Figure 4 title is confusing. Do the authors mean, "Locomotion of flies expressing neuronal Apamin, sleep in flies with ubiquitous expression of Apamin, and Smurf results induced by different types of stress."?

Answer: Corrected as below:

"Locomotion of flies expressing neuronal tApaminDC, sleep in flies with ubiquitous expression of tApaminDC, and Smurf results induced by different types of stress."

*- Figure 5: Some of these graphs are very cluttered and difficult to parse (particularly 5H). Suggest putting peptide sequences in figure title rather than underneath graphs to simplify and increase visual effectiveness. *

Answer: We have improved by removing the sequences to figure legend part.

*-Throughout: Methods section in particular could use a solid edit for grammar. Homogenize capitalization of "Gram-negative/-positive" and "gram-negative/-positive" *

Answer: We have corrected error.

*- Line 98: "an AMPs" should be "an AMP" *

Answer: We have corrected error.

*- Line 119: Incorrect grammar. Suggest, "which did not affect the lifespan of female flies and had only a slight effect on male flies" *

Answer: We have corrected error.

Reviewer #1 (Significance (Required)):

*The paper reveals that apamin has antimicrobial properties. The intended significance seems to be an exploration of apamin for therapeutic potential in gut health, but this is not explicitly stated by the authors. The contribution mainly appears to be conceptual in nature. *

*The findings appear to be in line with other recent in vitro results suggesting that apamin has antimicrobial properties (DOI: 10.9775/kvfd.2024.32125). *

*Researchers interested in developing therapeutic applications for bee venom constituents or promoting gut health and microbiome balance will likely find this research of interest. *

*My expertise is primarily in Drosophila molecular genetics and immunity. I have a broad understanding of Drosophila immune pathways, epithelial immunity, and infection dynamics. I do not feel qualified to comment on the statistics or data analysis aspects of this paper. *

Answer: We sincerely appreciate the reviewer's positive feedback regarding our findings on the antimicrobial properties of apamin. We are grateful for the acknowledgment that our results align with recent in vitro studies, such as the one referenced (DOI: 10.9775/kvfd.2024.32125), which further supports the significance of our work. We have cited this paper in the Discussion section as below.

"Our findings are consistent with recent in vitro studies demonstrating the antimicrobial and antibiofilm effects of apamin (AYDIN et al, 2024)."

We recognize the reviewer's observation that our intended significance-specifically, the exploration of apamin's therapeutic potential for gut health-was not explicitly stated in the original manuscript. To address this, we have revised the Introduction and Discussion sections to clearly articulate our aim of investigating apamin as a candidate for promoting gut health and microbiome balance. We believe this clarification will enhance the conceptual contribution of our study and its relevance to researchers interested in therapeutic applications of bee venom constituents.

"Apamin shows promising therapeutic potential for enhancing bee gut health by exhibiting antimicrobial properties that can help maintain a balanced microbiome. Its ability to modulate immune responses and promote gut integrity, particularly in the presence of harmful bacteria, positions apamin as a valuable candidate for developing strategies aimed at improving gut health in honeybees."

Additionally, we appreciate the reviewer's expertise in Drosophila molecular genetics and immunity, and we are grateful for their insights regarding the broader implications of our research. We will ensure that our manuscript reflects these considerations more explicitly.

Thank you once again for your valuable feedback, which has helped us improve the clarity and impact of our work.

Reviewer #2

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

General Comment. *The reviewer would like to thank the authors for their contributions to the research of animal venoms and their therapeutic value. The manuscript is very well and clearly written. Additionally, the choice of using a model organism such as D. melanogaster in the context of venoms research strengthens the manuscript by providing evidence that is both robust and broadly applicable, thus enhancing the manuscript's scientific merit and relevance to the field. *

Answer: We would like to express our sincere gratitude to the reviewer for the positive feedback and thoughtful comments regarding our manuscript. We are pleased to hear that the reviewer appreciates our contributions to the research on animal venoms and their therapeutic potential. The reviewer's acknowledgment of the clarity and quality of our writing is particularly encouraging, as we strive to communicate our findings effectively. Additionally, we are glad that the choice of Drosophila melanogaster as a model organism was recognized for its ability to strengthen our research by providing robust and broadly applicable evidence. This endorsement enhances the scientific merit and relevance of our work within the field. Thank you once again for the constructive feedback, which has been invaluable in refining our manuscript.

Comment 1. *What is the significance of that the biological property of apamin is independent of its disulfide bonds? Does it suggest that the core functional parts of apamin might not entirely depend on its stabilized structure? Could it mean that modifications to the molecule that disrupt disulfide bonds wouldn't necessarily eliminate all of its activity, which could be important in designing analogs or derivatives of apamin for research or therapeutic purposes etc.? This sentence is written in the abstract which means that it should be a key finding, and it should be clear and a given to the reader. However, it is not the case, and it should be stated more clearly. *

Answer: We greatly appreciate the reviewer for the perceptive notation. The fact that the biological functioning of apamin needs no disulfide bonds should bring forth the attention of the scientists because it has further implications. This hints that apamin's major functional units are most likely to compose from its polypeptide instead of being rooted in the disulfide-stabilized tertiary structure(Habermann, 1972). The strategy can then lead to the optimization of apamin-based drugs with altered disulfide bridges granting them either higher activity or reduced toxicity. These changes can give apamin additional properties like stability, bioavailability, or selectivity, which make it suitable for research and applied use. We have included an explanation for this in both the Results and Discussion sections.

"This finding suggests that the core functional components of apamin may not be entirely reliant on its stabilized structure."

"We discovered that apamin lacking the C-terminus retains its function as an antimicrobial agent, despite missing one of its two disulfide bridges. This finding suggests that the core functional components of apamin may not be entirely dependent on its stabilized structure, indicating that modifications to the molecule that disrupt these disulfide bonds could still maintain some level of activity. These insights are vital for designing analogs or derivatives of apamin, as they pave the way for developing new compounds that could retain therapeutic potential even without the native disulfide bond configuration (Habermann, 1972)."

Comment 2. *The authors well explained the evolutionary proximity between apamin producing Honeybees and D. melanogaster in order to justify the choice of the model organism which we can all agree on for genetics and developmental biology studies. However, when addressing the behavior of the insects (sleeping, locomotion, social etc.) which are driven by their ecological roles, evolutionary strategies, and social complexity. How much can you really tell about the role of apamin in the behavior of Honeybees (highly social and form colonies) by studying it on an insect (D. melanogaster) which has a completely different and divergent behavior (solitary and exhibit only few basic forms of social interaction)? *

Answer: We appreciate the reviewer's insightful comment. While Drosophila melanogaster is an excellent model organism for investigating fundamental biological processes, we recognize the limitations of using it to fully comprehend the complex behavioral effects of apamin in honeybees. Nevertheless, our study establishes a foundational understanding of apamin's potential impact on behavior, including its effects on sleep and locomotion-core behavioral processes that are conserved across many organisms, including insects (Zimmerman et al, 2008).

By employing Drosophila as a model, we were able to identify potential mechanisms of action for apamin, particularly regarding its effects on intestinal systems. Although honeybees and fruit flies exhibit ecological differences, there is substantial consensus and experimental evidence that many molecular pathways involved in immune responses are conserved between these species. Thus, while the interpretation of behavioral changes induced by apamin may be limited by the ecological and evolutionary divergence between honeybees and fruit flies, the molecular pathways governing the immune response in honeybees can be effectively studied using the Drosophila platform. This approach has previously revealed functions of genes related to human genetic diseases. We have clearly articulated this limitation and the advantages of using the fly model to study the honeybee immune system in the Discussion section as follows:

"In conclusion, it is important to note that much of our understanding of the honeybee immune system is derived from studies conducted on the Drosophila model, owing to the evolutionary proximity of these two species (Larsen et al, 2019b). This close relationship allows for valuable insights into immune mechanisms that are conserved across species (Evans et al, 2006; Morfin et al, 2021). Research has demonstrated that the fruit fly Drosophila melanogaster serves as an effective model for studying the effects of insecticides on honeybees, particularly in understanding the sub-lethal impacts of neonicotinoids, which are known to affect pollinators significantly (Tasman et al, 2021).

By investigating the function of honeybee AMPs within the Drosophila platform, we can further enhance our knowledge of immune responses and their implications. Just as research on Drosophila has significantly advanced our understanding of human genetic diseases (Bellen et al, 2010; Casci & Pandey, 2015; Bier, 2005; Perrimon et al, 2016; Rieder & Larschan, 2014; Bilder et al, 2021), studying honeybee AMPs in this context holds the potential to uncover novel therapeutic avenues and deepen our comprehension of immune function across taxa."

Comment 3. *Please include the following references: *

• Wehbe R, Frangieh J, Rima M, El Obeid D, Sabatier JM, Fajloun Z. Bee Venom: Overview of Main Compounds and Bioactivities for Therapeutic Interests. Molecules. 2019 Aug 19;24(16):2997. *

• Nader RA, Mackieh R, Wehbe R, El Obeid D, Sabatier JM, Fajloun Z. Beehive Products as Antibacterial Agents: A Review. Antibiotics. 2021; 10(6):717. *

Answer: We have incorporated the references mentioned above in appropriate sections of the manuscript. We appreciate the reviewer's suggestions.

Reviewer #2 (Significance (Required)):

The manuscript is very well and clearly written. Additionally, the choice of using a model organism such as D. melanogaster in the context of venoms research strengthens the manuscript by providing evidence that is both robust and broadly applicable, thus enhancing the manuscript's scientific merit and relevance to the field.

Answer: We would like to express our sincere gratitude to the reviewer for their positive feedback regarding our manuscript. We are thrilled to hear that the clarity and quality of our writing were appreciated. Additionally, we are glad that the choice of Drosophila melanogaster as a model organism in our venoms research was recognized for its ability to provide robust and broadly applicable evidence. This endorsement underscores the scientific merit and relevance of our work within the field, and we appreciate the reviewer's acknowledgment of this important aspect. Thank you for your encouraging comments, which motivate us to continue exploring this vital area of research.

This work has been published in GigaByte Journal under a CC-BY 4.0 license (https://doi.org/10.46471/gigabyte.143). These reviews are as follows.

**Reviewer 1. Joost Wagenaar **

Is there a clear statement of need explaining what problems the software is designed to solve and who the target audience is?

Yes. There is a clear statement of need, but the audience is not very targeted. The investigators outline the need for tools to help users identify phenotypic subtypes of disease and describe how the tool would help with this. Although the investigators mention that the tool will allow users to analyze biomarker data, the scope of the types of analysis that can be performed is relatively small. I think that it would benefit the tool to better define the targeted users (clinicians, data scientists, enthusiasts?) and develop specifically towards a single audience.

The tool leverages several existing R packages to run the analysis over the data and the provided tool can be described as a user-friendly wrapper around these libraries. The interface allows users to submit a file, and plot the results of the analysis within the app.

As Open Source Software are there guidelines on how to contribute, report issues or seek support on the code?

No. I did not see any guidelines for contributing to the project in the paper, or in the associated GitHub repository.

Is the documentation provided clear and user friendly?

Yes, the investigators did a great job providing documentation and installation instructions. [also video demo: https://youtu.be/cYZ8WOvabJs?si=DnxVuL65yr0wYYjq]

Is there a clearly-stated list of dependencies, and is the core functionality of the software documented to a satisfactory level?

Yes, the investigators provide a clearly-stated list of dependencies and instructions on how to install them prior to running the application. Is test data available, either included with the submission or openly available via cited third party sources (e.g. accession numbers, data DOIs)?