Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Most studies in sensory neuroscience investigate how individual sensory stimuli are represented in the brain (e.g., the motion or color of a single object). This study starts tackling the more difficult question of how the brain represents multiple stimuli simultaneously and how these representations help to segregate objects from cluttered scenes with overlapping objects.

Strengths

The authors first document the ability of humans to segregate two motion patterns based on differences in speed. Then they show that a monkey's performance is largely similar; thus establishing the monkey as a good model to study the underlying neural representations.

Careful quantification of the neural responses in the middle temporal area during the simultaneous presentation of fast and slow speeds leads to the surprising finding that, at low average speeds, many neurons respond as if the slowest speed is not present, while they show averaged responses at high speeds. This unexpected complexity of the integration of multiple stimuli is key to the model developed in this paper.

One experiment in which attention is drawn away from the receptive field supports the claim that this is not due to the involuntary capture of attention by fast speeds.

A classifier using the neuronal response and trained to distinguish single-speed from bi-speed stimuli shows a similar overall performance and dependence on the mean speed as the monkey. This supports the claim that these neurons may indeed underlie the animal's decision process.

The authors expand the well-established divisive normalization model to capture the responses to bi-speed stimuli. The incremental modeling (eq 9 and 10) clarifies which aspects of the tuning curves are captured by the parameters.

We thank the Reviewer for the thorough summary of the findings and supportive comments.

Weaknesses

While the comparison of the overall pattern of behavioral performance between monkeys and humans is important, some of the detailed comparisons are not well supported by the data. For instance, whether the monkey used the apparent coherence simply wasn't tested and a difference between 4 human subjects and a single monkey subject cannot be tested statistically in a meaningful manner. I recommend removing these observations from the manuscript and leaving it at "The difference between the monkey and human results may be due to species differences or individual variability" (and potentially add that there are differences in the task as well; the monkey received feedback on the correctness of their choice, while the humans did not.)

Thanks for the suggestion. We agree and have modified the text accordingly. We now state on page 8, lines 189-191, "The difference between the monkey and human results may be due to species differences or individual variability. The differences in behavioral tasks may also play a role – the monkey received feedback on the correctness of the choice, whereas human subjects did not."

A control experiment aims to show that the "fastest speed takes all" behavior is general by presenting two stimuli that move at fast/slow speeds in orthogonal directions. The claim that these responses also show the "fastest speed takes all" is not well supported by the data. In fact, for directions in which the slow speed leads to the largest response on its own, the population response to the bi-speed stimulus is the average of the response to the components (This is fine. One model can explain all direction tuning curve, which also explain averaging at the slower speed stronger directions). Only for the directions where the fast speed stimulus is the preferred direction is there a bias towards the faster speed (Figure 7A). The quantification of this effect in Figure 7B seems to suggest otherwise, but I suspect that this is driven by the larger amplitude of Rf in Figure 8, and the constraint that ws and wf are constant across directions. The interpretation of this experiment needs to be reconsidered.

The Reviewer raised a good question. Our model with fixed weights for faster and slower components across stimulus directions provided a parsimonious explanation for the whole tuning curve, regardless of whether the faster component elicited a stronger response than the slower component. Because the model can be well constrained by the measured direction-tuning curves, we did not restrain 𝑤 and 𝑤 to sum to one, which is more general. The linear weighted summation (LWS) model fits the neuronal responses to the bi-speed stimuli very well, accounting for an average of 91.8% (std = 7.2%) of the response variance across neurons. As suggested by the Reviewer, we now use the normalization model to fit the data with fixed weights across all motion directions. The normalization model also provides a good fit, accounting for an average of 90.5% (std = 7.1%) of the response variance across neurons.

Note that in the new Figure 8A, at the left side of the tuning curve (i.e., at negative vector average (VA) directions), where the slower component moving in a more preferred direction of the neurons than the faster component, the bi-speed response (red curve) is slightly lower than the average of the component response (gray curve), indicating a bias toward the weaker faster component. Therefore, the faster speed bias does not occur only when the faster component moves in the more preferred direction. This can also be seen in the direction-tuning curves of an example neuron that we added to the figure (new Fig. 8B). The peak responses to the slower and faster component were about the same, but the neuron still showed a faster-speed bias. At negative VA directions, the red curve is lower than the response average (gray curve) and is biased toward the weaker (faster) component.  

The faster-speed bias also occurs when the peak response to the slower component is stronger than the faster component. As a demonstration, Author response image 1 1 shows an example MT neuron that has a slow preferred speed (PS = 1.9 deg/s) and was stimulated by two speeds of 1.2 and 4.8 deg/s. The peak response to the faster component (blue) was weaker than that to the slower component (green). However, this neuron showed a strong bias toward the faster component. A normalization model fit with fixed weights for the faster and slower components (black curve) described the neuronal response to both speeds (red) well. This neuron was not included in the neuron population shown in Figure 8 because it was not tested with stimulus speeds of 2.5 and 10 deg/s.

Author response image 1.

An example MT neuron was tested with stimulus speeds of 1.2 and 4.8 deg/s. The preferred speed of this neuron was 1.9 deg/s. Fixed weights of 0.59 for the faster component and 0.12 for the slower component described the responses to the bispeed stimuli well using a normalization model. The neuron showed a faster-speed bias although its peak response to the slower component was higher than that of the faster component.

We modified the text to clarify these points:

Page 19, lines 405 – 410, “The bi-speed response was biased toward the faster component regardless of whether the response to the faster component was stronger (in positive VA directions) or weaker (in negative VA directions) than that to slower component (Fig. 8A). The result from an example neuron further demonstrated that, even when the peak firing rates of the faster and slower component responses were similar, the response elicited by the bi-speed stimuli was still biased toward the faster component (Fig. 8B). ”

Page 19, lines 421 – 427, “Because the model can be well constrained by the measured direction-tuning curves, it is not necessary to require 𝑤 and 𝑤 to sum to one, which is more general. An implicit assumption of the model is that, at a given pair of stimulus speeds, the response weights for the slower and faster components are fixed across motion directions. The model fitted MT responses very well, accounting for an average of 91.8% of the response variance (std = 7.2%, N = 21) (see Methods). The success of the model supports the assumption that the response weights are fixed across motion directions.”

Reviewer #2 (Public Review):

Summary:

This is a paper about the segmentation of visual stimuli based on speed cues. The experimental stimuli are random dot fields in which each dot moves at one of two velocities. By varying the difference between the two speeds, as well as the mean of the two speeds, the authors estimate the capacity of observers (human and non-human primates) to segment overlapping motion stimuli. Consistent with previous work, perceptual segmentation ability depends on the mean of the two speeds. Recordings from area MT in monkeys show that the neuronal population to compound stimuli often shows a bias towards the faster-speed stimuli. This bias can be accounted for with a computational model that modulates single-neuron firing rates by the speed preferences of the population. The authors also test the capacity of a linear classifier to produce the psychophysical results from the MT data.

Strengths:

Overall, this is a thorough treatment of the question of visual segmentation with speed cues. Previous work has mostly focused on other kinds of cues (direction, disparity, color), so the neurophysiological results are novel. The connection between MT activity and perceptual segmentation is potentially interesting, particularly as it relates to existing hypotheses about population coding.

We thank the Reviewer for the summary and comments.

Weaknesses:

Page 10: The relationship between (R-Rs) and (Rf-Rs) is described as "remarkably linear". I don't actually find this surprising, as the same term (Rs) appears on both the x- and y-axes. The R^2 values are a bit misleading for this reason.

The Reviewer is correct that subtracting a common term Rs from R and Rf would introduce correlation between (R-Rs) and (Rf-Rs). To address this concern, we conducted an additional analysis. We showed that, at most speed pairs, the R^2 values between (R-Rs) and (Rf-Rs) based on the data are significantly higher than the R^2 values between (R’-Rs) and (RfRs), in which R’ was a random combination of Rs and Rf. Since the same Rs was commonly subtracted in calculating R^2 (data) and R^2 (simulation), the difference between R^2 (data) and R^2 (simulation) suggests that the response pattern of R contributes to the additional correlation.

We now acknowledge this confounding factor and describe the new analysis results on page 14, lines 309 – 326. Please also see the response to Reviewer 3 about a similar concern.

Figure 9: I'm confused about the linear classifier section of the paper. The idea makes sense - the goal is to relate the neuronal recordings to the psychophysical data. However the results generally provide a poor quantitative match to the psychophysical data. There is mention of a "different paper" (page 26) involving a separate decoding study, as well as a preprint by Huang et al. (2023) that has better decoding results. But the Huang et al. preprint appears to be identical to the current manuscript, in that neither has a Figure 12, 13, or 14. The text also says (page 26) that the current paper is not really a decoding study, but the linear classifier (Figure 9F) is a decoder, as noted on page 10. It sounds like something got mixed up in the production of two or more papers from the same dataset.

We apologize for the confusion regarding the reference of Huang et al. (2023, bioRxiv). We referred to an earlier version of this bioRxiv manuscript (version 1), which included decoding analysis. In the bibliography, we provided two URLs for this pre-print. While the second link was correct, the first URL automatically links to the latest version (version 2), which did not have the abovementioned decoding analysis.

The analysis in Figure 9 is to apply a classifier to discriminate two-speed from singlespeed stimuli, which is a decoding analysis as the Reviewer pointed out. We revised the result section about the classifier to make it clear what the classifier can and cannot explain (pages 2223, lines 516-534). We also included a sentence at the end of this section that leads to additional decoding analysis to extract motion speed(s) from MT population responses (page 23, lines 541543), “To directly evaluate whether the population neural responses elicited by the bi-speed stimulus carry information about two speeds, it is important to conduct a decoding analysis to extract speed(s) from MT population responses.”

In any case, I think that some kind of decoding analysis would really strengthen the current paper by linking the physiology to the psychophysics, but given the limitations of the linear classifier, a more sophisticated approach might be necessary -- see for example Zemel, Dayan, and Pouget, 1998. The authors might also want to check out closely related work by Treue et al. (Nature Neuroscience 2000) and Watamaniuk and Duchon (1992).

We thank the Reviewer for the suggestion and agree that it is useful to incorporate additional decoding analysis that can better link physiology results to psychophysics. The decoding analysis we conducted was motivated by the framework proposed by Zemel, Dayan, and Pouget (1998), and also similar to the idea briefly mentioned in the Discussion of Treue et al. (2000). We have added the decoding analysis to this paper on pages 25-32.  

What do we learn from the normalization model? Its formulation is mostly a restatement of the results - that the faster and slower speeds differentially affect the combined response. This hypothesis is stated quantitatively in equation 8, which seems to provide a perfectly adequate account of the data. The normalization model in equation 10 is effectively the same hypothesis, with the mean population response interposed - it's not clear how much the actual tuning curve in Figure 10A even matters, since the main effect of the model is to flatten it out by averaging the functions in Figure 10B. Although the fit to the data is reasonable, the model uses 4 parameters to fit 5 data points and is likely underconstrained; the parameters other than alpha should at least be reported, as it would seem that sigma is actually the most important one. And I think it would help to examine how robust the statistical results are to different assumptions about the normalization pool.

In the linear weighted summation model (LWS) model (Eq. 8), the weights Ws and Wf are free parameters. We think the value of the normalization model (Eq. 9) is that it provides an explanation of what determines the response weights. We agree with the Reviewer that using the normalization model (Eq. 9) with 4 parameters to fit 5 data points of the tuning curves to bispeed stimuli of individual neurons is under-constrained. We, therefore, removed the section using the normalization model to fit overlapping stimuli moving in the same direction at different speeds.

A better way to constrain the normalization model is to use the full direction-tuning curves of MT neurons in response to two stimulus components moving in different directions at different speeds, as shown in Figure 8. We now use the normalization model (Eq. 9) to fit this data set (also suggested by Reviewer 1), in addition to the LWS model. We now report the median values of the model parameters of the normalization model, including the exponent n, sigma, alpha, and the constant c. We also compared the normalization model fit with the linear summation (LWS) model. We discuss the limitations of our data set and what needs to be done in future studies. The revisions are on page 20, lines 434-467 in the Results, and pages 34-35, lines 818-829 in Discussion.

Reviewer #3 (Public Review):

Summary:

This study concerns how macaque visual cortical area MT represents stimuli composed of more than one speed of motion.

Strengths:

The study is valuable because little is known about how the visual pathway segments and preserves information about multiple stimuli. The study presents compelling evidence that (on average) MT neurons represent the average of the two speeds, with a bias that accentuates the faster of the two speeds. An additional strength of the study is the inclusion of perceptual reports from both humans and one monkey participant performing a task in which they judged whether the stimuli involved one vs two different speeds. Ultimately, this study raises intriguing questions about how exactly the response patterns in visual cortical area MT might preserve information about each speed, since such information could potentially be lost in an average response as described here, depending on assumptions about how MT activity is evaluated by other visual areas.

Weaknesses:

My main concern is that the authors are missing an opportunity to make clear that the divisive normalization, while commonly used to describe neural response patterns in visual areas (and which fits the data here), fails on the theoretical front as an explanation for how information about multiple stimuli can be preserved. Thus, there is a bit of a disconnect between the goal of the paper - how does MT represent multiple stimuli? - and the results: mostly averaging responses which, while consistent with divisive normalization, would seem to correspond to the perception of a single intermediate speed. This is in contrast to the psychophysical results which show that subjects can at least distinguish one from two speeds. The paper would be strengthened by grappling with this conundrum in a head-on manner.

We thank the Reviewer for the constructive comments. We agree with the Reviewer that it is important to connect the encoding of multiple speeds with the perception. The Reviewer also raised an important question regarding whether multiple speeds can be extracted from population neural responses, given the encoding rules characterized in this study.

It is a hard problem to extract multiple stimulus values from the population neural response. Inspired by the theoretical framework proposed by Zemel et al. (1998), we conducted a detailed decoding study to extract motion speed(s) from MT population responses. We used the decoded speed(s) to perform a discrimination task similar to our psychophysics task and compared the decoder's performance with perception. We found that, at X4 speed difference, we could decode two speeds based on MT response, and the decoder's performance was similar to that of perception. However, at X2 speed difference, except at the slowest speeds of 1.25 and 2.5 deg/s, the decoder cannot extract two speeds and cannot differentiate between a bi-speed stimulus and a single log-mean speed stimulus. We have added the decoding analysis to this paper on pages 25-32. We also discuss the implications and limitations of these results (pages 35-36, lines 852-884).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Classifier:

One question I have is how the classifier's performance scales with the number of neurons used in the analysis. Here that number is set to the number that was recorded, but it is a free parameter in this analysis. Why does the arbitrary choice of 100 neurons match the animals' performance?

We apologize for the unclearness of this point. The decoding using the classifier was based on the neural responses of 100 recorded MT neurons in our data set. The number of 100 neurons was not a free parameter. We need to reconstruct the population neural response based on the responses of the recorded neurons and their preferred speeds (red and black dots in Figure 9A-E).  

We spline-fitted the reconstructed population neural responses (red and black curves in Figure 9-E). One way to change the number of neurons used for the decoding is to resample N points along the spline-fitted population responses, using N as a free parameter. However, we think it is better to conduct decoding based on the responses from the recorded neurons rather than based on interpolated responses. We now clarify on page 22, lines 520-522, that we based on the responses of the 100 recorded neurons in our dataset to do the classification (decoding).

Normalization Model:

Although the model is phenomenological, a schematic circuit diagram could help the reader understand how this could work (I think this is worthwhile even though the data cannot distinguish among different implementations of divisive normalization).

Thanks for this suggestion. We agree that a circuit diagram would help the readers understand how the model works. However, as the Reviewer pointed out, our data cannot distinguish between different implementations of the model. For example, divisive normalization can occur on the inputs to MT neurons or on MT neurons themselves. The circuit mechanism of weighting the component responses is not clear either. A schematic circuit diagram then mainly serves to recapitulate the normalization model in Equation 9. We, therefore, choose not to add a schematic circuit diagram at this time. We are interested in developing a circuit model to account for how visual neurons represent multiple stimuli in future studies.

Another suggestion is that the time courses could be used to constrain the model; the fact that it takes a while after the onset of the slow-speed response for averaging to reveal itself suggests the presence of inertia/hysteresis in the circuit).

We agree that the time course of MT responses could be used to constrain the model. This is also why we think it is important to document the time course in this paper. We now state in the Results, page 17, lines 354-357:

“At slow speeds, the very early faster-speed bias suggests a likely role of feedforward inputs to MT on the faster-speed bias. The slightly delayed reduction (normalization) in the bispeed response relative to the stronger component response also helps constrain the circuit model for divisive normalization.”

Two-Direction Experiment:

Applying the normalization model to this dataset could help determine its generality.

This is a good point. We now apply the normalization model (Eq. 9) to fit this data set with the full direction tuning curves in response to two stimuli moving in different directions at different speeds. Please also see the response to Reviewer 2 about the normalization model fit.

The results of the normalization model fit are now described on page 20 and Figure 8A, B, D.

Reviewer #2 (Recommendations For The Authors):

In terms of impact, I would say that the presentation is geared largely toward people who go to VSS. To broaden the appeal, the authors might consider a more general formulation of the four hypotheses stated at the bottom of page 3. These are prominent ideas in systems neuroscience - population encoding, Bayesian inference, etc.

We thank the Reviewer for the suggestion. We have revised the Introduction accordingly on pages 3-4, lines 43-69. Please also see the response to Reviewer 3 about the Introduction.

Figure 5: It might be helpful to show the predictions for different hypotheses. If the response to the transparent stimulus is equal to that of the faster stimulus, you will have a line with slope 1. If it is equal to the response to the slow stimulus, all points will lie on the x-axis. In between you get lines with slopes less than 1.

In Figures 5F1 and 5F2, we show dotted lines indicating faster-all (i.e., faster-componenttake-all), response averaging, and slower-all (i.e., slower-component-take-all) on the X-axis. We show those labels in between Figs. 5F1 and F2.

Figure 6: The analysis is not motivated by any particular question, and the results are presented without any quantitation. This section could be better motivated or else removed.

We now better motivate the section about the response time course on page 16, lines 336 – 339: “The temporal dynamics of the response bias toward the faster component may provide a useful constraint on the neural model that accounts for this phenomenon. We therefore examined the timecourse of MT response to the bi-speed stimuli. We asked whether the faster-speed bias occurred early in the neuronal response or developed gradually.”

On page 17, lines 354-357, we also state that “At slow speeds, the very early faster-speed bias suggests a likely role of feedforward inputs to MT on the faster-speed bias. The slightly delayed reduction (normalization) in the bi-speed response relative to the stronger component response also helps constrain the circuit model for divisive normalization.”

Equation (9): There appears to be an "S" missing in the denominator.

We double-checked and did not see a missing "S" in Equation 9, on page 20.  

Reviewer #3 (Recommendations For The Authors):

This is an impressive study, with the chief strengths being the computational/theoretical motivation and analyses and the inclusion of psychophysics together with primate neurophysiology. The manuscript is well-written and the figures are clear and convincing (with a couple of suggestions detailed below).

We thank the Reviewer for the comments.

Specific suggestions:

(1) Intro para 3

"It is conceivable that the responses of MT neurons elicited by two motion speeds may follow one of the following rules: (1) averaging the responses elicited by the individual speed components; (2) bias toward the speed component that elicits a stronger response, i.e. "soft-max operation" (Riesenhuber and Poggio, 1999); (3) bias toward the slower speed component, which may better represent the more probable slower speeds in nature scenes (Weiss et al., 2002); (4) bias toward the faster speed component, which may benefit the segmentation of a faster-moving stimulus from a slower background."

This would be a good place to point out which of these options is likely to preserve vs. lose information and how.

It seems to me that only #2 is clearly information-preserving, assuming that there are neurons with a variety of different speed preferences such that different neurons will exhibit different "winners". #1 would predict subjects would perceive only an intermediate speed, whereas #3 would predict perceiving only/primarily the slower speed and #4 would predict only/primarily perceiving the faster speed.

The difference between "only" and "primarily" would depend on whether the biases are complete or only partial. I acknowledge that the behavioral task in the study is not a "report all perceived speeds" task, but rather a 1 vs 2 speeds task, so the behavioral assay is not a direct assessment of the question I'm raising here, but I think it should still be possible to write about the perceptual implications of these different possibilities for encoding in an informative way.

Thanks for the suggestions. We have revised this paragraph in the Introduction on pages 3 – 4, lines 43 – 69.

(2) Analysis clarifications

The section "Relationship between the responses to bi-speed stimuli and constituent stimulus components" could use some clarification/rearrangement/polish. I had to read it several times. Possibly, rearrangement, simplification/explanation of nomenclature, and building up from a simpler to a more complex case would help. If I understand correctly, the outcome of the analysis is to obtain a weight value for every combination of slow and fast speeds used. The R's in equation 5 are measured responses, observed on the single stimulus and combined stimulus trials. It was not clear to me if the R's reflect average responses or individual trial responses; this should be clarified. Ws = 1- wf so in essence only 1 weight is computed for each combination. Then, in the subsequent sections of the manuscript, the authors explore whether the weight computed for each stimulus combination is the same or does it vary across conditions. If I have this right, then walking through these steps will aid the reader.

The Reviewer is correct. We now walk through these steps and better state the rationale for this approach. The R's in Equation 5 are trial-averaged responses, not trial-by-trial responses.

We have clarified these points on page 13.

To take a particular example, the sentence "Using this approach to estimate the response weights for individual neurons can be inaccurate because, at each speed pair, the weights are determined only by three data points" struck me as a rather backdoor way to get at the question. Is the estimate noisy? Or does the weighting vary systematically across speeds? I think the authors are arguing the latter; if so, it would be valuable to say so.

We wanted to estimate the weighting for each speed pair and determine whether the weights change with the stimulus speeds. Indeed, we found that the weights change systematically across speed pairs. The issue was not because the estimate was noisy (see below in response to the second paragraph for point 3.  

We have clarified this point in the text, on page 13, lines 273 – 280: “Our goal was to estimate the weights for each speed pair and determine whether the weights change with the stimulus speeds. In our main data set, the two speed components moved in the same direction. To determine the weights of 𝑤 and w_f for each neuron at each speed pair, we have three data points R, R_s, and R_f, which are trial-averaged responses. Since it is not possible to solve for both variables, 𝑤 and w_f, from a single equation (Eq. 5) with three data values, we introduced an additional constraint: 𝑤 + w_f =1. While this constraint may not yield the exact weights that would be obtained with a fully determined system, it nevertheless allows us to characterize how the relative weights vary with stimulus speed.”

(3) Figure 5

Related to the previous point, Figures 5A-E are subject to a possible confound. When plotting x vs y values, it is critical that the x and y not depend trivially on the same value. Here, the plots are R-Rs and Rf-Rs. Rs, therefore, is contained in both the x and y values. Assume, for the sake of argument, that R and Rf are constants, whereas Rs is drawn from a distribution of random noise. When Rs, by chance, has an extreme negative value, R-Rs and Rf-Rs will be large positive values. The solution to this artificial confound is to split the trials that generate Rs into two halves and subtract one half from R and the other half from Rf. Then, the same noisy draw will not be contributing to both x and y. The above is what is needed if the authors feel strongly about including this analysis.

The Reviewer is correct that subtracting a common term (Rs) would introduce a correlation between (R-Rs) and (Rf-Rs) (Reviewer 2 also raised this point). R's in Equations 5, 6, 7 (and Figure 5A-E) are trial-averaged responses. So, we cannot address the issue by dividing R’s into two halves. Our results showed that the regression slope (W_f) changed from near 1 to about 0.5 as the stimulus speeds increased, and the correlation coefficient between (R – Rs) and (R_f – Rs) was high at slow stimulus speeds. To determine whether these results can be explained by the confounding factor of subtracting a common term Rs, rather than by the pattern of R in representing two speeds, we did an additional analysis. We acknowledged the issue and described the new analysis on page 13, lines 303 – 326:

“Our results showed that the bi-speed response showed a strong bias toward the faster component when the speeds were slow and changed progressively from a scheme of ‘fastercomponent-take-all’ to ‘response-averaging’ as the speeds of the two stimulus components increased (Fig. 5F1). We found similar results when the speed separation between the stimulus components was small (×2), although the bias toward the faster component at low stimulus speeds was not as strong as x4 speed separation (Fig. 5A2-F2 and Table 1).  

In the regression between (𝑅 – 𝑅_s) and (𝑅_f – 𝑅_s), 𝑅_s was a common term and therefore could artificially introduce correlations. We wanted to determine whether our estimates of the regression slope (𝑤_f) and the coefficient of determination (𝑅²) can be explained by this confounding factor. At each speed pair and for each neuron from the data sample of the 100 neurons shown in Figure 5, we simulated the response to the bi-speed stimuli (𝑅 _e) as a randomly weighted sum of 𝑅_f and 𝑅_s of the same neuron.

𝑅_e = 𝑎𝑅_f + (1 − 𝑎)𝑅_s,

in which 𝑎 was a randomly generated weight (between 0 and 1) for 𝑅_f, and the weights for 𝑅_f and 𝑅_s summed to one. We then calculated the regression slope and the correlation coefficient between the simulated 𝑅_e - 𝑅_s and 𝑅_f - 𝑅_s across the 100 neurons. We repeated the process 1000 times and obtained the mean and 95% confidence interval (CI) of the regression slope and the 𝑅². The mean slope based on the simulated responses was 0.5 across all speed pairs. The estimated slope (𝑤_f) based on the data was significantly greater than the simulated slope at slow speeds of 1.25/5, 2.5/10 (Fig. 5F1), and 1.25/2.5, 2.5/5, and 5/10 degrees/s (Fig. 5F2) (bootstrap test, see p values in Table 1). The estimated 𝑅² based on the data was also significantly higher than the simulated 𝑅² for most of the speed pairs (Table 1). These results suggest that the faster-speed bias at the slow stimulus speeds and the consistent response weights across the neuron population at each speed pair are not analysis artifacts.”

However, I don't see why the analysis is needed at all. Can't Figure 5F be computed on its own? Rather than computing weights from the slopes in 5A-E, just compute the weights from each combination of stimulus conditions for each neuron, subject to the constraint ws=1-wf. I think this would be simpler to follow, not subject to the noise confound described in the previous point, and likely would make writing about the analysis easier.

We initially tried the suggested approach to determine the weights of the individual neurons. The weights from each speed combination for each neuron are calculated by:  𝑤_s = , 𝑤_f , and 𝑤_s and 𝑤_f sum to 1. 𝑅, 𝑅_f and  𝑅_s are the responses to the same motion direction. Using this approach to estimate response weights for individual neurons can be unreliable, particularly when 𝑅_f and 𝑅_s are similar. This situation often arises when the two speeds fall on opposite sides of the neuron's preferred speed, resulting in a small denominator (𝑅_f - 𝑅_s) and, consequently, an artificially inflated weight estimate. We therefore used an alternative approach. We estimated the response weights for the neuronal population at each speed pair (𝑅_f - 𝑅_s) using linear regression of (𝑅 - 𝑅_s) against (𝑅_f - 𝑅_s). The slope is the weight for the faster component for the population. This approach overcame the difficulty of determining the response weights for single neurons.

Nevertheless, if the data provide better constraints, it is possible to estimate the response weights for each speed pair for individual neurons. For example, we can calculate the weights for single neurons by using stimuli that move in different directions at two speeds. By characterizing the full direction tuning curves for R, R_f, and Rs, we have sufficient data to constrain the response weights for single neurons, as we did for the speed pair of 2.5 and 10º/s in Figure 8. In future studies, we can use this approach to measure the response weights for single neurons at different speed pairs and average the weights across the neuron population.  

We explain these considerations in the Results (pages 13–14, lines 265-326) and Discussion (pages 34-35, lines 818-829).

(4) Figure 7

Bidirectional analysis. It would be helpful to have a bit more explanation for why this analysis is not subject to the ws=1-wf constraint. In Figure 7B, a line could be added to show what ws + wf =1 would look like (i.e. a line with slope -1 going from (0,1) to (1,0); it looks like these weights are a little outside that line but there is still a negative trend suggesting competition.

For the data set when visual stimuli move in the same direction at different speeds, we included a constraint that W_s and W_f sum to 1. This is because one cannot solve two independent variables (Ws and Wf) using one equation R = W_s · R_s + W_f R_f, with three data values (R, Rs, Rf).

In the dataset using bi-directional stimuli (now Fig. 8), we can use the full direction tuning curves to constrain the linear weighted (LWS) summation model and the normalization model. So, we did not need to impose the additional constraint that Ws and Wf sum to one, which is more general. We now clarify this in the text, on page 19, lines 421-423.

As suggested, we added a line showing Ws + Wf = 1 for the LWS model fit (Fig. 8C) and the normalization model fit (Fig. 8D) (also see page 21, lines 482-484). Although 𝑤 and 𝑤 are not constrained to sum to one in the model fits, the fitted weights are roughly aligned with the dashed lines of Ws + Wf = 1.

(5) Attention task

General wording suggestions - a caution against using "attention" as a causal/mechanistic explanation as opposed to a hypothesized cognitive state. For example, "We asked whether the faster-speed bias was due to bottom-attention being drawn toward the faster stimulus component". This could be worded more conservatively as whether the bias is "still present if attention is directed elsewhere" - i.e. a description of the experimental manipulation.

We intended to test the hypothesis of whether the faster-speed bias can be explained by attention automatically drawn to the faster component and therefore enhance the contribution of the faster component to the bi-speed response. We now state it as a possible explanation to be tested. We changed the subtitle of this section to be more conservative: “Faster-speed bias still present when attention was directed away from the RFs”, on page 18, line 363.

We also modified the text on page 18, lines 364-367: “One possible explanation for the faster-speed bias may be that bottom-up attention is drawn toward the faster stimulus component, enhancing the response to the faster component. To address this question, we asked whether the faster-speed bias was still present if attention was directed away from the RFs.”

Relatedly, in the Discussion, the section on "Neural mechanisms", the sentence "The faster-speed bias was not due to an attentional modulation" should be rephrased as something like 'the bias survived or was still present despite an attentional modulation requiring the monkey to attend elsewhere'.

Our motivation for doing the attention-away experiment was to determine whether a bottom-up attentional modulation can explain the faster-speed bias. We now describe the results as suggested by the Reviewer. But we’d also like to interpret the implications of the results. In Discussion, page 34, lines 789-790, we now state: “We found that the faster-speed bias was still present when attention was directed away from the RFs, suggesting that the faster-speed bias cannot be explained by an attentional modulation.”  

(6) "A model that accounts for the neuronal responses to bi-speed stimuli". This section opens with: "We showed that the neuronal response in MT to a bi-speed stimulus can be described by a weighted sum of the neuron's responses to the individual speed components". "Weighted average" would be more appropriate here, given that ws = 1-wf.

As mentioned above, the added constraint of Ws+Wf = 1 was only a practical solution for determining the weights for the data set using visual stimuli moving in the same direction. More generally, Ws and Wf do not need to sum to one. As such, we prefer the wording of weighted sum.

(7) "As we have shown previously using visual stimuli moving transparently in different directions, a classifier's performance of discriminating a bi-directional stimulus from a singledirection stimulus is worse when the encoding rule is response-averaging than biased toward one of the stimulus components" - this is important! Can this be worked into the Introduction?

Yes, we now also mention this point in the Introduction regarding response averaging on page 4, lines 54-57: “While decoding two stimuli from a unimodal response is theoretically possible (Zemel et al., 1998; Treue et al., 2000), response averaging may result in poorer segmentation compared to encoding schemes that emphasize individual components, as demonstrated in neural coding of overlapping motion directions (Xiao and Huang, 2015).” Also, please see the response to point 1 above.

(8) Minor, but worth catching now - is the use of initials for human participants consistent with best practices approved at your institution?

Thanks for checking. The letters are not the initials of the human subjects. They are coded characters. We have clarified it in the legend of Figure 1, on page 7, line 168.

Author Response

Reviewer #1 (Public Review):

Summary:

In this paper, the effects of two sensory stimuli (visual and somatosensory) on fMRI responsiveness during absence seizures were investigated in GEARS rats with concurrent EEG recordings. SPM analysis of fMRI showed a significant reduction in whole-brain responsiveness during the ictal period compared to the interictal period under both stimuli, and this phenomenon was replicated in a structurally constrained whole-brain computational model of rat brains.

The conclusion of this paper is that whole-brain responsiveness to both sensory stimuli is inhibited and spatially impeded during seizures.

I also suggest the manuscript should be written in a way that is more accessible to readers who are less familiar with animal experiments. In addition, the implementation and interpretation of brain simulations need to be more careful and clear.

Several sections of the manuscript were clarified and simplified to be more accessible. Also, implementation and interpretations of brain simulations were modified to be more precise.

Strengths:

1) ZTE imaging sequence was selected over traditional EPI sequence as the optimal way to perform fMRI experiments during absence seizures.

2) A detailed classification of stimulation periods is achieved based on the relative position in time of the stimulation period with respect to the brain state.

3) A whole-brain model embedded with a realistic rat connectome is simulated on the TVB platform to replicate fMRI observations.

We thank the reviewer for indicating the strengths of our manuscript.

Weaknesses:

1) The analysis in this paper does not directly answer the scientific question posed by the authors, which is to explore the mechanisms of the reduced brain responsiveness to external stimuli during absence seizures (in terms of altered information processing), but merely characterizes the spatial involvement of such reduced responsiveness. The same holds for the use of mean-field modeling, which merely reproduces experimental results without explaining them mechanistically as what the authors have claimed at the head of the paper.

We agree with the reviewer that the manuscript does not answer specifically about the mechanisms of reduced brain responsiveness. The main scientific question addressed in the manuscript was to compare whole-brain responsiveness of stimulus between ictal and interictal states. The sentence that can lead to misinterpretations in the manuscript abstract: “The mechanism underlying the reduced responsiveness to external stimulus remains unknown.” was therefore modified to the following “The whole-brain spatial and temporal characteristics of reduced responsiveness to external stimulus remains unknown”.

2) The implementations of brain simulations need to be more specific.

Contribution:

The contribution of this paper is performing fMRI experiments under a rare condition that could provide fresh knowledge in the imaging field regarding the brain's responsiveness to environmental stimuli during absence seizures.

Reviewer #2 (Public Review):

Summary:

This study examined the possible effect of spike-wave discharges (SWDs) on the response to visual or somatosensory stimulation using fMRI and EEG. This is a significant topic because SWDs often are called seizures and because there is non-responsiveness at this time, it would be logical that responses to sensory stimulation are reduced. On the other hand, in rodents with SWDs, sensory stimulation (a noise, for example) often terminates the SWD/seizure.

In humans, these periods of SWDs are due to thalamocortical oscillations. A certain percentage of the normal population can have SWDs in response to photic stimulation at specific frequencies. Other individuals develop SWDs without stimulation. They disrupt consciousness. Individuals have an absent look, or "absence", which is called absence epilepsy.

The authors use a rat model to study the responses to stimulation of the visual or somatosensory systems during and in between SWDs. They report that the response to stimulation is reduced during the SWDs. While some data show this nicely, the authors also report on lines 396-8 "When comparing statistical responses between both states, significant changes (p<0.05, cluster-) were noticed in somatosensory auditory frontal..., with these regions being less activated in interictal state (see also Figure 4). That statement is at odds with their conclusion.

We thank the reviewer for noting this discrepancy. The statement should have been written vice versa and it has been corrected as: “When comparing statistical responses between both states, significant changes (p<0.05, cluster-level corrected) were noticed in the somatosensory, auditory and frontal cortices: these regions were less activated in ictal than in interictal state (see also Figure 4).”

They also conclude that stimulation slows the pathways activated by the stimulus. I do not see any data proving this. It would require repeated assessments of the pathways in time.

We agree with the reviewer that there are no data showing slowing of the pathways in response to stimulus. However, we are a bit confused about this comment, as to what part in conclusion section it refers to. We did not intentionally claim that stimulation slows the activated pathways in the manuscript.

The authors also study the hemodynamic response function (HRF) and it is not clear what conclusions can be made from the data.

Hemodynamic response functions were studied for two reasons:

• To account for possible change in HRF during the detection of activated regions. Indeed, a physiological change in HRF can mask the detection of an activation when the software uses a standard HRF to convolve the design matrix (David et al. 2008).

• To characterize the shape and polarity of fMRI activations in brain regions that we noticed to be differently activated between ictal and interictal states and evaluate whether alteration in activation was associated to alteration in hemodynamic.

The observed HRF decreases (rather than increases) in the cortex when stimulation was applied during SWD, was discussed in section 4.4., where we speculated that neuronal suppression caused by SWD can prevent responsiveness. In this case, the decreased HRF could either be a consequence or a cause of the observed neuronal suppression. The assumption that the HRF reduction is causal would be supported by a possible vascular steal effect from other activation regions. However, in the conclusion section we did not state this and therefore the following sentence was added to conclusions: “Moreover, the detected decreases in the cortical HRF when sensory stimulation was applied during spike-and-wave discharges, could play a role in decreased sensory perception. Further studies are required to evaluate whether this HRF change is a cause or a consequence of the reduced neuronal response”.

Finally, the authors use a model to analyze the data. This model is novel and while that is a strength, its validation is unclear. The conclusion is that the modeling supports the conclusions of the study, which is useful.

Details about the model were added.

Strengths:

Use of fMRI and EEG to study SWDs in rats.

Weaknesses:

Several aspects of the Methods and Results are unclear.

Reviewer #3 (Public Review):

Summary:

This is an interesting paper investigating fMRI changes during sensory (visual, tactile) stimulation and absence seizures in the GAERS model. The results are potentially important for the field and do suggest that sensory stimulation may not activate brain regions normally during absence seizures. However the findings are limited by substantial methodological issues that do not enable fMRI signals related to absence seizures to be fully disentangled from fMRI signals related to the sensory stimuli.

Strengths:

Investigating fMRI brain responses to sensory stimuli during absence seizures in an animal model is a novel approach with the potential to yield important insights.

The use of an awake, habituated model is a valid and potentially powerful approach.

Weaknesses:

The major difficulty with interpreting the results of this study is that the duration of the visual and auditory stimuli was 6 seconds, which is very close to the mean seizure duration per Table 1. Therefore the HRF model looking at fMRI responses to visual or auditory stimuli occurring during seizures was simultaneously weighting both seizure activity and the sensory (visual or auditory) stimuli over the same time intervals on average. The resulting maps and time courses claiming to show fMRI changes from visual or auditory stimulation during seizures will therefore in reality contain some mix of both sensory stimulation-related signals and seizure-related signals. The main claim that the sensory stimuli do not elicit the same activations during seizures as they do in the interictal period may still be true. However the attempts to localize these differences in space or time will be contaminated by the seizure-related signals.

The claims that differences were observed for example between visual cortex and superior colliculus signals with visual stim during seizures vs. interictal are unconvincing due to the above.

We understand this concern expressed by the reviewer and agree that seizure-related signals must be considered in the analysis when studying stimulation responses. Therefore, in modelling the responses in the SPM framework, we considered both stimulation and seizure-only states as regressors of interest and used seizure-only responses as nuisance regressors to account for error variance. Thereby, the effects caused by the stimulation should be, in theory, separated as much as possible from the effects caused by the seizure itself. Additionally, the cases where stimulations occurred fully inside a seizure (included in Figure 3, “...stimulation during ictal state) actually had a longer average seizure duration of 45 ± 60 s, therefore being much longer than 6s which an average duration taken from all seizures.

However, we acknowledge that there is a potential that some leftover effects from a seizure are still present, and we have noted this caution in the “Physiologic and methodologic considerations” section: “We note a caution that presented maps and time courses showing fMRI changes from visual or whisker stimulation during seizures may contain mixture of both sensory stimulation-related signals and seizure-related signals. To minimize this contamination, we considered in SPM both stimulation and seizure-only states as regressors of interest and used seizure-only responses as nuisance regressors to account for error variance. Thereby, the effects caused by the seizure itself should be separated as much as possible from the effects caused by stimulation.”

The maps shown in Figure 3 do not show clear changes in the areas claimed to be involved.

We clarified the overall appearance of Figure 3, by enlarging the selected cross sections for better anatomical differentiation and added anterior and posterior directions on all images.

Reviewer #1 (Recommendations For The Authors):

1) The implementations of brain simulations need to be more specific: How is the stimulation applied in the mean-field model in terms of its mathematical expression? The state variable of the model is the rate of neuronal firing, but how is it subsequently converted into fMRI responses? How are the statistical plots calculated? How much does this result depend on the model parameter?

Further details and explanations about the model have now been added to the manuscript. The stimulation of a specific region is simulated as an increase in the excitatory input to the specific node. In particular we use a square function for representing the stimulus (see for example panel A in Figure 6–figure supplement 1). As the referee mentions, the model describes the dynamics of the neuronal firing rates. This provides direct information about neuronal activity and responsiveness for which all the statistical analyses of the simulations shown in the paper were performed using the firing rates. For these analyses, no conversion to fMRI was needed. To build the statistical maps, an ANOVA (analysis of variance) test was used. The ANOVA test is originally designed to assess the significance of the change in the mean between two samples, and is calculated via an F-test as the ratio of the variance between and within samples. In our case it allowed us to assess the impact of the stimulation on the ongoing neuronal activity by performing a comparison of the timeseries of the firing rate with and without stimulation (this was performed independently for each state). For the results presented in this paper, the ANOVA analysis was performed using the “f_oneway” function of the scipy.stats. module in python. Regarding the dependence on the model parameter, the main results obtained in our paper are related with the responsiveness of the system under two quantitatively different types of ongoing dynamics: an asynchronous irregular activity (interictal period) and an oscillatory SWD type of dynamics (ictal period). In particular, we show how for the SWD dynamics the activity evoked by the stimulus is overshadowed by the ongoing activity which imposes a strong limitation in the response of the system and the propagation of the stimulus. In this sense, the main results of the simulations are very general, and no significant dependence on specific cellular or network parameters was observed within a physiologically relevant range or should be expected. Nevertheless, we point out that, as mentioned in the text, the key parameter that triggers the transition between the two types of dynamics is the strength of the adaptation current (in particular the strength of the spike-triggered adaptation parameter ‘b’ described in the Supplementary information), which in addition has the capacity of controlling the frequency of the oscillations. In the paper, this parameter was set such that the SWD frequency falls within the range observed in the GAERS (between 7-12Hz). We believe that further analysis around the region of transition between states, in particular from a dynamical point of view, could be of relevance for future work.

2) In the abstract, what exactly does "typical information flow in functional pathways" mean and which part of the results does this refer to?

We note that this sentence was overly complicated. By “typical information flow”, we were referring to sensory responsiveness during interictal state. Therefore, we made the following modifications to the abstract: “These results suggest that sensory processing observed during an interictal state can be hindered or even suppressed by the occurrence of an absence seizure, potentially contributing to decreased responsiveness.”

3) Figure 4 - Figure Supplement 1 performed an analysis of comparing states between 'when stimulation ended a seizure' and 'stimulation during an ictal period'. The authors should explain more clearly in the manuscript what is the reason and significance of considering the state of 'when stimulation ended a seizure'. And how is a seizure considered to be terminated by stimulation rather than ending spontaneously?

We have now added explanations to the manuscript section 2.5.3 as why this state was also of interest: “The case when stimulation ended a seizure is particularly interesting for studying the spatial and temporal aspects explaining shift from ictal, i.e. non-responsiveness state, to non-ictal, i.e. responsiveness state.” We agree that there is a possibility that seizures ended spontaneously at the same time as stimulus was applied but argue that seizures most probably end due to stimulation, based on results published previously (https://doi.org/10.1016/j.brs.2012.05.009).

4) In Section 3.1, some detailed descriptions of methods should be moved to Section 2, e.g. how the spatial and temporal SNR is obtained and the description of bad quality data. Also, I suggest the significance of selecting the optimal MRI sequence be stated earlier in the paper, as Section 3.1 cannot be expected from reading the abstract and introduction.

We moved some technical explanations of SNRs from section 3.1. to section 2.4.1. Significance of the selection of the MRI sequence is also now stated earlier in the introduction section: “For this purpose, the functionality of ZTE sequence was first piloted, and selected over traditional EPI sequence for its lower acoustic noise and reduced magnetic susceptibility artefacts. The selected MRI sequence thus appeared optimal for awake EEG-fMRI measurements.”

Some minor issues:

1) How is ROI defined in this paper? What type of atlas is used?

Anatomical ROIs were drawn based on Paxinos and Watson rat brain atlas 7th edition. Region was selected if there were statistically significant activations detected inside that region, based on activation maps. We clarified the definition of ROI as the following: “Anatomical ROIs, based on Paxinos atlas (Paxinos and Watson rat brain atlas 7th edition), were drawn on the brain areas where statistical differences were seen in activation maps.”

2) Section 4.3.2, "In addition, some responses were seen in the somatosensory cortex during the seizure state, which may be due to the fact that the linear model used did not completely remove the effect of the seizure itself" What is the reason for the authors to make such comments?

This claim was made because we saw similar trend of responses (deactivation) in F-contrast maps in the somatosensory cortex, when comparing “stimulation during ictal state” maps to "seizure map", leading us to assume that the effect of seizure was still apparent in the maps (even though “seizure only” states were used as nuisance regressors). However, as this claim is highly speculative, we have decided to delete this sentence in the manuscript.

3) Abbreviations such as SPM, HRF, CBF, etc. are not defined in the manuscript.

Definitions for these abbreviations were added.

4) Supplementary information-AdEx mean-field model, 've and vi', e and i should be subscripted.

Subscripts were added.

Reviewer #2 (Recommendations For The Authors):

Below are more detailed questions and concerns. Many questions are about the Methods, which seem to be written by a specialist. However, there are also questions about the experimental approach and conclusions.

One of the strengths of the study is the use of fMRI and EEG. However, to allow rats to be still in the magnet, isoflurane was used, and then as soon as rats recovered they were imaged. However isoflurane has effects on the brain long after the rats have appeared to wake up. Moreover, to train rats to be still, repetitive isoflurane sessions had to be used. Repetitive isoflurane should have a control of some kind, or be discussed as a limitation.

The repetitive use of isoflurane is indeed an important limiting factor that was not yet discussed in the manuscript. We have added the following sentences to the “Physiologic and methodologic considerations” section:

“As the used awake habituation and imaging protocol didn’t allow us to avoid the usage of isoflurane during the preparation steps, we cannot rule out the possible effect of using repetitive anesthesia on brain function. However, duration (~15 min) and concentration of anesthesia (~1.5%) during these steps were still moderate, whereas extended durations (1-3 h) of either single or repetitive isoflurane exposures have been used in previous studies where long-term effects on brain function have been observed (Long II et al., 2016; Stenroos et al., 2021). Moreover, there was a 5-15 min waiting period between the cessation of anesthesia and initiation of fMRI scan, to avoid the potential short-term effects of isoflurane that has been found to be most prominent during the 5 min after isoflurane cessation (Dvořáková et al., 2022).

An assumption of the study is that interictal periods are normal. However, they may not be. A control is necessary. One also wants to know how often GAERS have spontaneous spike-wave discharges (SWDs), what the authors call seizures. The reason is that the more common the SWDs, the less likely interictal periods are normal. It seems from the Methods that rats were selected if they had frequent seizures so many could be captured in a recording session. Those without frequent seizures were discarded.

A good control would be a normal rat that has spontaneous SWDs, since almost all rat strains have them, especially with age and in males (PMID: 7700522). However, whether they are frequent enough might be a problem. Alternatively, animals could be studied with rare seizures to assess the normal baseline, and compared to interictal states in GAERS.

We appreciate this concern raised by the Reviewer. Even though it would be interesting to study different strains and SWD frequency dependence, the aim of this study was to compare interictal vs ictal states in this specific animal model. We also understand that interictal periods could not necessarily model “normal” state and therefore went through the manuscript again to remove any claims referring to this.

About the mechanisms of SWDs, the authors should update their language which seems imprecise and lacks current citations (starting on line 71):

"Although the origin of absence seizures is not fully understood, current studies on rat models of absence seizures suggest that they arise from atypical excitatory-inhibitory patterns in the barrel field of the somatosensory cortex (Meeren et al. 2002; Polack et al. 2007) and lead to synchronous cortico-thalamic activity (Holmes, Brown, and Tucker 2004)."

Some of the best explanations for SWDs that I know of are from the papers of John Huguenard. His reviews are excellent. They discuss the mechanisms of thalamocortical oscillations.

We have reformatted the sentences discussing the mechanism of SWDs and included the explanations provided by manuscripts from Huguenard and McCafferty et al.: “Although the origin of absence seizures is not fully understood, current studies on rat models of absence seizures suggest that they arise from excitatory drive in the barrel field of the somatosensory cortex (Meeren et al. 2002; Polack et al. 2007, 2009, David et al., 2008) and then propagate to other structures (David et al., 2008) including thalamus, knowing to play an essential role during the ictal state (Huguenard, 2019). Notably, the thalamic subnetwork is believed to play a role in coordinating and spacing SWDs via feedforward inhibition together with burst firing patterns. These lead to the rhythms of neuronal silence and activation periods that are detected in SWD waves and spikes (McCafferty et al., 2018; Huguenard, 2019).”

The following also is not precise:

"Although seizures are initially triggered by hyperactive somatosensory cortical neurons, the majority of neuronal populations are deactivated rather than activated during the seizure, resulting in an overall decrease in neuronal activity during SWD (McCafferty et al. 2023)." What neuronal populations? Cortex? Which neurons in the cortex? Those projecting to the thalamus? What about thalamocortical relay cells? Thalamic gabaergic neurons?

Lines 85-8: "In addition, a previous fMRI study on GAERS, which measured changes in cerebral blood volume, found both deactivated and activated brain areas during seizures (David et al. 2008). Which areas and conditions led to reduced activity? Increased activity? How was it surmised?

"concurrent stimuli and therefore could contribute to the alterations in behavioral responsiveness" - This idea has been raised before by others (Logthetis, Barth). Please discuss these as the background for this study.

The particular section was modified to the following:

“Previous results on GAERS have indicated that, during an absence seizure, hyperactive electrophysiological activity in the somatosensory cortex can contribute to bilateral and regular SWD firing patterns in most parts of the cortex. These patterns propagate to different cortical areas (retrosplenial, visual, motor and secondary sensory), basal ganglia, cerebellum, substantia nigra and thalamus (David et al. 2008; Polack et al. 2007). Although SWDs are initially triggered by hyperactive somatosensory cortical neurons, neuronal firing rates, especially in majority of frontoparietal cortical and thalamocortical relay neurons, are decreased rather than increased during SWD, resulting in an overall decrease in activity in these neuronal populations (McCafferty et al. 2023). Previous fMRI studies have demonstrated blood volume or BOLD signal decreases in several cortical regions including parietal and occipital cortex, but also, quite surprisingly, increases in subcortical regions such as thalamus, medulla and pons (David et al., 2008; McCafferty et al., 2023). In line with these findings, graph-based analyses have shown an increased segregation of cortical networks from the rest of the brain (Wachsmuth et al. 2021). Altogether, alterations in these focal networks in the animal models of epilepsy impairs cognitive capabilities needed to process specific concurrent stimuli during SWD and therefore could contribute to the lack of behavioral responsiveness (Chipaux et al. 2013; Luo et al. 2011; Meeren et al. 2002; Studer et al. 2019), although partial voluntary control in certain stimulation schemes can be still present (Taylor et al., 2017).”

Please discuss the mean-field model more. What are its assumptions? What is its validation? Do other models also provide the same result?

We have now extended the discussion and explanation of the mean-field model, both in the main text and in the Supplementary information. The mean-field model is a statistical tool to estimate the mean activity of large neuronal populations, and as such its main assumptions are centered around the size of the population analyzed and the characteristic times of the neuronal dynamics under study. It has been shown that the formalism is valid for characteristic times of neuronal dynamics with a lower bond in the order of few milliseconds and with population size of in the order thousands of neurons (see El Boustani and Destexhe, Neural computation 2009; and Di Volo et al, Neural computation 2019), with both conditions satisfied in the simulations made for this work. Regarding the validation, the model has been extensively validated and used for simulating different brain states (Di Volo et al. 2009; Goldman et al. 2023), signal propagation in cortical circuits (Zerlaut et al, 2018) and to perform whole-brain simulations (Goldman et al, 2023). The standard validation of the mean-field implies its comparison with the activity obtained from the corresponding spiking neural network. For completeness we show in Author response image 1 an example of the SWD type of dynamics obtained from a spiking neural network together with the one obtained from the mean-field. This figure has been added now to the Supplementary information of the paper. Regarding the extension of the results to other models, we think that the generality of our results is an interesting point from our work. The main results obtained from our simulation are related with the responsiveness of the system during two different type of ongoing activity: in the interictal state there is a significant variation on the ongoing activity evoked by the stimulation that is propagated to other regions, while in the SWD state the evoked activity is overshadowed by the ongoing activity which imposes a strong limit to the responsiveness of the system and the propagation of the signal. In this sense, the results of the simulations are very general and should be extensible to other models. Of course, the advantage of using a model like ours is the capability of reproducing the different states, its applicability to large scale simulations, and the fact that it is built from biologically relevant single-cell models (AdEx).

Author response image 1.

Comparison of the SWD dynamics in the mean-field model and the underlying spiking-neural network of AdEx neurons. A) Raster plot (top) and mean firing rate (bottom) from an SWD type of dynamics obtained from the spiking- network simulations. The network is made of 8000 excitatory neurons and 2000 inhibitory neurons. Neurons in the network are randomly connected with probability p=0.05 for inhibitory-inhibitory and excitatory-inhibitory connections, and p=0.06 for excitatory-excitatory connections. Cellular parameters correspond to the ones used in the mean-field, with spike-triggered adaptation for excitatory neurons set to b=200pA. We show the results for excitatory (green) and inhibitory (red) neurons. B) Mean-firing rate obtained from a single mean-field model. We see that, although the amplitude of oscillations is larger in the spiking-network, the mean-field can correctly capture the general dynamics and frequency of the oscillations.

Line 11: "rats were equally divided by gender." Given n=11, does that mean 5 males and 6 females or the opposite?

Out of 11 animals, 6 were males, and 5 females. This is now mentioned in the manuscript.

What was the type of food?

Type of food was added to the manuscript (Extrudat, vitamin-fortified, irradiated > 25 kGy)

What were the electrodes?

This was provided in the manuscript. Carbon fiber filament was produced by World Precision Instruments. The tips of this filament were spread to brush-like shape to increase the contact surface above the skull.

"low noise zero echo time (ZTE) MRI sequence"- please explain for the non-specialist or provide references.

Reference added.

Lines 148-150: "The length of habituation period was selected based on pilot experiments and was sufficient for rats to be in low-stress state and produce absence seizures inside the magnet." How do the authors know the rats were in a low-stress state?

This claim was based on two factors. At the end of the habituation protocol, the motion of animals was considerably decreased according to previous study using similar restraint/habituation protocol (DOI: 10.3389/fnins.2018.00548). In this study the decreased motion is also correlated with decreased blood corticosterone levels which reduced to baseline levels (indicating low-stress state) after 4 days of habituation. Another factor is when epileptic rodents are continuously recorded for 24h, most SWDs occur during a state of passive wakefulness or drowsiness (Lannes et al. 1988, Coenen et al. 1991) . Either way, as we don’t have a way to provide direct evidence of low-stress state, we modified the sentence to the following:

“The length of habituation period was selected based on pilot experiments to provide low-motion data therefore giving rats a better chance to be in a low-stress state and thus produce absence seizures inside the magnet.”

Lines 150-2: "Respiration rate and motion were monitored during habituation sessions using a pressure pillow and video camera to estimate stress level." What were the criteria for a high stress level?

Criteria for high (or low) stress levels were based mostly on motion levels according to previous study (DOI: 10.1016/s0149-7634(05)80005-3). Still, as we didn’t measure direct measures of stress, we modified the sentence to the following:

“Pressure pillow and video camera were used to estimate physiological state, via breathing rate, and motion level, respectively.”

Lines 152-3: "During the last habituation session, EEG was measured to confirm that the rats produced a sufficient amount of absence seizures (10 or more per session)." If 10 min, the rats would basically be seizing the entire session, leading to doubt about what the interictal state was.

The length of the last habituation session was 60min and the fMRI scan 45min. Given that rats produced ~40-50 seizures during fMRI scan, on average they produced ~1 seizures/min, and one seizure lasting on average of 5-6s, giving ~45s periods for interictal states. 10 or more seizures were used as a threshold to give statistically meaningful findings based on pilot experiments.

Line 153: "Total of 2-5 fMRI experiments were conducted per rat within a 1-3-week period." What was the schedule for each animal? A table would be useful. If it varied, how do the authors know this was justified?

Please see Figure 1–figure supplement 2 for examples of habituation timelines for individual rats:

We found an error when stating 2-5 fMRI experiments, but it should be 3-5 fMRI experiments. This was corrected. We had an aim to acquire 12-14 sessions per stimulation condition and once a sufficient number of sessions were acquired, part of the animals was not used further. Two of the animals that were found to have good quality EEG and produced sufficient amounts of SWDs were kept, and briefly retrained for later second stimulation condition experiments. This was done to replace animals that needed to be excluded in the second stimulation condition due to bad quality EEG or lost implant. Extended use of some animals could theoretically bring slight variation to results but could actually be an advantage as animals were already well trained providing low-motion data.

"Before and after each habituation session, rats were given a treat of sugar water and/or chocolate cereals as positive reinforcement. " How much and what was the concentration of sugar water; chocolate cereal?

Rats were given 3 chocolate cereals and/or 1% sugar water. This was added to the manuscript now.

Line 188: "We relied on pilot calibration of the heated water to maintain the body temperature" Please explain.

Sentence was clarified:

“We relied on pilot calibration of the temperature of heated water circulating inside animal bed to maintain the normal body temperature of ~37 °C"

Line 190: "After manual tuning and matching of the transmit-receive coil, shimming and anatomical imaging" Please explain for the non-specialist.

Sentence was simplified:

“After routine preparation steps in the MRI console were done"

Lines 199-201: "Anatomical imaging was conducted with a T1-FLASH sequence (TR: 530 ms, TE: 4 ms, flip angle 196 18{degree sign}, bandwidth 39,682 kHz, matrix size 128 x 128, 51 slices, field-of-view 32 x 32 mm², resolution 0.25 x 0.25 x 0.5 mm3). fMRI was performed with a 3D ZTE sequence (TR: 0.971 ms, TE: 0 ms, flip angle 4{degree sign}, pulse length 1 µs, bandwidth 150 kHz, oversampling 4, matrix size 60 x 60 x 60, field-of-view 30 x 30 x 60 mm3 , resolution of 0.5 x 0.5 x 1 mm3 , polar under sampling factor 5.64 nr. of projections 2060 resulting to a volume acquisition time of about 2 s). A total of 1350 volumes (45 min) were acquired." Please explain for the non-specialist.

These technical parameters are provided for the sake of repeatability. Section was however clarified as the following and citation was added:

Anatomical imaging was conducted with a T1-FLASH sequence (repetition time: 530 ms, echo time: 4 ms, flip angle 18°, bandwidth 39,682 kHz, matrix size 128 x 128, 51 slices, field-of-view 32 x 32 mm², spatial resolution 0.25 x 0.25 x 0.5 mm3). fMRI was performed with a 3D ZTE sequence (repetition time: 0.971 ms, TE: 0 ms, flip angle 4°, pulse length 1 µs, bandwidth 150 kHz, oversampling 4, matrix size 60 x 60 x 60, field-of-view 30 x 30 x 60 mm3, spatial resolution of 0.5 x 0.5 x 1 mm3, polar under sampling factor 5.64, number of projections 2060 resulting to a volume acquisition time of about 2 s (look Wiesinger & Ho, 2022 for parameter explanations)). A total of 1350 volumes (45 min) were acquired.

"Visual (n=14 sessions, 5 rats) and somatosensory whisker (n=14 sessions, 4 rats)" - Please explain how multiple sessions were averaged for a single rat. Please justify the use of different numbers of sessions per rat.

All the sessions belonging to the same stimulus scheme (multiple sessions per rat) were put at the once as sessions in SPM analysis together with all the stimulus conditions belonging to these sessions. Justifications for using a different number of sessions per rat, were given above.

Lines 205-206: "For the visual stimulation, light pulses (3 Hz, 6 s total length, pulse length 166 ms) were produced by a blue led, and light was guided through two optical fibers to the front of the rat's eyes. What wavelength of blue? Why blue? Is the stimulation strong? Weak?

Wavelength was 470 nm and brightness 7065 mcd with a current of 20mA. Blue was selected as it is in the frequency range that rat can differentiate and this color has been used in previous literature ( https://doi.org/10.1016/j.neuroimage.2020.117542, https://doi.org/10.1016/j.jneumeth.2021.109287)

Line 212: "Stimulation parameters were based on previous rat stimulation fMRI studies to produce robust responses" What is a robust response? One where a lot of visual cortical voxels are activated?

Sentence was corrected as the following:

“Stimulation parameters were based on previous rat stimulation fMRI studies and chosen to activate voxels widely in visual and somatosensory pathways, correspondingly.”

Line 245: "Seizures were confirmed as SWDs if they had a typical regular pattern, had at least double the amplitude compared to baseline signal..." What was the "typical" pattern? What baseline signal was it compared to? Was the baseline measured as an amplitude? Peak to trough?

Sentence was corrected to the following:

“Seizures were confirmed as SWDs if they had a typical regular spike and wave pattern with 7-12 Hz frequency range and had at least double the amplitude compared to baseline signal. All other signals were classified as baseline i.e. signal absent of a distinctive 7-12 Hz frequency power but spread within frequencies from 1 to 90 Hz.”

"using rigid, affine, and SYN registrations" Please explain for the non-specialist.

Corrected as the following:

“using rigid, affine (linear) and SYN (non-linear) registrations”

Line 274-5: "However, there were also intermediate cases where the seizure started or ended during the stimulation block (Figure 1 - Figure Supplement 1). These intermediate cases were modeled as confounds" Why confounds? They could be very interesting because the stimulation may not be affected if timed at the end of the seizure. What was the definition of start and end? Defining the onset and end of seizures is tricky.

We agree that these cases are also highly interesting. Indeed, all the intermediate cases were also analyzed separately but not included in the manuscript (other than the case when stimulation immediately ended a seizure) as no statistical findings were found when comparing these cases to the baseline. E.g. for the case when stimulation was applied towards the end of seizure, it provided weakened responses but still stronger compared to case when stimulation was applied fully during a seizure (indicating some responsiveness after the cessation of seizure). As these intermediate cases led to results with higher variance, we considered them as confounds in the general linear model (i.e. reducing unwanted variance from the results of interests).

Definition of onset and end of seizure can be difficult in some cases. When looking at the signal itself, especially towards the end of seizure the amplitude of SWDs can get weaker and thus the shift from seizure to baseline signal can be more problematic to differentiate. However, when looking at the power spectrum the boundaries were more easily detectable. Thus, in the definitions of onsets and ends of seizure we relied on both the signal and power spectrum (stated in the manuscript).

"in the SPM analysis" Please explain for the non-specialist.

Definition of SPM together with a link to software site was added.

Line 276: "of fMRI data (see 2.5.3.) and thus explained variance that was not accounted for by the main effects of interest. " Please clarify.

Clarified as:

“Intermediate cases, where the seizure started or ended during the stimulation block (Figure 1–figure supplement 1), were considered as confounds of no-interest in the SPM analysis of fMRI data and the explained variance caused by the confounds were reduced from the main effects of interests”

Line 277: "Additionally, a contrast..." What is meant?

This chapter in 2.5.3. was modified as a whole to be more clear.

Line 278-9: "...was given to two cases: i) when stimulation ended a seizure (0-2 s between stimulation start and seizure end)..." Again, how is the seizure onset and end defined?

Look comment above.

Lines 281-2: "Stimulations that did not fully coincide with a seizure were considered as nuisance regressors in the second level analysis." What is meant by nuisance regressor?

Reference to SPM 12 manual was given for technical terms referring to analysis software.

Lines 283-8: "Motion periods were also included as multiple regressors (not convolved with a basis function) to be used as nuisance regressors. Stimulations that coincided with a motion above 0.3% of the voxel size were not considered stimulation inputs. Stimulation and seizure inputs were convolved with "3 gamma distribution basis functions" (i.e. 3rd 285 order gamma) in SPM (option: basis functions, gamma functions, order: 3), to account for temporal and dispersion variations in the hemodynamic response. The choice of 3rd order gamma was based on the expectation that time-to peak and shape of HRFs of seizure could vary across voxels (David et al. 2008)." Please explain the technical terms.

Reference for SPM 12 manual was given for technical terms referring to analysis software, and HRF was defined.

"BAMS rat connectome" - Please explain the technical terms.

Modified as:

“…connection matrix of the rat nervous system (BAMS rat connectome, Bota, Dong, and Swanson 2012).”

Results

After removing problematic animals and sessions, was there sufficient power? There probably wasn't enough to determine sex differences.

After removing problematic sessions, we found statistically significant results (multiple comparison corrected) results in both activation maps, and hemodynamic responses. To determine sex differences, there were not enough animals for statistical findings (p>0.05).

Figure 2 - I don't understand "tSNR" here. What is the point here?

B vs C. Are these different brain areas or the same but SNR was adjusted?

D. Where is FD explained? I think explaining what the parts of the figure show would be helpful.

tSNR, the temporal signal-to-noise ratio, demonstrates the behavior of noise through time. Readers who are planning to mimic the used awake fMRI protocol together with the single loop coil, might be interested on data quality aspect, and ability for the coil to capture signal from noise, as it is one of the most important factors in fMRI designs where small signal changes have to be distinguished from the background noise.

B and C illustrate the same brain area, but B was acquired with high resolution anatomical scanning (T1 FLASH), and C was acquired with low resolution ZTE scanning. We clarified the figure legend to the following:

“…spatial signal-to-noise ratios of an illustrative high resolution anatomical T1-FLASH (B), and low resolution ZTE image (C)

FD was explained in section 2.5.1. Some parts of the explanation were clarified: “Framewise displacement (FD) (Figure 2E) was calculated as follows. First, the differential of successive motion parameters (x, y, z translation, roll, pitch, yaw rotation) was calculated. Then absolute value was taken from each parameter and rotational parameters were divided by 5 mm (as estimate of the rat brain radius) to convert degrees to millimeters (Power et al. 2012). Lastly, all the parameters were summed together.”

Table 1 has no statistical comparisons.

Table 1 is purely an illustration of stimulation and seizure occurrence. There is no specific interest to compare stimulation types (in what state of seizure it occurred) as it does not provide any meaningful inferences to the study.

Statistical activation maps - it is not clear how this was done.

Creation of statistical maps are explained in section 2.5.3.

Line 384-5: "In addition, some responses were observed in the somatosensory cortex during a seizure state, probably due to incomplete nuisance removal of the effect of the seizure itself by the linear model used." I don't see why the authors would not suggest that the result is logical given that stimuli should activate the somatosensory cortex.

Sentence was modified as the following:

“In addition, responses were observed in the somatosensory cortex during a seizure state”

Fig 3 "F-contrast maps." Please explain.

Creation of statistical maps are explained in section 2.5.3.

HRF- please define. The ROI selection is unclear - it "was based on statistical differences seen in activation maps." But how were ROIs drawn? Also, why were HRFs examined at the end of seizures?

HRF was defined, and definitions of HRF and ROI were moved from results section 3.3. to method section 2.5.3.

Definition of ROI was clarified:

“Anatomical ROIs, based on Paxinos atlas (Paxinos and Watson rat brain atlas 7th edition), were drawn on the brain areas where statistical differences were seen in activation maps.”

HRFs were estimated additionally at the end of seizure as it was specifically interesting to study brain state shifts from ictal to interictal. This shift was also providing us statistically significant findings in means that brain responses differed from ictal stimulation.

Line 421: "Interestingly, the response amplitude was higher when the stimulation ended a seizure compared to when it did not" Why is this interesting?

Word “interestingly” was changed to “additionally” to avoid any inferences in the results section.

Line 427: "Notably, HRFs amplitudes were both negatively and positively signed during the ictal 427 state, depending on the brain region." Why is this notable?

Word “notably” was removed to avoid any inferences in the results section.

Please explain the legends of Figures 4 and 6 more clearly.

Figure 4, and figure 4 – figure supplement 1, legends were clarified:

“HRFs was calculated in selected ROI, belonging to visual or somatosensory area, by multiplying gamma basis functions (Figure 1–figure supplement 1, B) with their corresponding average beta values over a ROI and taking a sum of these values.”

Using the comments above as a guide, please revise the Discussion to be more precise and more clear about what was shown and what can be concluded in light of limitations. Please ensure the literature is cited where appropriate.

Some parts of the discussion and conclusion sections were modified.

Reviewer #3 (Recommendations For The Authors):

Minor comments:

Formatting: fMRI maps in Figures 3 and 5 should be more clearly labeled, indicating anterior and posterior directions on all images, and the cross sections should be enlarged to enable anatomical areas to be more clearly differentiated.

Anterior and posterior directions were added, and cross sections were enlarged.

The Methods section 2.41 and other places in the text, and Figure 2 - Figure Supplement 1 say that there was less artifact on the EEG with ZTA than with GE-EPI. However the EEG shown in Figure 2 - Figure Supplement 1 Part C shows much more artifact in the left (ZTE) trace than the right (GE-EPI) trace. This apparent contradiction should be resolved.

The figure was actually demonstrating the relative change to the signal when MRI sequences were on, and by this standard, the ZTE produced both less amplitude and frequency changes than EPI. In the example figure, the baseline fluctuations in the EEG trace in the left were higher in amplitude than in the right, and this could potentially lead to misconception of ZTE producing more noise. Figure legend was clarified to highlight relative change:

“ZTE also caused relatively less artificial noise on EEG signal, keeping both amplitude of the signal and frequencies relatively more intact, which improved live detection of absence seizures.”

Figure 2 - Supplement 1, part B horizontal axis should provide units.

Units were added.

Figure 2 - Supplement 1, legend last sentence says arrows mark the beginning of each "sequence." Is this a typo and should this instead say "each seizure"?

Should state “each fMRI sequence” which was corrected.

Line 307, Methods "to reveal brain areas where ictal stimulation provided higher amplitude response than interictal" - should this be reversed, ie weren't the authors analyzing a contrast to determine where interictal signals were higher than ictal signals?

This should be reversed, and was corrected, thank you for noting this.

Figure 6 - Figure Supplement 1, the scales are very different for many of the plots so they are hard to compare. Especially in the ictal periods (D, E, F) it is hard to see if any changes are happening during ictal stimulation similar to interictal stimulation due to very different scales. The activity related to SWD is so large that it overshadows the rest and perhaps should be subtracted out.

We point out that Figure 6 - Figure Supplement 1 reproduces with a higher level of detail the results shown of Figure 6 from the main text, where all signals are plotted in the same scale. The difference between scales used in this figure is intended, and its purpose is to show and highlight the large differences observed on the ongoing activity and the evoked response between the two states (ictal and interictal). In interictal periods the ongoing activity is characterized by fluctuations around a baseline level whose variance is highly affected by the application of the stimulus. On the contrary, ictal periods are characterized by large oscillations, with periods of high and synchronized activity followed by periods of nearly no activity, where the effect of the stimulus on the dynamics is overshadowed by the ongoing dynamics (both from local and from afferent nodes) as the referee mentions, and which imposes a strong limit to the responsiveness of the system and the propagation of the signal.

Author response:

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

eLife assessment

This valuable contribution studies factors that impact molecular exchange between dense and dilute phases of biomolecular condensates through continuum models and coarse-grained simulations. The authors provide solid evidence that interfacial resistance can cause molecules to bounce off the interface and limit mixing. Results like these can inform how experimental results in the field of biological condensates are interpreted.

We would like to sincerely thank the editors for spending time on our manuscript and for the very positive assessment of our work. We have carefully considered and addressed the reviewers’ comments in the point-by-point response below and have revised our manuscript accordingly.

Reviewer #1 (Public Review):

Summary:

In this paper by Zhang, the authors build a physical framework to probe the mechanisms that underlie the exchange of molecules between coexisting dense and dilute liquid-like phases of condensates. They first propose a continuum model, in the context of a FRAP-like experiment where the fluorescently labeled molecules inside the condensate are bleached at t=0 and the recovery of fluorescence is measured. Through this model, they identify how the key timescales of internal molecular mixing, replenishment from dilute phase, and interface transfer contribute to molecular exchange timescale. Motivated by a recent experiment reported by some of the co-authors previously (Brangwynne et al. in 2019) finding strong interfacial resistance in in-vitro protein droplets of LAF-1, they seek to understand the microscopic features contributing to the interfacial conductance (inversely proportional to the resistance). To check, they perform coarse-grained MD simulations of sticker-spacer self-associative polymers and report how conductance varies significantly even across the few explored sequences. Further, by looking at individual trajectories, they postulate that "bouncing" - i.e., molecules that approach the interface but are not successfully absorbed - is a strong contributor to this mass transfer limitation. Consistent with their predictions, sequences that have more free unbound stickers (i.e., for example through imbalance sequence sticker stoichiometries) have higher conductances and they show a simple linear scaling between the number of unbound stickers and conductance. Finally, they predict a droplet-size-dependent transition in recovery time behavior.

Strengths:

(1) This paper is well-written overall and clear to understand.

(2) By combining coarse-grained simulations, continuum modeling, and comparison to published data, the authors provide a solid picture of how their proposed framework relates to molecular exchange mechanisms that are dominated by interface resistance and LAF-1 droplets.

(3) The choice of different ways to estimate conductance from simulation and reported data are thoughtful and convincing in their near agreement (although a little discussion of why and when they differ would be merited as well).

We would like to thank the reviewer for the positive evaluation of our work. Indeed, we are grateful to the reviewer for this thoughtful, detailed, and constructive report, which has helped us strengthen the manuscript.

Weaknesses:

(1) Almost the entirety of this paper is motivated by a previously reported FRAP experiment on a particular LAF-1 droplet in vitro. There are a few major concerns I have with how the original data is used, how these results may generalize, and the lack of connection of predictions with any other experiments (published or new).

a. The mean values of cdense, cdilute, diffusivities, etc. are taken from Taylor et al. to rule in the importance of interfacial mass transfer limits. While this may be true, the values originally inferred (in the 2019 paper that this paper is strongly built off) report extremely large confidence intervals/inferred standard errors. The authors should accordingly report all their inferences with correct standardized errors or confidence intervals, which in turn, allow us to better understand these data.

Yes, agreed. We have now included the standard errors of the parameters from Taylor et al. (2019), and reported the corresponding standard errors for the timescales and interface conductance using error propagation. We have modified Fig. 1C right panel as well as the text in the figure caption:

“(Right) Expected recovery times and if the slowest recovery process was either the flux from the dilute phase or diffusion within the droplet, respectively, with and taken from Taylor et al. (2019). While the timescale associated with interface resistance is unknown, the measured recovery time is much longer than and , suggesting the recovery is limited by flux through the interface, with an interface conductance of  (Below Figure 1)”

b. The generalizability of this model is hard to gauge when all comparisons are made to a single experiment reported in a previous paper.

i. Conceptually, the model is limited to single-component sticker-spacer polymers undergoing phase separation which is already a very simplified model of condensates - for e.g., LAF1 droplets in the cell have no perceptible interfacial mass limitations, also reported in Taylor et al. 2019 - so how these mechanisms relate to living systems as opposed to specific biochemistry experiments. So the authors need to discuss the implications and limitations of their model in the living context where there are multiple species, finite-size effects, and active processes at play.

We thank the reviewer for the critical comment. To address this point, we have included a paragraph in the Discussion regarding in vivo situations:

“In this work, we focused on the exchange dynamics of in vitro single-component condensates. How is the picture modified for condensates inside cells? It has been shown that Ddx4-YFP droplets in the cell nucleus exhibit negligible interface resistance Taylor et al. (2019), which raises the question whether interface resistance is relevant to natural condensates in vivo. Future quantitative FRAP and single-molecule tracking experiments on different types of droplets in the cell will address this question. One complication is that condensates in cells are almost always multi-component, which can increase the complexity of the exchange dynamics. Interestingly, formation of multiple layers or the presence of excess molecules of one species coating the droplet is likely to increase interface resistance. A notable example is the Pickering effect, in which adsorbed particles partially cover the interface, thereby reducing the accessible area and the overall condensate surface tension, slowing down the exchange dynamics Folkmann et al. (2021). The development of theory and modeling for the exchange dynamics of multi-component condensates is currently underway. (Lines 323-334)”

ii. Second, can the authors connect their model to make predictions of the impact of perturbations to LAF-1 on exchange timescales? For example, are mutants (which change the number or positioning of "stickers") expected to show particular trends in conductances or FRAP timescales? Since LAF-1 is a relatively well-studied protein in vitro, can the authors further contrast their expectations with already published datasets that explore these perturbations, even if they don't generate new data?

Our model is intended to address interface exchange dynamics at the conceptual level. The underlying mechanism for the large interface resistance of LAF-1 droplets could be more complicated than explored in our work. To study the impact of perturbations to LAF-1 on exchange timescales likely requires substantially more sophisticated molecular dynamics simulations. We undertook an extensive search for FRAP experiments on LAF-1 droplets where the whole droplet is photobleached, but were not able to find another dataset. We would be grateful if the reviewer is aware of such data and can point us to it.

iii. A key prediction of the interface limitation model is the size-dependent crossover in FRAP dynamics. Can the authors reanalyze published data on LAF-1 (albeit of different-size droplets) to check their predictions? At the least, is the crossover radius within experimentally testable limits?

Based on our prediction, the crossover radius for LAF-1 droplet is around 70 𝜇m. We have added a sentence in the text to point this out:

“We also predict the crossover for LAF-1 droplets to be around 𝑅 = 71 𝜇m, which in principle can be tested experimentally. (Lines 285-286)”

Unfortunately, most of FRAP experiments in Taylor at al. (2019) are partial FRAP experiments, in which only part of the dense phase is photobleached. The recovery time for such experiments reflects primarily the internal mixing speed of the dense phase rather than the exchange dynamics at the interface or transport from the dilute phase.

c. The authors nicely relate the exchange timescale to various model parameters. Is LAF-1 the only protein for which the various dilute/dense concentrations/diffusivities are known? Given the large number of FRAP and other related studies, can the authors report on a few other model condensate protein systems? This will help broaden the reach of this model in the context of other previously reported data. If such data are lacking, a discussion of this would be important.

Yes, indeed, we have found numerous publications with FRAP experiments performed on whole droplets of various proteins. However, none of these have provided a complete set of parameters to allow a quantitative analysis. Part of the reason is because it is nontrivial to have an accurate measurement of the partition coefficient (cden/cdil). We have added a sentence in the Discussion to promote future quantitative experiment and analysis of condensate exchange dynamics:

“We hope that our study will motivate further experimental investigations into the anomalous exchange dynamics of LAF-1 droplets and potentially other condensates, and the mechanisms underlying interface resistance. (Lines 320-322)”

To broaden the audience for this work in the hope of stimulating such studies, we have also modified the title and abstract so that it will be more visible to the FRAP community:

“The exchange dynamics of biomolecular condensates (Line 1)”

“A hallmark of biomolecular condensates formed via liquid-liquid phase separation is that they dynamically exchange material with their surroundings, and this process can be crucial to condensate function. Intuitively, the rate of exchange can be limited by the flux from the dilute phase or by the mixing speed in the dense phase. Surprisingly, a recent experiment suggests that exchange can also be limited by the dynamics at the droplet interface, implying the existence of an “interface resistance”. Here, we first derive an analytical expression for the timescale of condensate material exchange, which clearly conveys the physical factors controlling exchange dynamics. We then utilize sticker-spacer polymer models to show that interface resistance can arise when incident molecules transiently touch the interface without entering the dense phase, i.e., the molecules “bounce” from the interface. Our work provides insight into condensate exchange dynamics, with implications for both natural and synthetic systems. (Lines 16-26)”

(2) The reported sticker-spacer simulations, while interesting, represent a very small portion of the parameter space. Can the authors - through a combination of simulation, analyses, or physical reasoning, comment on how the features of their underlying microscopic model (sequence length, implicit linker length, relative stoichiometry of A/B for a given length, overall concentration, sequence pattern properties like correlation length) connect to conductance? This will provide more compelling evidence relating their studies beyond the cursory examination of handpicked sequences. A more verbose description of some of the methods would be appreciated as well, including specifically how to (a) calculate the bond lifetime of isolated A-B pair, and (b) how equilibration/convergence of MD simulations is established.

In our simulation, the interface conductance is essentially controlled by the fraction of unbound stickers, the encounter rate of a pair of unbound stickers, the dilute- and dense-phase concentrations, and the width of the interface. As a result, weaker binding strength and/or deviation of A:B stoichiometry from 1:1 result in a higher interface conductance. A6B6 polymers with long blocks of stickers of the same type (compared to (A2B2)3 and (A3B3)2) have a lower dilute-phase concentration and thinner interface width, so lower conductance. Sequence length and implicit linker length can have more complex effects, which are beyond the scope of the current study. We have now provided an explicit expression for 𝜅 in Equation (14) and added a discussion sentence in the text:

“More generally, we find that the interface conductance of the sticker-spacer polymers is controlled by the encounter rate of a pair of unbound stickers and the availability of these stickers, which in turn depends on the sticker-sticker binding strength, the dilute- and dense-phase polymer concentrations, and the width of the interface:

where 𝓃 is the number of monomers in a polymer,  is the global stoichiometry (i.e., ), and are the fractions of unbound A/B monomers in the dilute and dense phases. (Lines 208-214)”

We have also added a few sentences in Appendix 2 to describe how we calculate the bond lifetime of an isolated A-B pair and how equilibration in simulations is established.

“Briefly, the bond lifetime of an isolated pair is obtained by simulating a bound pair of A-B stickers in a box and recording the time when they first separate by the cutoff distance of the attractive interaction nm. The mean bond lifetime 𝜏 is found by averaging results of 1000 replicates with different random seeds. (Lines 642-645)”

“To test if the system has reached equilibrium, we compare the dense- and dilute-phase concentrations derived from the first and second halves of the recorded data. The agreement indicates that the system has reached equilibrium. (Lines 586-589)”

(3) A lot of the main text repeats previously published models (continuum ones in Taylor et al. 2019 and Hubsatch et al., 2021, amongst others) and the idea of interface resistance being limiting was already explored quantitatively in Taylor 2019 (including approximate estimates of mass transfer limitations) - this is fine in context. While the authors do a good job of referring to past work in context, the main results of this paper, in my reading, are:

- a simplified physical form relating conductance timescales.

- sticker-spacer simulations probing microscopic origins.

- analysis of size-dependent FRAP scaling.

I am stating this not as a major weakness, but, rather - I would recommend summarizing and categorizing the sections to make the distinctions between previously reported work and current advances sufficiently clear.

We thank the reviewer for a clear summary of the contributions of our work. We have highlighted our main contributions in multiple places:

“Here, we first derive an analytical expression for the timescale of condensate material exchange, which clearly conveys the physical factors controlling exchange dynamics. We then utilize sticker-spacer polymer models to show that interface resistance can arise when incident molecules transiently touch the interface without entering the dense phase, i.e., the molecules “bounce” from the interface. (Lines 21-25)”

“In the following, we first derive an analytical expression for the timescale of condensate material exchange, which conveys a clear physical picture of what controls this timescale. We then utilize a “sticker-spacer” polymer model to investigate the mechanism of interface resistance. We find that a large interface resistance can occur when molecules bounce off the interface rather than being directly absorbed. We finally discuss characteristic features of the FRAP recovery pattern of droplets when the exchange dynamics is limited by different factors. (Lines 65-70)”

“Specifically, we first derived an analytical expression for the exchange rate, which conveys the clear physical picture that this rate can be limited by the flux of molecules from the dilute phase, by the speed of mixing inside the dense phase, or by the dynamics of molecules at the droplet interface. Motivated by recent FRAP measurements Taylor et al. (2019) that the exchange rate of LAF-1 droplets can be limited by interface resistance, which contradicts predictions of conventional mean-field theory, we investigated possible physical mechanisms underlying interface resistance using a “sticker-spacer” model. Specifically, we demonstrated via simulations a notable example in which incident molecules have formed all possible internal bonds, and thus bounce from the interface, giving rise to a large interface resistance. Finally, we discussed the signatures in FRAP recovery patterns of the presence of a large interface resistance. (Lines 291-300)”

Reviewer #2 (Public Review):

Summary:

In this paper, the authors have obtained an analytical expression that provides intuition about regimes of interfacial resistance that depend on droplet size. Additionally, through simulations, the authors provide microscopic insight into the arrangement of sticky and non-sticky functional groups at the interface. The authors introduce bouncing dynamics for rationalizing quantity recovery timescales.

I found several sections that felt incomplete or needed revision and additional data to support the central claim and make the paper self-contained and coherent.

We thank the reviewer for spending time on our manuscript and for the helpful critical comments.

First, the analytical theory operates with diffusion coefficients for dilute and dense phases. For the dilute phase, this is fine. For the dense phase, I have doubts that dynamics can be described as diffusive. Most likely, dynamics is highly subdiffusive due to crowded, entangled, and viscoelastic environments of densely packed interactive biomolecules. Some explanation and justification are in order here.

The reviewer is correct in noting that molecules within a condensate can move subdiffusively due to the viscoelastic nature of the condensate. However, subdiffusion only occurs at short time and small length scales, the motion of molecules becomes diffusive at longer time and larger length scales. The crossover time here is the terminal relaxation time measured to be on the order of milliseconds to seconds for typical condensates (see Alshareedah, Ibraheem, et al. "Determinants of viscoelasticity and flow activation energy in biomolecular condensates" Science Advances 10.7, 2024). We previously have also found that, for sticker-spacer polymers, this relaxation time is determined by the time it takes for a sticker to switch to a new partner (see Ronceray et al. (2022) in References), which is therefore largely determined by the bond lifetime of a sticker pair. The crossover length scale is expected to be comparable to the size of a molecule based on the theory of polymer disentanglement. Importantly, in order for the bleached droplet to recover its fluorescence, the bleached molecules must travel for a much longer time and a much larger length than the crossover time and length. It is therefore expected that the molecules move diffusively on the relevant timescale of a FRAP experiment, albeit with a diffusion coefficient that reflects crowding and entanglement on short time and length scales.

The second major issue is that I did not find a clean comparison of simulations with the derived analytical expression. Simulations test various microscopic properties on the value of k, which is important. But how do we know that it is the same quantity that appears in the expressions? Also, how can we be sure that analytical expressions can guide simulations and experiments as claimed? The authors should provide sound evidence of the predictive aspect of their derived expressions.

We thank the reviewer for raising this critical issue. We agree with the reviewer that we did not perform an explicit simulation to validate the developed theory, which leaves a gap between our theory and simulations. The main reason is because simulation of an in silico “FRAP experiment” on a 3D droplet is very computationally costly. Nevertheless, following the reviewer’s suggestion, we have now performed such a simulation in which we “bleached” a small A6B6 droplet and measured its recovery time. The good agreement between simulation and theory helps validate our overall combined computational and analytical approach. We have incorporated the new simulation and results into the manuscript. Two new sections including new figures (Figure 4 and Appendix 2 Figure 4) are added: “Direct simulation of droplet FRAP” in the main text (lines 232-261) and “Details of simulation and theory of FRAP recovery of an A6B6 droplet” in Appendix 2 (lines 665-715).

Are the plots in Figure 4 coming from experiment, theory, and simulation? I could not find any information either in the text or in the caption.

Figure 4 (now Figure 5) is from theory which uses parameters of the A6B6 system in simulation. We have added the following sentences to clarify:

“We compare the measured FRAP recovery time for the small droplet (green circle) to theoretical predictions from Equation (6) (gray) and Equations (1) - (4) (black) in Figure 5A. (Lines 255-257)”

“Figure 5. FRAP recovery patterns for large versus small droplets can be notably different for condensates with a sufficiently large interface resistance. (A) Expected relaxation time as a function of droplet radius for in silico “FRAP experiments” on the A6B6 system. The interface resistance dominates recovery times for smaller droplets, whereas dense-phase diffusion dominates recovery times for larger droplets. Green circle: FRAP recovery time obtained from direct simulation of an A6B6 droplet of radius 37 nm. Black curve: the recovery time as a function of droplet radius from a single exponential fit of the exact solution of the recovery curve from Equations (1) - (4). Gray curve: the recovery time predicted by Equation (6). Yellow, blue, and red curves: the recovery time when dense-phase, dilute-phase, and interface flux limit the exchange dynamics, i.e., the first, second, and last term in Equation (6), respectively. Parameters matched to the simulated A6B6 system in the slab geometry: (B) Time courses of fluorescence profiles for A6B6 droplets of radius  (top) and  (bottom); red is fully bleached, green is fully recovered. These concentration profiles are the numerical solutions of Equations (1) - (3) using the parameters in (A). (Below Figure 5)”

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

The goal of Knudsen-Palmer et al. was to define a biological set of rules that dictate the differential RNAi-mediated silencing of distinct target genes, motivated by facilitating the long-term development of effective RNAi-based drugs/therapeutics. To achieve this, the authors use a combination of computational modeling and RNAi function assays to reveal several criteria for effective RNAi-mediated silencing. This work provides insights into how (1) cis-regulatory elements influence the RNAi-mediated regulation of genes; (2) it is determined that genes can "recover" from RNAi-silencing signals in an animal; and 3) pUGylation occurs exclusively downstream of the dsRNA trigger sequence, suggesting 3º siRNAs are not produced. In addition, the authors show that the speed at which RNAi-silencing is triggered does not correlate with the longevity of the silencing. These insights are significant because they suggest that if we understand the rules by which RNAi pathways effectively silence genes with different transcription/processing levels then we can design more effective synthetic RNAi-based

therapeutics targeting endogenous genes. The conclusions of this study are mostly supported by the data, but there are some aspects that need to be clarified.

We thank the reviewer for their kind words and for appreciating the practical utility of our approach and discoveries. 

(1) The methods do not describe the "aged RNAi plates feeding assay" in Figure 2E. The figure legend states that "aged RNAi plates" were used to trigger weaker RNAi, but the detail explaining the experiment is insufficient. How aged is aged? If the goal was to effectively reduce the dsRNA load available to the animals, why not quantitatively titrate the dsRNA provided? Were worms previously fed on the plates, or was simply a lawn of bacteria grown until presumably the IPTG on the plate was exhausted?

We have elaborated our methods section to describe that the plates were left at 4ºC for about 4 months before adding bacteria and performing the assay, with one possible reason for the weaker knockdown being that perhaps the IPTG in the RNAi plates is less effective. However, it is worth noting that the robustness of a feeding RNAi assay can vary from culture to culture and/or batch of plates. We therefore always perform RNAi assays with wild-type animals alongside test strains to gauge the strength of the RNAi assay for a given culture and batch of plates. We called the data in Figure 2E “weak” because of the response of wild-type animals was weak as evidenced by weak twitching in levamisole. Despite this reduced effect, we observed 100% penetrance in wild-type animals, enabling us to sensitively detect the reduced responses of the mutants. 

(2) Is the data presented in Figure 2F completed using the "aged RNAi plates" to achieve the partial silencing of dpy-7 observed? Clarification of this point would be helpful.

No. The only occasion when plates were older was as in response to comment 1 above.

(3) Throughout the manuscript the authors refer to "non-dividing cells" when discussing animals' ability to recover from RNA silencing. It is not clear what the authors specifically mean with the phrase "non-dividing cells", but as this is referred to in one of their major findings, it should be clarified. Do they mean the cells are somatic cells in aged animals, thus if they are "non-dividing" the siRNA pools within the cells cannot be diluted by cell division? Based on the methods, the animals of RNAi assays were L4/Young adults that were scored over 8 days after the initial pulse of dsRNA feeding. If this is the case, wouldn't these animals be growing into gravid adults after the feeding, and thus have dividing cells as they grew?

We thank the reviewer for highlighting the need to explain this point further. Our experiment test the silencing of the unc-22 gene, which is expressed and functions in body-wall muscle cells. Most of the body wall muscles in C. elegans are developed by the L1 stage (reviewed in Krause and Liu, 2012), and they do not divide between the L4 and adult stages. Therefore, during the duration of the experiment where we delivered a pulse of dsRNA and examined responses over days, none of these cells divide. We have added a statement in the main text to explicitly say that the recovery from silencing by dsRNA that we observed cannot be explained by dilution during cell divisions.

(4) What are the typical expression levels/turnover of unc-22 and bli-1? Based on the results from the altered cis-regulatory regions of bli-1 and unc-22 in Figure 5, it seems like the transcription/turnover rates of each of these genes could also be used as a proof of principle for testing the model proposed in Figure 4. The strength of the model would be further increased if the RNAi sensitivity of unc-22 reflects differences in its transcription/turnover rates compared to bli-1.

We can get a sense of the relative abundances of unc-22 and bli-1 across development from the RNA-seq experiments that have been performed by others in the field (see below). However, these data cannot be used to infer either the production or the turnover rates. Future experiments that measure production (the combined rate of transcriptional run-on, splicing, export from the nucleus, etc.) will be required to define the production rates. Similarly, assays that detect the rate of degradation of transcripts without confounding presence from continued production will be needed to establish turnover rates. Future efforts to obtain values for these in vivo rates for multiple genes will help further test the model.

Author response image 1.

Expression data for unc-22:

Author response image 2.

Expression data for bli-1:

Reviewer #2 (Public Review):

Summary:

This manuscript by Knudsen-Palmer et al. describes and models the contribution of MUT-16 and RDE-10 in the silencing through RNAi by the Argonaute protein NRDE-3 or others. The authors show that MUT-16 and RDE-10 constitute an intersecting network that can be redundant or not depending on the gene being targeted by RNAi. In addition, the authors provide evidence that increasing dsRNA processing can compensate for NRDE-3 mutants. Overall, the authors provide convincing evidence to understand the factors involved in RNAi in C. elegans by using a genetic approach.

Major Strengths:

The author's work presents a compelling case for understanding the intricacies of RNA interference (RNAi) within the model organism Caenorhabditis elegans through a meticulous genetic approach. By harnessing genetic manipulation, they delve into the role of MUT-16 and RDE-10 in RNAi, offering a nuanced understanding of the molecular mechanisms at play in two independent case study targets (unc-22 and bli-1).

We thank the reviewer for their kind words and for appreciating our genetic analysis.

Major Weaknesses:

(1) It is unclear how the molecular mechanisms of amplification are different under the MUT-16 and RDE-10 branches of the regulatory pathway, since they are clearly distinct proteins structurally. It would be interesting to do some small-RNA-seq of products generated from unc-22 and bli-1, on wild-type conditions and some of the mutants studied (eg. mut-16, rde-10 and mut16 + rde-10). That would provide some insights into whether the products of the 2 amplifications are the same in all conditions, just changing in abundance, or whether they are distinct in sequence patterns.

As we highlight in the paper, MUT-16 and RDE-10 are indeed very different proteins. One possible hypothesis suggested by this difference is that different kinds of small RNAs are made when the underlying mechanism relies on MUT-16 versus on RDE-10. However, postulating such a difference is not necessary for explaining the data. Furthermore, since the amounts of 2º siRNAs do not have to be correlated with the strength of silencing (Figure 4E), this work raises caution against the over-reliance on small RNA sequencing for inferring gene silencing. Nevertheless, it is indeed an attractive possibility that the amounts of small RNA, their distributions along mRNA sequence, and/or the sequence biases of the accumulating small RNAs could be different when relying on MUT-16- or RDE-10-dependent mechanisms. Future work that directly examine the small RNAs that accumulate in different mutant strains after initiating RNAi can shed light on these possibilities.

(2) In the same line, Figure 5 aims to provide insights into the sequence determinants that influence the RNAi of bli-1. It is unclear whether the changes in transcript stability dictated by the 3'UTR are the sole factor governing the preference for the MUT-16 and RDE-10 branches of the regulatory pathway. In line with the mutant jam297, it might be interesting to test whether factors like codon optimality, splicing, ... of the ORF region upstream from bli-1-dsRNA can affect its sensitivity to the MUT-16 and RDE-10 branches of the regulatory pathway.

In Figure 5, we eliminated the possibility that any gene that is transcribed using the bli-1 promoter would require NRDE-3, and showed using jam297 that modifications to the 3’ cis regulatory regions of a target can alter the dependence on NRDE-3 for knockdown. We agree that future experiments that control individual aspects of bli-1, potentially one feature at a time, can reveal the separate contributions of each characteristic of the gene to the observed dependence on NRDE-3 of the wild-type bli-1 gene. However, given the many ways that the same level of transcript knockdown can be achieved in our modeling (Figure 4 and its supplemental figures) we expect that multiple characteristics could contribute to NRDE-3 dependence. 

Recommendations For The Authors:

Reviewer #1 (Recommendations For The Authors):

(1) On page 5, the authors state that "MUT-16 and RDE-10 are redundantly or additively required for silencing unc-22"; however, based on their data in Figure 1D, it seems nearly 100% silencing of unc-22 is achieved in single mut-16 or rde-10 mutants. If this is the case, wouldn't it suggest that redundancy of MUT-16 and RDE-10, and not an "additive effect" of MUT-16 and RDE-10 function? Although, as the mutator complex nucleates around MUT-16, the data in Figure 1D suggests it is possible that the presence of MUT-16 or RDE-10 is sufficient for the recruitment of one or more factors that triggers the silencing of unc-22, and thus only one of these factors is necessary.

Because we are seeing 100% silencing in wild-type, mut-16(-), or rde-10(-) animals in Figure 1D, this assay (where the silencing response is strong) does not allow us to discriminate between differing levels of silencing. The “weak” RNAi assay in Figure 2E provides the opportunity to observe differences in the contributions made by MUT-16 or RDE-10, supporting the idea that the 2º siRNAs and relative contributions to silencing can indeed be additive, explaining the complete loss of silencing only in the double mutant. While MUT-16 has been shown to be required for the recruitment of other Mutators in the germline, Mutator foci are not detectable in the soma. Given that unc-22 and bli-1 are somatic targets, we are hesitant to assume a mechanism for the production of small RNAs that requires a similar MUT-16-dependent nucleation in somatic cells. MUT-16 is clearly required for full silencing. But, if it functions similarly in the soma and the germline remains an open question. Indeed the mechanism(s) for producing small RNAs in somatic cells could be different from that used for production of small RNAs in the germline because of known differences in the use of RNA-dependent RNA polymerases (e.g. Ravikumar et al., Nucleic Acids Res. 2019). Future studies that determine the subcellular localization(s) and potential biochemical function(s) of RDE-10 and MUT-16 in somatic cells are needed to further delineate mechanisms.

(2) On page 10, "rather than one that looks a frequency" - the "a" should be "at".

We thank the reviewer and have fixed this typo. 

(3) Figure 4 is very crowded, further dividing 4A (right) and 4B into subpanels would help the readability of the figure.

We thank the reviewer for identifying these figures as being particularly crowded. These panels are presented as single units because the left and right portions of each panel are intimately connected. In Fig. 4A, the outline of mechanism deduced on the left is based on experiments at various scales shown on the right. We have now clarified this in the figure legend. In Fig. 4B, the equations on the right define and use the constants depicted on the left and the definitions below apply to both parts. We have now adjusted both figure parts to make these connections clearer. 

(4) References to the subpanels of Figure 4 in the text on page 12 are off from the figure and figure legend.

For example:

"Overall, τkd and tkd were uncorrelated..." refers to 4C when it should refer to 4D. "However, the maximal amount of 2ºsiRNAs..." refers to 4D when it should refer to 4E. "Additionally, an increase in transcription..." refers to 4E when it should refer to 4F.

"When a fixed amount of dsRNA was exposed..." refers to 4F when it should refer to 4G.

We thank the reviewer for catching these errors and we have corrected these figure references.

Reviewer #2 (Recommendations For The Authors):

I would encourage the authors to follow up on some of the more mechanistic comments made above, that would strengthen and complement the genetic part of the work presented.

We agree that additional work is needed to elucidate differences in molecular mechanisms for amplifying small RNAs in an MUT-16-dependent vs. RDE-10-dependent manner. We hope to address these extensions of our work in future manuscripts that focus on the biochemistry of these proteins and the populations of small RNAs generated using them.

I appreciate the efforts to computationally model the dynamics of the system, but I am not sure that it helps that the mathematical modelling treats both branches of the pathway as functionally equals, since they could have some mechanistic specialisation that is not yet elucidated by the current work.

Our assumption that both branches are equivalent is the most parsimonious. If we allowed for differences, even more values for the parameters of the model will agree with experimental data. The strength of the model is that despite such conservative assumptions, it agrees with experimental data. Biochemical elaborations that make the MUT-16 and RDE-10 branches qualitatively different could exist in vivo as suggested by the reviewer. Even with such qualitative differences in detail, the overall impact on gene silencing is a quantitative and additive one as demonstrated by our experiments. Future experimental work focused on biochemistry could elucidate how a Maelstrom domain-containing protein (RDE-10) and an intrinsically disordered protein (MUT-16) act differently to ultimately promote small RNA production.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

Summary:

The authors tried to identify the relationships among the gut microbiota, lipid metabolites, and the host in type 2 diabetes (T2DM) by using macaques that spontaneously develop T2DM, considered one of the best models of the human disease.

Strengths:

The authors comprehensively compared the gut microbiota and plasma fatty acids between macaques with spontaneous T2DM and control macaques and verified the results with macaques on a high-fat diet-fed mice model.

Weaknesses:

Comment 1: The observed multi-omics of the macaques can be done on humans, which weakens the impact of the conclusion of the manuscript.

We fully acknowledge the critical role of human studies in T2DM research. In our study, the spontaneous T2DM macaque model provided a unique window to address inherent challenges in human studies, including medication interference and environmental heterogeneity. Human studies have struggled to standardize confounding factors such as diet, exercise, and antibiotic use. Moreover, most human T2DM patients receive long-term glucose-lowering medications (e.g., metformin), which directly alter gut microbiota composition and function, masking disease-associated microbial signatures (Sun et al., 2018; Petakh et al., 2023). In contrast, the spontaneous T2DM macaques, untreated with glucose-lowering drugs or antibiotics under strictly controlled conditions, revealed microbiota dysbiosis driven purely by disease progression. Our work bridged the gap between rodent studies and human clinical trials, providing an important clinical reference for guiding targeted interventions, particularly microbiota modulation. We sincerely appreciate the valuable comments. We have added background to the part of the introduction, “In fact, T2DM macaques avoid medication interference and environmental heterogeneity under controlled experimental conditions, and share key pathological features with humans, such as amyloidosis of pancreatic islets, which is absent in mouse models (25, 26), suggesting that T2DM macaques are the optimal animal model for simulating human T2DM and its complications (27).” (Lines 98-103).

References:

Sun L., Xie C., Wang G., Wu Y., Wu Q., Wang X., Liu J., Deng Y., Xia J., et al. 2018) Gut microbiota and intestinal FXR mediate the clinical benefits of metformin Nat. Med 24:1919-1929 https://doi.org/10.1038/s41591-018-0222-4

Petakh P., Kamyshna I., Kamyshnyi A 2023) Effects of metformin on the gut microbiota: A systematic review Mol. metab 77:101805-101805 https://doi.org/10.1016/j.molmet.2023.101805

Comment 2: In addition, the age and sex of the control macaque group did not necessarily match those of the T2DM group, leaving the possibility for compromising the analysis.

Thank you for pointing this out. The availability of spontaneous T2DM macaques is very limited. Wang et al. (2018) identified only nine diabetic macaques among 2,000 screened, and our prior study (Jiang et al., 2022) found merely seven diabetic cases in 1,408 macaques. In this work, we obtained eight spontaneous T2DM macaques with FPG ≥ 7 mmol/L and eight heathy control macaques with FPG ≤ 6.1 mmol/L (three consecutive detections, each detection interval of one month) from a population of 1,698 captive macaques. To avoid confound factors affect the investigated macaques, all macaques were individually housed with standardized diets and environmental controls. While age and sex partially matched, controls originated from the same population to minimize confounding. The T2DM and control groups were matched for age period (5 adult and 3 elder) and had comparable mean ages (mean age of T2DM individuals = 12.88, mean age of control individuals = 11.25) (Table S1). In terms of gender matching, we compared blood metabolome data of 12 healthy adult female and 12 healthy adult male macaques from another study (Liu et al., 2023) and obtained only a small number of differential metabolites that were not associated with tryptophan (Table 1). We acknowledge this limitation and will prioritize matched controls in future studies.

Author response table 1.

List of all differential metabolites.

References:

Wang J., Xu S., Gao J., Zhang L., Zhang Z., Yang W., Li Y., Liao S., Zhou H., Liu P., et al. 2018) SILAC-based quantitative proteomic analysis of the livers of spontaneous obese and diabetic rhesus monkeys Am. J. Physiol-endoc. M 315:E29-E306 https://doi.org/10.1152/ajpendo.00016.2018

Jiang C., Pan X., Luo J., Liu X., Zhang L., Liu Y., Lei G., Hu G., Li J 2022) Alterations in microbiota and metabolites related to spontaneous diabetes and pre-diabetes in rhesus macaques Genes 13:1513 https://doi.org/10.3390/genes13091513

Liu X., Liu X.Y., Wang X.Q., Shang K., Li J.W., Lan Y., Wang J., Li J., et al. 2023). Multi-Omics Analysis Reveals Changes in Tryptophan and Cholesterol Metabolism before and after Sexual Maturation in Captive Macaques BMC Genomics 24:308. https://doi.org/10.1186/s12864-023-09404-3

Comment 3: Regarding the metabolomic analysis, the authors did not include fecal samples which are important, considering the authors' claim about the importance of gut microbiota in the pathogenesis of T2DM.

We thank the reviewer for this suggestion. This study employed untargeted metabolomics on macaque fecal samples to identify metabolites associated with spontaneously developing T2DM. To validate the metabolites identified through the untargeted metabolomic analysis, we conducted targeted medium- and long-chain fatty acid (MLCFA) metabolomics on macaque serum, and we further quantitatively examined the content of palmitic acid (PA) in mice feces, ileum, and serum. Although targeted MLCFA metabolomics was not performed on macaque fecal samples, we performed untargeted metabolomics on macaque feces and confirmed the contribution of PA in mice that underwent fecal microbiota transplantation (FMT) from T2DM macaques. We have added future expectations in the part of the discussion, “Previous studies have shown that insulin-resistant patients exhibit increased fecal monosaccharides associated with microbial carbohydrate metabolism (70). Furthermore, commensal species of Lachnospiraceae actively overproduce long-chain fatty acids during metabolic dysfunction through altered bacterial lipid metabolism. The microbe-derived fatty acids impair intestinal epithelial integrity to exacerbate metabolic dysregulation (71). Given that microbial metabolic activity causally modulates host metabolic homeostasis, the content change of PA was potentially associated with a dynamic equilibrium between host absorption and microbial metabolism. Further integrative studies on the fecal fatty acid metabolome, microbial PA metabolism, and functional pathways will be crucial for delineating causal links between dysbiosis and lipid metabolic dysfunction in T2DM.” (Lines 426-437).

Comment 4: In the mouse experiments, the control group should be given a FMT from control macaques rather than just untreated SPF mice since the fecal microbiota composition is likely very different between macaques and mice.

Thanks for your helpful suggestion. We recognized the importance of a FMT control group and supplemented mouse experiments (using the C57BL/6J strain) with FMT from control macaques (HFT group). Another group of mice without FMT was set as control. Due to the lengthy experimental period, observations were concluded at 30 days post-FMT. We compared changes in the gut microbiota before and after antibiotic treatment in mice (-14D and 0D), and tracked body weight and fasting plasma glucose (FPG) levels from day -14 to day 30. At 30 days after FMT, fecal samples from all groups were collected for 16S rRNA sequencing. Additionally, samples of T2DM microbiota transplant (TP), and control transplant (HTP) were sequenced. Finally, we integrated the 16S sequencing data from the FTPA group (palmitic acid (PA) diet and FMT from T2DM macaques) and FT group (normal diet and FMT from T2DM macaques) at day 30 for combined analysis. The results showed that the antibiotic treatment used in this study effectively depleted the gut microbiota. Following FMT, gut microbial diversity stabilized within 30 days, with similar microbial community proportions between HFT and control groups. Core functional groups of the healthy microbiota (Bacteroidota and Bacillota) stably colonized mice despite host species divergence, confirming that T2DM phenotypes originate specifically from macaque microbiota. Importantly, increased abundance of Lachnospiraceae (including genera Ruminococcus (current name: Mediterraneibacter), Coprococcus, and Clostridium) and the key species Ruminococcus gnavus (current name: Mediterraneibacter gnavus) were also observed in FT group versus HFT group on day 30, validating our original findings. We have added findings in the results, “To eliminate interference from host species divergence in gut microbiota composition, we supplemented mouse experiments using FMT from control macaques (HFT group) (Figure S4A). By day 30, the HFT group exhibited significantly lower body weight than the untreated control group (p < 0.05) (Figure S4B). Throughout the experimental period, FPG levels in both HFT and control groups remained within the normal range (< 6 mmol/L) without significant differences, indicating that transplantation of control macaque microbiota did not induce glycemic alterations (Figure S4C).” (Lines 276-283), and “Integrating 16S rRNA sequencing data from the HFT, FT, and FTPA groups showed that the antibiotic treatment effectively depleted the gut microbiota, resulting in microbial diversity decreased sharply, with the dominant phyla shifting from Bacteroidota and Bacillota to Pseudomonadota (Figure S4D-G). The HFT group restored microbial diversity within 30 days, achieving community proportions comparable to untreated controls. Core functional phyla (Bacteroidota and Bacillota) stably colonized in HFT group (Figure S4D-I). Critically, FT and FTPA groups exhibited increased Lachnospiraceae (including genera Ruminococcus (current name: Mediterraneibacter), Coprococcus, and Clostridium) compared with the HFT group on day 30. In addition, LEfSe comparison identified significant R. gnavus (current name: M. gnavus) enrichment in the FT group (LDA > 3, p < 0.01) (Figure S4J-M).” (Lines 324-334, 825-837). Specifically:

(1) Experimental design: transplant preparation and FMT from control macaques

After single cage feeding and FPG detection, fecal samples from three control macaques were collected and mixed for transplantation preparation. Then, 4 ml diluent (Berland et al., 2021) was added per gram of feces. Sodium L-ascorbic acid (5% (w/v)) and L-cysteine hydrochloride monohydrate (0.1% (w/v)) were added to all suspensions (The sterile diluent of control group was added with the same amount of reagent). The mixture was homogenized and filtered sequentially through 200, 400, and 800 μm sterile mesh screens. The filtrate was centrifuged (600 × g, 5 min), and supernatants were aliquoted (400 μL/tube) for storage at -80°C. For use, the transplant was quickly thawed in a 37℃ water bath.

Specific-pathogen-free male C57BL/6J mice aged 6 weeks were randomized into control and HFT (receiving FMT from control macaques) groups. Mice received antibiotic water (ampicillin, neomycin sulfate, and metronidazole, 1 g/L each) from days -14 to 0. All mice were maintained under standard conditions (12h light/dark, 22-25°C, 40-60% humidity) with sterile diet and twice-daily water changes. Body weight, fasting plasma glucose (FPG) were monitored, and fecal samples were collected throughout the study, with fecal 16S rRNA sequencing performed (Figure S4). The study was approved by the Ethics Committee of College of Life Sciences, Sichuan University, and conducted in accordance with the local legislation and institutional requirements.

(2) Results

Body weight monitoring revealed no significant difference between HFT and control groups before (-14D) and after (0D) antibiotic treatment. By day 30, the HFT group exhibited significantly lower body weight than the untreated control group (p < 0.05) (Figure S4B). Throughout the experimental period, FPG levels in both HFT and control groups remained within the normal range (< 6 mmol/L) without significant differences, indicating that transplantation of control macaque microbiota did not induce glycemic alterations (Figure S4C).

Shannon and Simpson indices showed a significant reduction in gut microbiota diversity after antibiotic treatment (0D) (p < 0.01) (Figure S4D,E). The intestinal microbiota of normal mice (-14D) was predominantly composed of Bacteroidota and Bacillota. After two weeks of antibiotic treatment (0D), microbial diversity decreased sharply compared to the -14D group, with the dominant phyla shifting from Bacteroidota and Bacillota to Pseudomonadota (Author response image 1A; Figure S4L). In healthy gut homeostasis, obligate anaerobes such as Bacillota and Bacteroidota maintain intestinal equilibrium. Antibiotic disruption induced dysbiosis in mice, causing substantial restructuring of fecal microbial composition. During dysbiosis, colon epithelial cells shift to anaerobic glycolysis for energy production, increasing epithelial oxygenation and driving expansion of facultative anaerobic Pseudomonadota (de Nies et al., 2023; Szajewska et al., 2024).

NMDS analysis of integrated 16S rRNA sequencing data of FTPA30D (PA diet and FMT from T2DM macaques) and FT30D (normal diet and FMT from T2DM macaques) revealed high intra-group repeatability among pre-antibiotic (-14D), post-antibiotic (0D), HFT30D, T2DM microbiota transplant (TP), and control transplant (HTP) groups. The 0D group showed maximal separation from other clusters, while the -14D, control30D, and HFT30D clustered closely together, with HFT30D nearest to control30D (Figure S4F). On the day 30, all groups showed restoration of microbiota community structure, and the composition of gut microbiota in HFT30D was basically consistent with the control30D group at all taxonomic levels (Author response image 1A-C). At the phylum level, HFT30D group showed significantly reduced relative abundance of Pseudomonadota and increased abundance of Bacteroidota, Bacillota_A, Bacillota_I, and gut barrier-enhancing Verrucomicrobiota (Author response image 1A). These findings demonstrated that FMT from control macaques effectively restored the gut microbiota of antibiotic-treated mice toward a normative state.

Author response image 1.

Composition of gut microbiota in mice. (A) Phylum level; (B) Family level; (C) Genus level.

At the phylum level, the FT30D and FTPA30D groups exhibited lower proportions of Bacteroidota/Bacillota compared to the HFT30D (Author response image 1A). Family-level analysis revealed markedly increased abundance of Lactobacillaceae and Lachnospiraceae in FTPA30D and FT30D groups relative to HFT30D, consistent with the changes in the microbiota of spontaneously T2DM macaques (Author response image 1B). Notably, while both HTP and TP groups contained Lachnospiraceae, only FT30D and FTPA30D mice demonstrated significant increase of this family, which was close to that in TP group. Although Muribaculaceae and Bacteroidaceae showed partial recovery in these groups, their relative abundances remained substantially lower than in control30D and HFT30D groups, suggesting that microbiota transplantation from T2DM macaques may reduce specific beneficial taxa while promoting expansion of conditionally pathogenic or metabolically-altered bacteria, such as Lachnospiraceae.

Further analysis of Lachnospiraceae dynamics revealed that at the genus level, most Lachnospiraceae members exhibited higher abundance in the TP group compared to the HTP group. FT30D and FTPA30D groups showed increased abundance of Ruminococcus (current name: Mediterraneibacter), Coprococcus, and Clostridium relative to HFT30D group, consistent with prior analyses (Figure S4). LEfSe comparison between FT30D and HFT30D identified significantly enriched Ruminococcus gnavus (current name: Mediterraneibacter gnavus) in FT30D recipients (LDA > 3, p < 0.01), corroborating earlier findings (Figure S4L). As a mucin-degrading microbe, R. gnavus (current name: M. gnavus) promotes insulin resistance through modulation of tryptamine/phenethylamine levels (Zhai et al., 2023) and exhibits pro-inflammatory properties (Henke et al., 2019; Paone and Cani, 2020). The absence of R. gnavus (current name: M. gnavus) enrichment in FTPA30D was potentially related to differential long-term impacts of T2DM microbiota transplantation across the 30- versus 120-day experimental timelines.

Author response image 2.

Identification of differential microbiota in mice. (A) Linear discriminant analysis Effect Size (LEfSe) analysis between pre-antibiotic (-14D) and post-antibiotic (0D) groups; (B) HFT and FTPA groups; (C) HFT and FT groups.

References:

Berland M., Cadiou J., Levenez F., Galleron N., Quinquis B., Thirion F., Gauthier F., Le ChatelierE., Plaza Oñate F., Schwintner C., et al. 2021) High engraftment capacity of frozen ready-to-use human fecal microbiota transplants assessed in germ-free mice Sci. Rep 11 https://doi.org/10.1038/s41598-021-83638-7

Szajewska H., Scott KP., Meij T de., Forslund-Startceva S.K., Knight R., Koren O., Little P., Johnston B.C., Łukasik J., Suez J., Tancredi D.J., Sanders M.E 2024) Antibiotic-perturbed microbiota and the role of probiotics Nat. Rev. Gastro. Hepat 1-18 https://doi.org/10.1038/s41575-024-01023-x

de Nies L., Kobras C.M., Stracy M 2023) Antibiotic-induced collateral damage to the microbiota and associated infections. Nat. Rev. Microbiol 21:789-804 https://doi.org/10.1038/s41579-023-00936-9

Zhai L., Xiao H., Lin C., Wong H.L.X., Lam Y.Y., Gong M., Wu G., Ning Z., Huang C., Zhang Y., et al. 2023) Gut microbiota-derived tryptamine and phenethylamine impair insulin sensitivity in metabolic syndrome and irritable bowel syndrome Nat. Commun 14 https://doi.org/10 .1038/s41467-023-40552-y

Henke M.T., Kenny D.J., Cassilly C.D., Vlamakis H., Xavier R.J., Clardy J 2019) Ruminococcusgnavus, a member of the human gut microbiome associated with Crohn's disease, produces an inflammatory polysaccharide Proc. Nat. Acad. Sci 116:12672-12677 https://doi.org/10.1073/pnas.1904099116

Paone P., Cani P.D 2020) Mucus barrier, mucins and gut microbiota: the expected slimy partners? Gut 69:2232-2243 https://doi.org/10.1136/gutjnl-2020-322260

Comment 5: Additionally, the palmitic acid-containing diets fed to mice to induce a diabetes-like condition do not mimic spontaneous T2DM in macaques.

Thanks for your helpful suggestion. We agree that the palmitic acid (PA)-containing diet alone could not fully mimic spontaneous T2DM in macaques. In our study, the PA diet was employed in mouse experiments to investigate whether gut microbiota modulates serum PA levels and mediates T2DM progression. Our critical finding revealed that microbiota was essential for enhanced PA absorption, while simply increasing dietary levels of PA did not effectively enhance intestinal uptake. The fecal microbiota transplantation (FMT) combined with PA-diet approach successfully induced prediabetic states in mice, which can be further applied to the induction of T2DM in macaques. We have added future expectations in the part of the discussion, “Our study highlights the essential roles of gut microbiota in T2DM development, which may account for the inability of prior studies to induce T2DM in macaques through high-fat diet intervention alone (28, 29). Furthermore, applying this approach to induce T2DM in macaques will enable deeper investigation into gut-microbiota-driven mechanisms underlying disease pathogenesis.” (Lines 393-398).

Reviewer #1 (Recommendations for the authors):

General comments

Comment 1: The authors used macaques in this study. The author claims that macaques may be the best animal model to investigate the relationships among gut microbiota, lipid metabolites, and the host in type 2 diabetes (T2DM). However, there have already been some studies investigating these relationships in humans (for example, doi: 10.1016/j.cmet.2022.12.013, and doi: 10.1038/s41586-023-06466-x). The authors should cite and discuss these papers.

We thank the reviewer for this suggestion. We have cited the two papers in the part of discussion, “Previous studies have shown that insulin-resistant patients exhibit increased fecal monosaccharides associated with microbial carbohydrate metabolism (70). Furthermore, commensal species of Lachnospiraceae actively overproduce long-chain fatty acids during metabolic dysfunction through altered bacterial lipid metabolism. The microbe-derived fatty acids impair intestinal epithelial integrity to exacerbate metabolic dysregulation (71).” (Lines 426-432).

Specific comments

Major:

Comment 2: (1) First of all, sex and age of the T2DM and control groups are different (Suppl Table 1). Since the size of the captive population is 1,698, the authors should be able to select the factors including the sex and age of the control group to match those of the T2DM group and they should do so.

In this work, we obtained eight spontaneous T2DM macaques with FPG ≥ 7 mmol/L and eight heathy control macaques with FPG ≤ 6.1 mmol/L (three consecutive detections, each detection interval of one month) from a population of 1,698 captive macaques. To avoid confound factors affect the investigated macaques, all macaques were individually housed with standardized diets and environmental controls. While age and sex partially matched, controls originated from the same population to minimize confounding. The T2DM and control groups were matched for age period (5 adult and 3 elder) and had comparable mean ages (mean age of T2DM individuals = 12.88, mean age of control individuals = 11.25) (Table S1). In terms of gender matching, we compared blood metabolome data of 12 healthy adult female and 12 healthy adult male macaques from another study (Liu et al., 2023) and obtained only a very small number of differential metabolites that were not associated with tryptophan (Author response table 1). We acknowledge this limitation and will prioritize matched controls in future studies.

References:

Liu X., Liu X.Y., Wang X.Q., Shang K., Li J.W., Lan Y., Wang J., Li J., et al. 2023). Multi-Omics Analysis Reveals Changes in Tryptophan and Cholesterol Metabolism before and after Sexual Maturation in Captive Macaques BMC Genomics 24:308. https://doi.org/10.1186/s12864-023-09404-3

Comment 3: (2) Are the normal ranges known for the parameters of macaques shown in Table 1? If so, the authors should include those values in Table 1. If not, the authors should show the values of average and SD or SE of all 1,698 individuals as the reference.

We thank the reviewer for this suggestion. In this study, the normal ranges of fasting plasma glucose (FPG), fasting plasma insulin (FPI), homeostasismodel assessment- insulin resistance (HOMA-IR), and glycosylated hemoglobin A1cwe (HbA1c) were referenced against human standards. According to the American Diabetes Association (ADA) for glucose metabolism status and the diagnostic criteria for diabetes, individuals with FPG ≥ 7 mmol/L were diagnosed as T2DM subjects, and individuals with FPG ≤ 6.1 mmol/L were controls. More sensitive assays show a normal fasting plasma insulin level to be under 12 μU/mL (Matsuda and DeFronzo, 1999). HOMA-IR ≥ 2.67 indicated the possibility of insulin resistance, which is used in clinical diagnosis (Lorenzo et al., 2012). HbA1c percentages higher than 6.5% were used as an auxiliary diagnostic index for diabetic macaques (Cowie et al., 2010). The normal ranges of triglycerides (TG), total cholesterol (TC), high-density lipoprotein cholesterol (HDL), and low-density lipoprotein cholesterol (LDL) were referenced against the blood lipid index of rhesus macaques (Yu et al., 2019). We have added the normal ranges of parameters to Table 1, “FPG: fasting plasma glucose (normal range: ≤ 6.1 mmol/L); FPI: fasting plasma insulin (normal range: ≤ 12 μU/mL); HOMA-IR: homeostasismodel assessment- insulin resistance (normal range: ≤ 2.67); BMI: body mass index; HbA1c: glycosylated hemoglobin A1c (normal range: < 6.5%); TG: triglycerides (normal range: 0.95±0.47 mmol/L); TC: total cholesterol (normal range: 3.06±0.98 mmol/L); HDL: high-density lipoprotein cholesterol (normal range: 1.62±0.46 mmol/L); LDL: low-density lipoprotein cholesterol (normal range: 2.47±0.98 mmol/L). (30, 31, 32, 33).”.

References:

Matsuda M., DeFronzo R.A 1999) Insulin sensitivity indices obtained from oral glucose tolerance testing: comparison with the euglycemic insulin clamp Diabetes care 22:1462-1470 https://doi.org/10.2337/diacare.22.9.1462

Lorenzo C., Hazuda H.P., Haffner S.M 2012) Insulin resistance and excess risk of diabetes in Mexican-Americans: the San Antonio Heart Study J. Clin. Endocr. Metab 97:793-799 https://doi.org/10.1210/jc.2011-2272

Cowie C.C., Rust K.F., Byrd-Holt D.D., Gregg E.W., Ford E.S., Geiss L.S., Bainbridge K.E., Fradkin J.E 2010) Prevalence of diabetes and high risk for diabetes using A1C criteria in the US population in 1988–2006 Diabetes care 33:562-568 https://doi.org/10.2337/dc09-1524

Yu W., Hao X., Yang F., Ma J., Zhao Y., Li Y., Wang J., Xu H., Chen L., Liu Q., et al. 2019) Hematological and biochemical parameters for Chinese rhesus macaque PLoS One 14:e0222338 https://doi.org/10.1371/journal.pone.0222338

Comment 4: (3) The authors measured the fasting plasma glucose (FPG) levels, but it is common to measure whole blood glucose since glucose is consumed during the processing of obtaining plasma which could compromise the results. Please explain why plasma glucose levels were measured.

The criteria for screening spontaneous T2DM macaques were guided by the American Diabetes Association (ADA) for glucose metabolism status and the diagnostic criteria for diabetes. Individuals with FPG ≥ 7 mmol/L were diagnosed as T2DM subjects, and individuals with FPG ≤ 6.1 mmol/L were controls. For the identified subjects, a total of three times of FPG tests were employed, with an interval of one month to reduce the possible error. These individuals were raised in a single cage, and blood samples were collected after an overnight fast at least 12 h. After the three test results meet the standards, venous blood was collected for FPG testing to ensure the reliability of the data to the greatest extent. We have added FPG values of three time to the Table S1.

Comment 5: (4) Since the BMI of the T2DM and control groups did not significantly differ (p>0.05, Table 1), the food intake of the two groups may not significantly differ as well. The authors should examine the food intake data. The food intake is also important in considering the relevance of feeding the PA diet in mice experiments. Were the intake of T2DM macaques including PA more than the control group?

All macaques in this study were individually housed under standardized environments with timed and measured feeding to minimize confounders. Given the non-significant BMI difference between T2DM and control groups, food intake was probably not significantly different. In this study, our findings highlight the essential roles of gut microbiota in T2DM development, and this is probable also the reason that previous studies have failed to induce T2DM in macaques because they have only used a high-fat diet (Ji et al., 2012; Tang, 2020). We agree that PA intake in T2DM macaques warrants focused investigation. Future investigations will incorporate detailed dietary monitoring including palmitic acid (PA) intake and nutrient composition to examine potential relationships between specific dietary components, metabolic parameters, and diabetes progression.

References

Ji F., Jin L., Zeng X., Zhang X., Zhang Y., Sun Y., Gao L., He H., Rao J., Liu X., et al. 2012) Comparison of gene expression between naturally occurring and diet-induced T2DM in cynomolgus monkeys Dongwuxue Yanjiu 33:79–84 https://doi.org/10.3724/SP.J.1141.2012 .01079

Tang MT. 2020) Study on the Role of Glucose and Lipid in the Establishment of Type 2 Diabetic Cynomolgus Monkey Model M.S. Thesis, Dept. Veterinary Med., South China Agricultural Univ. 2020

Comment 6: (5) It may be that the fecal microbiome of the T2DM macaques is involved in the pathogenesis of T2DM; however, it is more important how the gut microbiota compositions were obtained/established by those T2DM macaques. There was no description of when the fecal samples were collected during the course of T2DM. If it was after T2DM symptoms appeared, the authors should perform gut metagenome and also gut metabolome analyses to see the change in those parameters to try to understand how gut microbiome changes are induced leading to T2DM pathogenesis.

The spontaneous T2DM macaques untreated with glucose-lowering drugs or antibiotics, revealed microbiota dysbiosis driven purely by disease progression. After macaques met diagnostic thresholds across three FPG assessments (each detection interval of one month), we collected fresh fecal samples and stored them aseptically at -80 °C until analysis. The scarcity of spontaneous T2DM macaques precludes invasive sampling, restricting tissue collection to naturally deceased diabetic individuals, which prevented us to explicitly define the disease stage of the T2DM individuals. We recognize the scientific value of gut metagenomic and metabolomic analyses to track microbiome evolution during diabetes progression. This study explored the interaction of gut microbiota and metabolites in T2DM macaques, and future studies can continue to investigate its dynamic changes in the disease process of T2DM.

Comment 7: (6) Regarding the fatty acids, the authors only measured them in the plasma, but they also should measure in feces, since the authors focus on gut microbiota; in addition, a recent report showed fecal fatty acids, especially elaidic acid, contributed the pathogenesis of obesity and T2DM by acting on the gut epithelial cells (doi: 10.1016/j.cmet.2022.12.013). Besides, this study showed the link between a Lachnospiraceae species and fecal palmitic and elaidic acids, which the authors also focused on in this manuscript.

We thank the reviewer for this suggestion. This study employed untargeted metabolomics on macaque fecal samples to identify metabolites associated with spontaneously developing T2DM. To validate the metabolites identified through the untargeted metabolomic analysis, we conducted targeted medium- and long-chain fatty acid (MLCFA) metabolomics on macaque serum, and we further quantitatively examined the content of palmitic acid (PA) in mice feces, ileum, and serum. Although targeted MLCFA metabolomics was not performed on macaque fecal samples, we did perform untargeted metabolomics on macaque feces and confirmed the contribution of PA in mice that underwent fecal microbiota transplantation (FMT) from T2DM macaques. We have added future expectations in the part of the discussion, “Previous studies have shown that insulin-resistant individuals exhibit increased fecal monosaccharides associated with microbial carbohydrate metabolism (70). Furthermore, commensal species of Lachnospiraceae actively overproduce long-chain fatty acids during metabolic dysfunction through altered bacterial lipid metabolism. The microbe-derived fatty acids impair intestinal epithelial integrity to exacerbate metabolic dysregulation (71). Given that microbial metabolic activity causally modulates host metabolic homeostasis, the content change of PA was potentially associated with a dynamic equilibrium between host absorption and microbial metabolism. Further integrative studies on the fecal fatty acid metabolome, microbial PA metabolism, and functional pathways will be crucial for delineating causal links between dysbiosis and lipid metabolic dysfunction in T2DM.” (Lines 426-437).

Comment 8: (7) In FMT and PA diet experiments, SPF mice were used as the control group. However, the gut microbiota composition of the SPF mice is markedly different from that of macaques; the difference must be much bigger than the difference between T2DM and healthy control macaques; therefore, mice with FMT from healthy control macaques have to be used as the control group. As mentioned above (in point #4), is the feeding of mice with PA diet a relevant model reflecting the condition observed in macaques in this study?

Thanks for your helpful suggestion. We recognized the importance of a FMT control group and supplemented mouse experiments (using the C57BL/6J strain) with FMT from control macaques (HFT group). Another group of mice without FMT was set as control. Due to the lengthy experimental period, observations were concluded at 30 days post-FMT. We compared changes in the gut microbiota before and after antibiotic treatment in mice (-14D and 0D), and tracked body weight and fasting plasma glucose (FPG) levels from day -14 to day 30. At 30 days after FMT, fecal samples from all groups were collected for 16S rRNA sequencing. Additionally, samples of T2DM microbiota transplant (TP), and control transplant (HTP) were sequenced. Finally, we integrated the 16S sequencing data from the FTPA group (palmitic acid (PA) diet and FMT from T2DM macaques) and FT group (normal diet and FMT from T2DM macaques) at day 30 for combined analysis. The results showed that the antibiotic treatment used in this study effectively depleted the gut microbiota. Following FMT, gut microbial diversity stabilized within 30 days, with similar microbial community proportions between HFT and control groups. Core functional groups of the healthy microbiota (Bacteroidota and Bacillota) stably colonized mice despite host species divergence, confirming that T2DM phenotypes originate specifically from macaque microbiota. Importantly, increased abundance of Lachnospiraceae (including genera Ruminococcus (current name: Mediterraneibacter), Coprococcus, and Clostridium) and the key species Ruminococcus gnavus (current name: Mediterraneibacter gnavus) were also observed in FT group versus HFT group on day 30, validating our original findings. We have added findings in the results, “To eliminate interference from host species divergence in gut microbiota composition, we supplemented mouse experiments using FMT from control macaques (HFT group) (Figure S4A). By day 30, the HFT group exhibited significantly lower body weight than the untreated control group (p < 0.05) (Figure S4B). Throughout the experimental period, FPG levels in both HFT and control groups remained within the normal range (< 6 mmol/L) without significant differences, indicating that transplantation of control macaque microbiota did not induce glycemic alterations (Figure S4C).” (Lines 276-283), and “Integrating 16S rRNA sequencing data from the HFT, FT, and FTPA groups showed that the antibiotic treatment effectively depleted the gut microbiota, resulting in microbial diversity decreased sharply, with the dominant phyla shifting from Bacteroidota and Bacillota to Pseudomonadota (Figure S4D-G). The HFT group restored microbial diversity within 30 days, achieving community proportions comparable to untreated controls. Core functional phyla (Bacteroidota and Bacillota) stably colonized in HFT group (Figure S4D-I). Critically, FT and FTPA groups exhibited increased Lachnospiraceae (including genera Ruminococcus (current name: Mediterraneibacter), Coprococcus, and Clostridium) compared with the HFT group on day 30. In addition, LEfSe comparison identified significant R. gnavus (current name: M. gnavus) enrichment in the FT group (LDA > 3, p < 0.01) (Figure S4J-M).” (Lines 324-334, 825-837).

We agree that the PA-containing diet alone could not fully mimic spontaneous T2DM in macaques. In our study, the PA diet was employed in mouse experiments to investigate whether gut microbiota modulates serum PA levels and mediates T2DM progression. Our critical finding revealed that microbiota was essential for enhanced PA absorption, while simply increasing dietary levels of PA did not effectively enhance intestinal uptake. The FMT combined with PA-diet approach successfully induced prediabetic states in mice, which can be further applied to the induction of T2DM in macaques. We have added future expectations in the part of the discussion, “Our study highlights the essential roles of gut microbiota in T2DM development, which may account for the inability of prior studies to induce T2DM in macaques through high-fat diet intervention alone (28, 29). Furthermore, applying this approach to induce T2DM in macaques will enable deeper investigation into gut-microbiota-driven mechanisms underlying disease pathogenesis.” (Lines 393-398).

Comment 9: FPG was measured here in the mouse experiments, but there was no description of whether mice were under fasting conditions, and this should be clarified. If there are no fasting durations, this should be described in the Materials and Methods section.

As suggested, we have added description to the Materials and Methods section, “Throughout the experiment, body weight and feces were collected every month, FPG was detected every half month under fasting at least 12 h.” (Lines 619-620).

Comment 10: From the PA contents in feces, ileum, and serum in mice (Figures 5A-D), the authors concluded that the absorption of PA was significantly enhanced in the ileum leading to the increase of PA in serum. However, it could also be possible that consumption of PA by gut microbiota occurs at the same time and the authors should discuss the possibility.

We thank the reviewer for spotting this. We have added a discussion to the manuscript, “Previous studies have shown that insulin-resistant individuals exhibit increased fecal monosaccharides associated with microbial carbohydrate metabolism (70). Furthermore, commensal species of Lachnospiraceae actively overproduce long-chain fatty acids during metabolic dysfunction through altered bacterial lipid metabolism. The microbe-derived fatty acids impair intestinal epithelial integrity to exacerbate metabolic dysregulation (71). Given that microbial metabolic activity causally modulates host metabolic homeostasis, the content change of PA was potentially associated with a dynamic equilibrium between host absorption and microbial metabolism. Further integrative studies on the fecal fatty acid metabolome, microbial PA metabolism, and functional pathways will be crucial for delineating causal links between dysbiosis and lipid metabolic dysfunction in T2DM.” (Lines 426-437).

Comment 11: (8) Nomenclature and classification of bacteria has been revised by the List of Prokaryotic names with Standing in Nomenclature (LPSN) (https://lpsn.dsmz.de/) and recognized as Global Core Biodata Resource in 2023. For example, Ruminococcus gnavus is now Mediterraneibacter gnavus. Therefore, the name of microbes should be corrected accordingly; one proposal is to show the revised correct name with the previous name in parenthesis, such as "Mediterraneibacter gnavus (previously Ruminococcus gnavus)".

Thank you for pointing this out. We have corrected the name of microbe, “Ruminococcus (current name: Mediterraneibacter)”, “Ruminococcus gnavus (current name: Mediterraneibacter gnavus), and “R. gnavus (current name: M. gnavus)” (Lines 146, 313, 316-317, 336, 345, 367-368, 401, 404-405, 409, 448, 764-765)

Minor:

Comment 12:

(1) The sentence starting "A total of..." (lines 143-144) seems grammatically wrong; a word such as "represented" should be inserted after "differentially", or alternatively "differentially" should be "differential"?

(2) "medium-and" (line 220) needs a space between "medium-" and "and" to make it "medium- and".

(3) Abbreviations should be spelled out when they appear for the first time in the main text; for example, WBC, NEU, and LYM in line 237.

(4) Should FGP (line 437) be FPG?

(5) What is the definition of "prediabetes" in mice? Is this clearly defined elsewhere?

We sincerely thank the reviewer for careful reading. As suggested, we have improved the statements and revised it according to the requirements:

(1) Line 143: “A total of 21 microbes were identified as differential microbes”.

(2) Line 221: “targeted medium- and long-chain fatty acid”.

(3) Lines 238-239: “white blood cell (WBC)”, “neutrophil (NEU)”, and “lymphocyte (LYM)”.

(4) Line 472: “FPG, HbA1c and FPI were detected”.

(5) Prediabetes or impaired glucose regulation (IGR) is diagnosed when one exhibits blood glucose level higher than normal yet below the diabetic threshold, which is even more prevalent than T2DM in the population (American Diabetes, 2021). Given the higher glycemic diagnostic criteria in mice, we assessed diabetic manifestations integrating physiological and pathological evidence. Compared to control mice, those receiving FMT from T2DM macaques combined with a high-palmitic-acid diet (FTPA group) developed prediabetic characteristics by day 120. Physiological alterations included elevated fasting plasma glucose (FPG), increased fasting plasma insulin (FPI), impaired glucose tolerance, heightened insulin resistance, weight gain, and elevated serum total cholesterol (TC) and triglyceride (TG) levels. Particularly in pathological changes, hepatocytes focal necrosis with inflammatory cell infiltration was commonly observed in FTPA group, alongside decreased volume in pancreatic islets and inflammatory cell infiltration (lines 258-276).

References:

American Diabetes Association 2021) 2. Classification and diagnosis of diabetes: standards of medical care in diabetes—2021 Diabetes care 44:S15-S33 https://doi.org/10.2337/dc21-S002

Reviewer #2 (Public review):

This study analyzes the interaction among the gut microbiota, lipid metabolism, and the host in type 2 diabetes (T2DM) using rhesus macaques. The authors first identified 8 macaques with T2DM from 1698 individuals. Then, they observed in T2DM macaques: dysbiosis by 16S rRNA gene amplicon analysis and shotgun sequencing, imbalanced tryptophan metabolism and fatty acid beta oxidization in the feces by metabolome analysis, increased plasma concentration of palmitic acid by MS analysis, and sn inflammatory gene signature of blood cells by transcriptomic analysis. Finally, they transplanted feces of T2DM macaques into mice and fed them with palmitic acid and showed that those mice became diabetic through increased absorption of palmitic acid in the ileum.

Comment 1: This study clearly shows the interaction among gut microbiota, lipid metabolism, and the host in T2DM. The experiments were well designed and performed, and the data are convincing. One point I would suggest is that in the experiments of mice with FMT, control mice should be those colonized with feces of healthy macaques, but not with no FMT.

See response to Reviewer 1, Public review comment 4.

Author Response

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

Reviewer #1 (Public Review):

Assessment:

The manuscript titled 'Rab7 dependent regulation of goblet cell protein CLCA1 modulates gastrointestinal 1 homeostasis' by Gaur et al discusses the role of Rab7 in the development of ulcerative colitis by regulating the lysosomal degradation of Clca1, a mucin protease. The manuscript presents interesting data and provides a potential molecular mechanism for the pathological alterations observed in ulcerative colitis. Gaur et al demonstrate that Rab7 levels are lowered in UC and CD. However, a similar analysis of Rab7 levels in ulcerative colitis (UC) and Crohn's disease (CD) patient samples was conducted recently (Du et al, Dev Cell, 2020) which showed that Rab7 levels are found to be elevated under these conditions. While Gaur et al have briefly mentioned Du et al's paper in passing in the discussion, they need to discuss these contradictory results in their paper and clarify these differences. Additionally, Du et al are not included in the list of references.

Strengths:

The manuscript used a multi-pronged approach and compares patient samples, mouse models of DSS, and protocols that allow differentiation of goblet cells. They also use a nanogel-based delivery system for siRNAs, which is ideal for the knockdown of specific genes in the gut.

Weaknesses:

(1) Du et al, Dev Cell 2020 (https://doi.org/10.1016/j.devcel.2020.03.002) have previously shown that Rab7 levels are elevated in a similar set of colonic samples (age group, number etc.) from UC and CD patients. Gaur et al have not discussed this paper or its findings in detail, which directly contradicts their results. Clarification regarding this should be provided.

We thank and appreciate the reviewer for bringing this point.

The results shown by Du et al, Dev Cell, 2020 depict elevated expression of Rab7 in UC and CD patients compared to controls. In first occurrence, these results appear contradictory, but there may be a few possible explanations for this.

Firstly, Rab7 expression levels may fluctuate in the tissue depending on the degree of the gut inflammation. This can be concluded from our observations in DSS-mice dynamics model and the human patient samples with mild and moderate UC. Furthermore, Du et al provide no information of the severity of the condition among the patients employed in the study. Our motive, in the current work, was to emphasize this aspect. This point was mentioned in the discussion section of the manuscript. However, in view of the reviewer’s concern, we have now added a detailed comment on this in the main text of the revised version of the manuscript.

Secondly, the control biopsies in our investigation were acquired from non-IBD patients, and not what was done by Du et al., wherein biopsies from the normal para-carcinoma region of the colorectal cancer patients were used. One cannot overlook the fact that physiological and molecular changes are apparent even in non-inflamed regions in the gut of an IBD or CRC patient. It is possible that the observed discrepancy arises due to the differences in the sample type used for comparing the Rab7 expression.

Finally, the main sub-tissue region showing a decrease in Rab7 expression in UC samples, appeared to be the Goblet cells which was not covered by Du et al.

Keeping these points in mind we do not think that there is a contradiction in our findings with that of Du et al., 2020. In the revised submission some of these explanations are incorporated (Lines 106-109).

This was an oversight from our side. We have actually mentioned Du et al., 2020 in the discussion (line number 345) but somehow the reference was missing in the main list. We have ensured that the reference is included in the revised version and that their findings are included both in main text and in the discussion.

Reviewer #2 (Public Review):

Summary:

In this work, the authors report a role for the well-studied GTPase Rab7 in gut homeostasis. The study combines cell culture experiments with mouse models and human ulcerative colitis patient tissues to propose a model where, Rab7 by delivering a key mucous component CLCA1 to lysosomes, regulates its secretion in the goblet cells. This is important for the maintenance of mucous permeability and gut microbiota composition. In the absence of Rab7, CLCA1 protein levels are higher in tissues as well as the mucus layer, corroborating with the anticorrelation of Rab7 (reduced) and CLCA1 (increased) from ulcerative colitis patients. The authors conclude that Rab7 maintains CLCA1 level by controlling its lysosomal degradation, thereby playing a vital role in mucous composition, colon integrity, and gut homeostasis.

Strengths:

The biggest strength of this manuscript is the combination of cell culture, mouse model, and human tissues. The experiments are largely well done and, in most cases, the results support their conclusions. The authors go to substantial lengths to find a link, such as alteration in microbiota, or mucus proteomics.

Weaknesses:

(1) There are also some weaknesses that need to be addressed. The association of Rab7 with UC in both mice and humans is clear, however, claims on the underlying mechanisms are less clear. Does Rab7 regulate specifically CLCA1 delivery to lysosomes, or is it an outcome of a generic trafficking defect?

We thank the reviewer for the insightful comment. We would like to bring forth the following explanation for each these concerns:

Our immunofluorescence imaging experiments revealed co-localization of Rab7 protein with CLCA1 and the lysosomes (Fig 7I). In addition, the absence of Rab7 affects the transport of CLCA1 to lysosomes (Fig 7J). This demonstrates that Rab7 may be involved in regulation of CLCA1 transport (presumably along with other cargo), to lysosomes selectively. However, we do recognize that the point raised by the reviewer about possible effect of a generic trafficking defect is valid.

(2) CLCA1 is a secretory protein, how does it get routed to lysosomes, i.e., through Golgi-derived vesicles, or by endocytosis of mucous components? Mechanistic details on how CLCA1 is routed to lysosomes will add substantial value.

As mentioned in the manuscript, the trafficking of CLCA1 protein or CLCA1-containing vesicles within the goblet cell is unknown, with no information on the proteins involved in its mobility. The switching of CLCA1 containing vesicles from the secretory route to lysosomes needs extensive investigation involving overall trafficking of the protein. Taken together, the complete answer to both these important questions will need a series of experiments and those may be interesting avenues for future research.

(3) Why does the level of Rab7 fluctuate during DSS treatment (Fig 1B)?

This is a very thoughtful point from the reviewer. We detected a distinct pattern of Rab7 expression fluctuation in intestinal epithelial cells after DSS-dynamics treatment in mice. Perhaps, these changes are the result of complex cellular signaling in response to the DSS treatment. Rab7, being a fundamental protein involved in protein sorting pathway, is expected to undergo alteration based on cells requirement. Presently there are no reports suggesting the regulatory mechanisms that govern Rab7 levels in the gut.

(4) Does the reduction seen in Rab7 levels (by WB) also reflect in reduced Rab7 endosome numbers?

We observed reduction in Rab7 expression both at RNA and protein levels. To confirm whether this alteration will lead to reduced Rab7 positive endosome numbers may require detailed investigations.

(5) Are other late endosomal (and lysosomal) populations also reduced upon DSS treatment and UC? Is there a general defect in lysosomal function?

There are no direct evidences showing reduction in the late endosomal and lysosomal population during gut inflammation, but few studies link lysosomal dysfunction with risk for colitis (doi: 10.1016/j.immuni.2016.05.007).

(6) The evidence for lysosomal delivery of CLCA1 (Fig 7 I, J) is weak. Although used sometimes in combination with antibodies, lysotracker red is not well compatible with permeabilization and immunofluorescence staining. The authors can substantiate this result further using lysosomal antibodies such as Lamp1 and Lamp2. For Fig 7J, it will be good to see a reduction in Rab7 levels upon KD in the same cell.

We used Lysotracker red in live cells followed by fixation. So, permeabilization issues were resolved. Lamp1, as suggested by the reviewer, is definitely a better marker for lysosomes in immunofluorescence studies, but is also shown to mark late endosomes (doi: 10.1083/jcb.132.4.565). As Rab7 protein also marks the late endosomes, using Lamp1 may leave the ambiguity of CLCA1 in Rab7 positive late endosomes versus lysosomes. Nevertheless, we have carried out this experiment, as suggested by the reviewer, by staining the cells with LAMP1 (author response image 1). As demonstrated in our previous data, the colocalization of CLCA1 with LAMP1 positive vesicles decreased upon Rab7 knockdown. Also, we observed a decrease in the intensity of LAMP1 staining in cells with Rab7 knockdown. Additionally, we noted a reduction in the LAMP1 staining intensity in cells where Rab7 was knocked down. This observation can be attributed to the decrease in the presence of Rab7-positive vesicles or late endosomes which also exhibit LAMP1 staining.

Author response image 1.

(A) Representative confocal images of HT29-MTX-E12 cells transfected with either scrambled siRNA (control) or Rab7 siRNA (Rab7Knockdown). Cells are stained with CLCA1 (green) using antiCLCA1 antibody and lysosomes with LAMP1. (B) Graph shows quantitation of colocalization between CLCA1 and LAMP1 from images (n=20) using Mander’s overlap coefficient. Inset shows zoomed areas of the image with colocalization puncta (yellow) marked with arrows.

(7) In this connection, Fig S3D is somewhat confusing. While it is clear that the pattern of Muc2 in WT and Rab7-/- cells are different, how this corroborates with the in vivo data on alterations in mucus layer permeability -- as claimed -- is not clear.

The data in Fig. S3D suggest the involvement of Rab7 in packaging of Muc2. The whole idea for doing this experiment was to support our observation in the Rab7KD-mice model where mucus layer was seen to be loose and more permeable in Rab7 deficient mice.

(8) Overall, the work shows a role for a well-studied GTPase, Rab7, in gut homeostasis. This is an important finding and could provide scope and testable hypotheses for future studies aimed at understanding in detail the mechanisms involved.

We thank the reviewer for this comment.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Specific questions to the authors:

(1) Why is the dotted line in Fig. 1c at -7.5? What does this signify?

Response: The dotted line was intended to represent the baseline; in the revised manuscript it is corrected and placed at y=0.

(2) Du et al should be cited. Fig 6 K-Q from Du et al should be discussed and reasons for contradictory findings should be given in greater detail, rather than a single sentence in the discussion.

Response: The reference for Du et al is included in the list and the possible reasons the findings of the current work are discussed in the main text (Line 106-109).

(3) Fig1. Why are Rab7 levels low even in remission patient samples? Can DSS be withdrawn to induce remission followed by analysis of colonic samples?

Response: A possible explanation for this observation could be that the restoration of Rab7 levels may not immediately follow the resolution of clinical symptoms in remission patients. After the remission initiation, the normalization of cellular processes, including the regulation of Rab7 expression, might exhibit a time lag. A thorough investigation of Rab7 levels and the allied pathways at different time points during the remission phase could provide deeper insights into the gradual dynamics of recovery. As suggested by the reviewer, DSS withdrawal induced recovery model can be utilized for understanding the same and could be a good approach for future investigations.

(4) Fig. 2: Single-channel fluorescence should be shown.

Response: The single channel fluorescence images are incorporated in Fig. S2.

(5) Line 456 should be modified. 'Blind pathologist' does not read well!

Response: The line has been modified with ‘Blinded pathologist’.

(6) Other inflammatory markers, cytokine levels should be looked at in addition to TNF alpha.

Response: TNF-α is a crucial mediator in intestinal inflammation, actively contributing to the development of IBD. Elevated levels of TNF-α are observed in patients of IBD (Billmeier U. et al, World J Gastroenterol. 2016). In the current work, while probing for TNF-α our primary objective was to examine this significant indicator of colitis following Rab7 knockdown in mice, aiming to gain insights into heightened gut inflammation.

(7) Quantitation of S3D should be provided.

Response: The dispersed expression of Muc2 was observed in n=20 cells per sample and it was a qualitative observation. The aim was to identify any changes in Muc2 packaging under Rab7 knockout conditions.

(8) Microbiota analysis should include Rab7KD+DSS mice.

Response: We understand the importance of this point, however, in the current work our primary objective was to specifically investigate changes in microbial diversity and abundance in Rab7KD mice compared to both DSS+CScr and CScr mice. Rab7KD+DSS mice is expected to show higher dysbiosis in comparison to DSS+CScr.

(9) Fig 6 H and I, G. How do Clca1 levels reduce in Rab7kd +DSS relative to Scr+DSS while they are higher in Rab7kd compared to Scr. Comment.

Response: The decreased expression of CLCA1 in the mucus of DSS+Rab7KD mice can be attributed to a consequence of significant reduction in goblet cell numbers in these mice, as evidenced by the observed loss of these cells (Fig.S3 B and Fig. S3C). CLCA1 is exclusively secreted by goblet cells, so a decline in their numbers directly affects CLCA1 levels.

(10) How are Rab7 levels downregulated? What is the predicted mechanism?

Response: While our current study didn't explore this aspect, it's worth noting that Rab7 protein levels undergo regulation through various mechanisms, including post-translational modifications such as Ubiquitination and SUMOylation. These modifications are known to regulate Rab7 stability, transport and recycling. Specific experiments conducted during this study (work not included in the manuscript) indicated the participation of SENP7, a deSUMOylase, in controlling the stability of Rab7 protein, particularly in the context of colitis. Additionally, goblet cell specific mechanisms are also likely to be controlling the Rab7 in the gut.

(11) What is the explanation for opposite changes in CLCa1 RNA (down) and protein (up).

Response: The reduction in CLCA1 at the RNA level could be associated with the decrease in goblet cell numbers during colitis. Our investigation indicates that Rab7 predominantly influences CLCA1 at the protein level by impacting its degradation pathway. It is important to acknowledge that not all the alterations in CLCA1 observed during colitis can be solely attributed to Rab7, but our study has identified a connection between Rab7 and CLCA1.

(12) In light of Du et al, it would be interesting to see how the number of peroxisomes changes upon alteration of Rab7 levels.

Response: The suggestion by the reviewer is noteworthy. Since, being an altogether different domain, it deviates from the primary objectives of current work. Here, our goal was specifically on exploring the role of Rab7 in goblet cell functioning. Thus is an attractive theme for future investigations.

(13) While Gaur et al suggest in their discussion that Du et al may have observed an upregulation in Rab7 levels in different cell types of the intestine, this is not apparent from the data provided. Tissue sections should be carefully analysed to provide data supporting this observation. Differences in reagents used (antibodies) should also be considered. As far as the human patient data is concerned, it does not appear that the sample stages are very different across the two manuscripts (based on age, inclusion criteria etc.).

Response: This has been explained in detail in our public comments.

Reviewer #2 (Recommendations For The Authors):

(1) In general, image-based measurements could be done better (for example, object-based statistics than pixel-based overlaps) and represented differently. It is difficult to appreciate the reduction in Rab7 levels in goblet cells in Fig 2 A, C. It might be good to show the channels separately, and perhaps use an intensity gradient LUT for the Rab7 channel.

Response: The single channel fluorescence images are incorporated in Fig. S2.

(2) The EM images, and particularly Fig 2F are not convincing, with an oddly square-shaped vesicle. I'm not sure what value they are adding to the interpretation.

Response: The observed square-shaped vesicle in Fig. 2F could be attributed to the dynamic nature of vesicles within a cell. This dynamicity allows them to adopt various shapes depending on their state and function within the cell. The presence of Rab7 near vacuoles of goblet cells signify its probable involvement in the regulation of secretory function of these cells which is the key aspect being covered in this work.

(3) A general method question concerns the definition of the distal colon. How is this decided, particularly when colon lengths are reduced upon DSS treatment?

Response: The murine colon is divided into proximal and distal colon of mouse and has a visual difference of inner folds which are quite prominent in proximal colon. Additionally, the portion towards the rectum (predominantly distal colon) was majorly utilized for the experiments. In each case the various experimental groups were matched for the respective areas.

(4) The use of an in vivo intestine-specific Rab7 silencing model is good. Why does Rab7 KD itself not capitulate aspects of DSS treatment, rather it seems to exacerbate it.

Response: Our objective was to determine whether the downregulation of Rab7 during colitis was the cause or consequence of gut inflammation. Interestingly, our investigation using the murine Rab7 knockdown model revealed that the reduction of Rab7 expression in the intestine exacerbates inflammation. Subsequent analysis demonstrated that the absence of Rab7 disrupts goblet cell secretory function, consequently contributing to heightened inflammation. Our findings overall suggest that Rab7 downregulation is not merely a consequence but plays a contributory role in aggravating inflammation in the context of colitis.

(5) The axes labels in Fig 5 are not readable. It is unclear how Rab7 KD is more similar in gut microbiota phenotypes to DSS than to CScr.

Response: The microbial analysis revealed an abnormal composition of gut microbiota in Rab7KD mice compared to CScr. Interestingly, this composition exhibited some similarity to the inflamed gut microbiota observed in DSSScr mice. The analysis further demonstrated a shift in microbial diversity in Rab7KD mice, showcasing characteristics akin to those observed in inflamed mice. This similarity in gut microbiota phenotypes between Rab7KD and DSSScr suggests a potential link or influence of Rab7 downregulation on the microbiota, contributing to the observed similarities with DSS-induced inflammation.

(6) The use of mucous proteomics to identify mechanisms of Rab7-mediated phenotype is a good approach. The replicates in the proteomics dataset (Fig 6F) do not seem to match. Detailing of methodology used for analysis will help to overcome these doubts.

Response: The identified proteins in different samples of mucus proteomics were subjected to label free quantification. Subsequently, the significantly altered proteins were subjected to analysis with the False Discovery Rate (FDR) to control for potential false positives and ascertain the validity of the findings.

(7) It will be good to see the immunoblots showing the negative correlation between Rab7 and CLCL1 in Fig 7D.

Response: Fig. 7C shows western blot for protein expression of CLCA1of the same control and UC samples which were used in Fig. 1F to show Rab7 expression. Fig. 7D is the quantitative correlation plot for Fig. 1F (Rab7 expression) and Fig. 7C (CLCA1 expression).

(8) Why is UC different from the DSS model for Rab7 gene expression but not protein levels? Endosomal counts could help address this.

Response: We encountered challenges in accurately counting the individual puncta of Rab7 expression in immunofluorescence images due to the nature of tissue samples. Locating endosomes within a single cell proved to be challenging, and the proximity of many puncta made it difficult to delineate them individually. Despite these technical difficulties, the intriguing prospect of correlating Rab7 expression with endosomal counts remains a compelling aspect that may well be area for future investigations.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The manuscript entitled "Phosphodiesterase 1A Physically Interacts with YTHDF2 and Reinforces the Progression of Non-Small Cell Lung Cancer" explores the role of PDE1A in promoting NSCLC progression by binding to the m6A reader YTHDF2 and regulating the mRNA stability of several novel target genes, consequently activating the STAT3 pathway and leading to metastasis and drug resistance.

Strengths:

The study addresses a novel mechanism involving PDE1A and YTHDF2 interaction in NSCLC, contributing to our understanding of cancer progression.

Weaknesses:

The following issues should be addressed:

(1) The body weight changes and/or survival times of each group in the in vivo metastasis studies should be provided.

Thank you for your suggestion! We have already provided the body weight of each group in the in vivo metastasis studies in FigureS4D and FigureS5D (see below).

(2) In Figure 7, the direct binding between YTHDF2 and the potential target genes should be further validated by silencing YTHDF2 to observe the half-life of the mRNA levels of target genes, in addition to silencing PDE1A.

Thank you for your suggestion! We have found that siYTHDF2 does not significantly affect expression of SOCS2 in NSCLC cells (see author response image 1 below). We hypothesize that YTHDF2 functions as a m6A reader to recognize the target mRNA, thus if YTHDF2 is silence by siRNA, there is still some expression in the cells, allowing it to continue recognizing and exerting its function. Therefore, the mRNA of SOCS2 could not significantly affect expressed. However, PDE1A functions as a degrader of mRNA, thus when it is disrupted, the mRNA degradation effect could be strong.

Author response image 1.

SOCS2 mRNA expression after siYTHDF2 in NSCLC cells

(3) In Figure 7, the potential methylation sites of "A" on the target genes such as SOCS2 should be verified by mutation analysis, followed by m6A IP or reporter assays.

Thank you for your suggestion! The m6A IP or reporter assays may be carried out to detect the potential methylation sites in future. We have added the suggestion in manuscript “Meanwhile, YTHDF2 might act as an m6A RNA “reader” by interacting with PDE1A, but the mechanism might need further investigation”.

(4) In Figure 6G, the correlation between the mRNA levels of STAT3 and YTHDF2 needs clarification. According to the authors' mechanism, the STAT3 pathway is activated, rather than upregulation of mRNA levels (or protein levels, as shown in Figure 6F). Figure 7 does not provide evidence that STAT3 is a bona fide target gene regulated by YTHDF2.

Thank you for your suggestion! The reviewer is right, STAT3 pathway is activated, rather than upregulation of mRNA levels by YTHDF2, so the relationship between YTHDF2 mRNA and STAT3 mRNA is not suitable for this study. Meanwhile, the relationship between YTHDF2 mRNA and STAT3 mRNA is not as strong as we expected with Pearson value 0.37. Thus, we have already deleted Figure 6G in the revised version.

(5) The final figure, which discusses sensitization to cisplatin by PDE1A suppression, does not appear to be closely related to the interaction or regulation of PDE1A/YTHDF2. If the authors claim this is an m6A-associated event, additional evidence is needed. Otherwise, this part could be removed from the manuscript.

Thank you for your suggestion! We have already deleted Figure 8 just as the reviewer suggested.

Reviewer #2 (Public review):

This manuscript aims to investigate the biological impact and mechanisms of phosphodiesterase 1A (PDE1A) in promoting non-small cell lung cancer (NSCLC) progression. They first analyzed several databases and used three established NSCLC cell lines and a normal cell line to demonstrate that PDE1A is overexpressed in lung cancer and its expression negatively correlated with the outcomes of patients. Based on this data, they suggested PDE1A could be considered as a novel prognostic predictor in lung cancer treatment and progression. To study the biological function of PDE1A in NSCLC, they focused on testing the effect of inhibition of PDE1A genetically and pharmacologically on cell proliferation, migration, and invasion in vitro. They also used an experimental metastasis model via tail vein injection of H1299 cells to test if PDE1A promoted metastasis. By database analysis, they also decided to investigate if PDE1A promoted angiogenesis by co-culturing NSCLC cells with HUVECs as well as assessing the tumors from the subcutaneous xenograft model. However, in this model, whether PDE1A modulation impacted tumor metastasis was not examined. To address the mechanism of how PDE1A promotes metastasis, the authors again performed a bioinformatic and GSEA enrichment analysis and confirmed PDE1A indeed activated STAT3 signaling to promote migration. In combination with IP followed by Mass spectrometry, they found PDE1A is a partner of YTHDF2, the cooperation of PDE1A and YTHDF2 negatively regulated SOCS2 mRNA as demonstrated by RIP assay, and ultimately activated STAT3 signaling. Finally, the authors shifted the direction from metastasis to chemoresistance, specifically, they found that PDEA1 inhibitions sensitized NSCLC cells to cisplatin through MET and NRF2 signaling.

Strength:

Overall, the manuscript was well-written and the majority of the data supported the conclusions. The authors used a series of methods including cell lines, animal models, and database analysis to demonstrate the novel roles and mechanism of how PDE1 promotes NSCLC invasion and metastasis as well as cisplatin sensitivity. Given that PDE1A inhibitors have been perused to use in clinic, this study provided valuable findings that have the translational potential for NSCLC treatment.

Weaknesses:

The role of YTHDF2 in PDE1A-promoted tumor metastasis was not investigated. To make the findings more clinical and physiologically relevant, it would be interesting to test if inhibition of PDE1A impacts metastasis using lung cancer orthotopic and patient-derived xenograft models. It is also important to use a cisplatin-resistant NSCLC cell line to test if a PDE1A inhibitor has the potential to sensitize cisplatin in vitro and in vivo.

Thank you for your suggestion! The role of YTHDF2 in PDE1A-promoted tumor metastasis may need in vivo analysis. Therefore, we discussed the point in the discussion section “In addition, it is worth testing if PDE1A inhibition affects metastasis in lung cancer orthotopic and patient-derived xenograft models. The role of YTHDF2 in PDE1A-driven tumor metastasis should be elucidated in future studies”.

The reviewer is absolutely right, it is very important to use a cisplatin-resistant NSCLC cell line to test the potential effect of PDE1A in sensitization to cisplatin. The current data could not support the conclusion, more data is needed to make the final conclusion. As suggested by reviewer 1, we have deleted these data in this version.

Furthermore, this study relied heavily on different database analyses, although providing novel and compelling data that was followed up and confirmed in the paper, it is critical to have detailed statistical description section on data acquisition throughout the manuscript.

Thank you for your suggestion! We have already added the detailed statistical description section in Figure legends.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Scale Bar Display: Scale bars should be included in Figures 4F, 5F, and 6E to ensure clarity and accuracy in the presented microscopic images.

Thank you for your suggestion! We have already added the scale bars on Figures 4F, 5F, and 6E.

(2) HE Staining Images: The authors are suggested to provide more images for HE staining of lungs to offer a comprehensive visual representation and to substantiate the findings.

Thank you for your suggestion! We have already provided more images for HE staining of lungs in Figure S4E and Figure S5E.

Reviewer #2 (Recommendations for the authors):

It would be helpful to clarify several points in the manuscript for better understanding.

(1)The HELF cells were stated between the epithelial cell line (page 7, line 118) and fibroblast (page 12, line 288) which needs to be clarified. It is not clear if the cells used in this study were periodically authenticated.

Thank you for your suggestion! We have already revised the expression of HELF cells, and it is actually the human lung fibroblasts.

(2) More details could be added to the methods such as the amount of Matrigel coated for invasion assay and the components for the lysis buffer and IP buffer.

Thank you for your suggestion! We have already added more details in the Methods section.

(3) Providing the rationale for using 20% FBS instead of using some chemoattracts such as EGF, LPA, or HGF or a low level of FBS for migration will be helpful.

Thank you for your suggestion! Although chemoattracts are suitable for cell migration experiment, and 20% FBS is also suitable for cell migration experiment. We listed the literatures using this system below for example.

(1) Xiaolin Peng, Zhengming Wang, Yang Liu. et al. Oxyfadichalcone C inhibits melanoma A375 cell proliferation and metastasis via suppressing PI3K/Akt and MAPK/ERK pathways, Life Sciences, 2018, 206, 35-44. https://doi.org/10.1016/j.lfs.2018.05.032

(2) Rong, S., Dai, B., Yang, C. et al. HNRNPC modulates PKM alternative splicing via m6A methylation, upregulating PKM2 expression to promote aerobic glycolysis in papillary thyroid carcinoma and drive malignant progression. J Transl Med, 2024, 22, 914 (2024). https://doi.org/10.1186/s12967-024-05668-9

(4) For HPA analysis In Figure 1, it would be great to assess how many lung cancer cases are NSCLC and define IDO/area for the y-axis.

Thank you for your suggestion! There are 19 samples were analyzed, they are all NSCLC sample, and we have already revised our manuscript accordingly. Meanwhile, we also made a mistake, it should be IOD/area which means Integral optical density/area. We have revised the Figures and Figure legends.

(5) On page 23, line 480, "Therefore, this study reveals the effect and mechanism of PDEA1 in promoting HCC metastasis...", should HCC be NSCLC?

Thank you for your suggestion! We have already revised the manuscript accordingly.

(6) Specific scramble siRNAs should be clearly shown in their respective figures. In Figure 7F, it is not clear why DMSO did not scramble siRNA was used as the control.

Thank you for your suggestion! It is our fault to show the DMSO in Figure 5F, DMSO is the negative control of Figure 5G, and we have revised the Figure 5F and 5G accordingly.

Author response:

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

Reviewer #1 (Public review):

Summary:

Park et al. conducted various analyses attempting to elucidate the biological significance of SARS-CoV-2 mutations. However, the study lacks a clear objective. The specific goals of the analyses in each subsection are unclear, as is how the results from these subsections are interconnected. Compiling results from unrelated analyses into a single paper can be confusing for readers. Clarifying the objective and narrowing down the topics would make the paper's purpose clearer.

The logic of the study is also unclear. For instance, the authors developed an evaluation score, APESS, for analyzing viral sequences. Although they state that the APESS score correlates with viral infectivity, there is no explanation in the results section about why this is the case.

The structure of the paper should be reconsidered.

Thank you for your feedback. We have heeded the input that the study lacks a clear objective and made sure that the overall goal of the study is reflected in the Abstract, Results, and Discussion.

We have made sure that the specific goals in each subsection are clearer in the Results section that better explain the goals of those sections and elaborated on how the components of our study connect to each other. We have addressed these in more detail in the ‘Recommendations for the authors’ section.

Thank you for the feedback on APESS, our evaluation model. APESS was created based on virus properties that we discovered of SARS-CoV-2 in our study. When applying our evaluation model, high APESS scores indicated high infectivity. APESS is calculated from a comprehensive evaluation of SARS-CoV-2 at the nucleotide, amino acid, and protein structure levels.

The detailed explanations and exact calculations of APESS are detailed in the Materials and Methods section in line 571 but we should have been more detailed in the Results section as well. We have made sure to properly indicate this in the Results section in line 284.

And overall, we have made edits to the manuscript that accurately explain our research by amending terms, restructuring arguments, and providing more clarity for the interconnectivity of the research.

Reviewer #2 (Public review):

Summary:

The authors have developed a machine learning tool AIVE to predict the infectivity of SARS-CoV-2 variants and also a scoring metric to measure infectivity. A large number of virus sequences were used with a very detailed analysis that incorporates hydrophobic, hydrophilic, acid, and alkaline characteristics. The protein structures were also considered to measure infectivity and search for core mutations. The study especially focused on the S protein of SARS-CoV-2. The contents of this study would be of interest to many researchers related to this area and the web service would be helpful to easily analyze such data without in-depth bioinformatics expertise.

Strengths:

- Analysis of large-scale data.

- Experimental validation on a partial set of searched mutations.

- A user-friendly web-based analysis platform that is made public.

Weaknesses:

- Complexity of the research.

Thank you for your kind feedback. Our study explored a wide range of topics including biochemical properties, machine learning, and viral infectivity.

In presenting our research, we recognize that our comprehensive analysis may have slightly obscured the specific aims and overall objective of the study. We investigated properties in the viral sequences of SARS-CoV-2 and examined big data, clinical data, and expression data to elucidate their effect on viral infectivity. We then used evaluation modeling and in silico and in vitro validation.

We have clarified the aims of our research and improved upon the flow of the manuscript by adding sentences that outline the goals of our research in the appropriate sub sections of the Results and Discussion sections.

Reviewer #1 (Recommendations for the authors):

The abstract should clearly state the backgrounds, objectives, strategies, and findings of this study in an orderly manner.

Thank you for your feedback. We have restructured the Abstract to better reflect the goals and methods of our study. We start the Abstract by introducing the background of the study ‘An unprecedented amount of SARS-CoV-2 data has been accumulated compared with previous infectious diseases, enabling insights into its evolutionary process and more thorough analyses.’ in line 48. Then we more clearly stated the overall objectives of our research in line 50 as ‘This study investigates SARS-CoV-2 features as it evolves to evaluate its infectivity.’ Then, we clearly defined our specific discoveries in the virus, the purpose of our evaluation model, and how we validated our findings.

In the Introduction, the message of each paragraph is unclear. Please clearly state the objectives of the study and what was done to achieve these objectives.

Thank you for the feedback. We have updated the Introduction section to more clearly state the objectives of the study.

To increase clarity, we have moved ‘Furthermore, hydrophobic properties in the amino acid sequence affect protein folding. Coronavirus hydrophobicity has significant effects on amino acid properties and protein folding.’ to line 127.

In line 130, we rephrased the first sentence of the paragraph to ‘For these prior approaches to virus analysis and prediction, expertise with the relevant fields is required for a full understanding.’ to better establish the link between the background information and aims of the study. Then in line 134, we added ‘elucidate properties about the virus’ to clarify the aims of the study.

In line 141, we have improved the clarity of the sentence to better present the scope and objectives of the study.

The relationship between the sections in the Results is unclear. Clarify why each section is necessary and how they are interconnected.

We investigated properties in the viral sequences of SARS-CoV-2 that highlighted amino acid substitutions or changes in polarity (Figure 1). In VOCs, we noted trends or absences of amino acid substitutions at specific positions (Figure 2). We examined epidemiological and clinical data to determine the infectivity, severity, and symptomaticity of lineages. Looking at expression data and binding affinity further illuminated the effect of amino acid substitutions (Figure 3). We created APESS, an evaluation modeling, that is comprehensively calculated from the nucleotide, amino acid, and protein structure levels of the virus. Evaluation of lineages revealed that higher APESS scores were associated with higher infectivity (Figure 4). We used in silico and in vitro validation to reinforce our findings then used machine learning to make predictions on future developments (Figure 5). We created candidate sequences for evaluation and utilized machine learning in predictions (Figure 6).

We have added explanations to each section in Results that elucidate the objective of each section and how they connect with each other in the wider study.

In line 157, we have added ‘We examined the amino acid sequences of SARS-CoV-2 to make discoveries about biochemical properties.’ to clearly outline the objective of the subsection.

In line 207, we have improved the phrasing of the sentence.

In line 278, we stressed that ‘We developed APESS, an evaluation model to analyze viral sequences based on the nucleotide, amino acid, and protein structure properties.’ to properly define the purpose and background of APESS.

Please define abbreviations when they first appear.

We have added the full terms for the stated abbreviations in the relevant sections of the manuscript.

In line 107, we have added the proper abbreviation for Our World in Data (OWID).

In lines 143, 175, and 489 we have added the full term for Variants of Concern (VOCs).

In line 160, we have added the full term for Receptor Binding Motif (RBM).

Reviewer #2 (Recommendations for the authors):

(1) pg 9, line 51, full name of RBM should be declared.

We have added the full name of Receptor Binding Motif (RBM) to the appropriate section in the Abstract.

(2) How are the Variants of Concern (VOCs) defined?

Thank you for the comment and we apologize for the confusion. Variants of Concern as defined by the World Health Organization are specified in the Materials and Methods section. We have also added the full name for Variants of Concern (VOCs) when they are first mentioned in the Introduction and Results sections.

(3) pg 17, line 297. The purpose of using AI/ML to predict amino acid substitutions at specific locations is not clear. The VOCs and related mutation loci were already searched, so the AA substitution prediction step seems a little repetitive. Is it to create customized sequences? Also, if prediction (or probability) was made, some performance evaluation would be helpful.

Thank you for this feedback. The purpose of utilizing machine learning to make predictions about amino acid substitutions is to assess the possibility of amino acid substitutions occurring at specific locations. These potential amino acid substitutions were evaluated by APESS to have high scores, linking them to high infectivity. As the feedback suggests, amino acid substitutions in VOCs are researched but our prediction sought to ascertain the likelihood of amino acid substitutions that our evaluation model associated with infectivity. In the Results section in line 330, we assessed the probability of amino acid substitutions N460K and Q493R that the study found to be significant. The datasets that we utilized for these predictions are detailed in the Materials and Methods section in line 677.

The models we trained with machine learning predicted the probability of mutations based on samples in each group and their performance was evaluated by comparing the presence of mutations in the clades they diverged from. We have added the following sentences to line 330: “We used Accuracy, Precision, Recall, and F1 score to evaluate performance. All models showed high performance scores above 0.95 in Precision, Recall, and F1 score. For accuracy, XGBoost, scored above 0.89, exhibiting relatively high performance while LightGBM scored above 0.78.”

(4) pg 17, line 289. The objective of creating candidate lineages is not clear and would be helpful for the readers if its purpose is elaborated on. Since there are enough SARS-CoV-2 sequences, wouldn't it be more realistic and accurate to use those real sequences instead of creating them? Furthermore, the candidate lineages should be defined but they were missing in this section. This part made it a little difficult to follow the overall paper's logic.

The manuscript should have been clearer on what ‘candidate lineages’ signified, we apologize for the confusion. In line 314, we included the following sentences for clarity: ‘We introduced amino acid substitutions at specific locations in the SARS-CoV-2 backbone for the wildtype and VOCs. The amino acid substitutions were lysine (K), arginine (R), asparagine (N), serine (S), tyrosine (Y), and glycine (G). We then evaluated the infectivity of these candidate lineages with our evaluation model APESS.’

The purpose of creating candidate lineages in our study was to assess the effect of specific amino acid substitutions on the virus’ infectivity. The amino acid substitutions we evaluated were lysine (K), arginine (R), asparagine (N), serine (S), tyrosine (Y), and glycine (G). We determined that examining the introduction of specific amino acid substitutions to SARS-CoV-2 sequences would highlight the significance they had on infectivity. We have revised the paragraph in line 314 of the Results section to convey what we were doing.

(5) This study covers very detailed contents regarding lineages, mutations, and their effect on infectivity. It would be more readable if subsections could be added per group of investigation, especially in the results and discussion section.

In the Results section, we have emphasized the objective of each subsection and how they connect with one another for the overall goals of our study.

In line 157, we have added ‘We examined the amino acid sequences of SARS-CoV-2 to make discoveries about biochemical properties.’ to clearly outline the objective of the subsection.

In line 207, we have improved the phrasing of the sentence.

In line 278, we stressed that ‘We developed APESS, an evaluation model to analyze viral sequences based on the nucleotide, amino acid, and protein structure properties.’ to properly define the purpose and background of APESS.

We have made edits to the Discussion section to more clearly indicate subsections.

In line 389, we have added ‘In our investigation of various viruses’ to clearly indicate the background on other viruses.

In line 409, we added the sentence ‘We made discoveries on specific amino acid substitutions at positions.’ to indicate the subsection talking about N437R, N460K, and D467 mutations.

In line 471, we added the sentence ‘We created AIVE to feature our findings and analyses on an online platform.’ And modified the following sentence to better explain AIVE.

(6) pg 26, line 557. The criteria for the SCPSi scores were set to 0.9 and 0.1 by the proportion of the Omicron and Delta variants. How do other criteria affect the performance of the method?

Thank you for the question and check point. We used 0.9/0.1 for our initial criteria in our SCPS calculation. To determine how that affected performance, we have used 0.8/0.2 and 0.7/0.3 as the criteria.

After calculating APESS with different SCPS weights (0.9/0.1, 0.8/0/2, 0.7/0.3), we used a Gaussian Mixture Model (GMM) to compare how the groups were divided based on APESS. All three groups with different SCPS weights were determined to accurately reflect data patterns when they had four components.

When comparing parameter values, the group that used the original weights of 0.9 and 0.1 for SCPS showed the lowest values for variance and standard error across all four components. This indicates that each component was stable and clearly distinguishable from one another.

The group where the weights were adjusted to 0.7 and 0.3 for SCPS showed significantly higher variance and a large error for the G2 component. The distribution of each component was more widespread, signifying that the stability and reliability was lower.

The group where the weights were adjusted to 0.8 and 0.2 for SCPS was positioned between the two previous groups for finer data classification and reliability. However, the group notably lacked reliability when it came to the SE values for the G4 component.

Thus, the original model with 0.9 and 0.1 weight is the most reliable.

When the Gaussian Density for each group was plotted, the group with 0.9/0.1 SCPS weights showed the highest peak near 2 (G1), with a value of approximately 2. For the group with SCPS 0.8/0.2 weights, the highest peak appeared near 4.2 (G3), showing a high value around 14. For the group with SCPS 0.7/0.3 weights, the highest peak appeared near 3.7 (G3) showing a value around 5. The group with 0.9/0.1 SCPS weights exhibited a more uniform Gaussian distribution compared to the other two.

Author response image 1.

Superposition of Gaussian Densities for SCPS weight 0.9/0.1

Author response table 1.

Statistical values of the Superposition of Gaussian Densities for SCPS weight 0.9/0.1

Author response image 2.

Superposition of Gaussian Densities for SCPS weight 0.8/0.2

Author response table 2.

Statistical values of the Superposition of Gaussian Densities for SCPS weight 0.8/0.2

Author response image 3.

Superposition of Gaussian Densities for SCPS weight 0.7/0.3

Author response table 3.

Statistical values of the Superposition of Gaussian Densities for SCPS weight 0.7/0.3

(7) Overall, the approach is very detailed and realistic. Just curious if this approach would be also applicable to other viruses such as influenza.

We appreciate the insightful comments from the reviewer, and this is a direction we hope to take our research in the future. Our study focused on SARS-CoV-2 and the properties we discovered from the virus’ spike protein interacting with the host’s ACE2 receptor. In our investigation of other coronaviruses such as MERS-CoV, SARS-CoV-1 possesses a different structure and properties than these viruses as we have illustrated in Supplementary Figure 24. We had provided explanations about our investigation of other viruses in the Discussion section. In line 389, we have added ‘In our investigation of various viruses’ to better signpost this section.

Author response:

(1) General Statements

As you will see in our attached rebuttal to the reviewers, we have added several new experiments and revised manuscript to fully address their concerns.

(2) Point-by-point description of the revisions

Reviewer #1:

Evidence, reproducibility and clarity

Summary:

The manuscript by Yang et al. describes a new CME accessory protein. CCDC32 has been previously suggested to interact with AP2 and in the present work the authors confirm this interaction and show that it is a bona fide CME regulator. In agreement with its interaction with AP2, CCDC32 recruitment to CCPs mirrors the accumulation of clathrin. Knockdown of CCDC32 reduces the amount of productive CCPs, suggestive of a stabilisation role in early clathrin assemblies. Immunoprecipitation experiments mapped the interaction of CCDC42 to the α-appendage of the AP2 complex α-subunit. Finally, the authors show that the CCDC32 nonsense mutations found in patients with cardio-facial-neuro-developmental syndrome disrupt the interaction of this protein to the AP2 complex. The manuscript is well written and the conclusions regarding the role of CCDC32 in CME are supported by good quality data. As detailed below, a few improvements/clarifications are needed to reinforce some of the conclusions, especially the ones regarding CFNDS.

We thank the referee for their positive comments. In light of a recently published paper describing CCDC32 as a co-chaperone required for AP2 assembly (Wan et al., PNAS, 2024, see reviewer 2), we have added several additional experiments to address all concerns and consequently gained further insight into CCDC32-AP2 interactions and the important dual role of CCDC32 in regulating CME. 

Major comments:

(1) Why did the protein could just be visualized at CCPs after knockdown of the endogenous protein? This is highly unusual, especially on stable cell lines. Could this be that the tag is interfering with the expressed protein function rendering it incapable of outcompeting the endogenous? Does this points to a regulated recruitment?

The reviewer is correct, this would be unusual; however, it is not the case. We misspoke in the text (although the figure legend was correct) these experiments were performed without siRNA knockdown and we can indeed detect eGFP-CCDC32 being recruited to CCPs in the presence of endogenous protein. Nonetheless, we repeated the experiment to be certain (see Author response image 1).  

Author response image 1.

Cohort-averaged fluorescence intensity traces of CCPs (marked with mRuby-CLCa) and CCP-enriched eGFPCCDC32(FL).

(2) The disease mutation used in the paper does not correspond to the truncation found in patients. The authors use an 1-54 truncation, but the patients described in Harel et al. have frame shifts at the positions 19 (Thr19Tyrfs*12) and 64 (Glu64Glyfs*12), while the patient described in Abdalla et al. have the deletion of two introns, leading to a frameshift around amino acid 90. Moreover, to be precisely test the function of these disease mutations, one would need to add the extra amino acids generated by the frame shift. For example, as denoted in the mutation description in Harel et al., the frameshift at position 19 changes the Threonine 19 to a Tyrosine and ads a run of 12 extra amino acids (Thr19Tyrfs*12).

The label of the disease mutant p.(Thr19Tyrfs12) and p.(Glu64Glyfs12) is based on a 194aa polypeptide version of CCDC32 initiated at a nonconventional start site that contains a 9 aa peptide (VRGSCLRFQ) upstream of the N-terminus we show. Thus, we are indeed using the appropriate mutation site (see: https://www.uniprot.org/uniprotkb/Q9BV29/entry). The reviewer is correct that we have not included the extra 12 aa in our construct; however as these residues are not present in the other CFNDS mutants, we think it unlikely that they contribute to the disease phenotype.  Rather, as neither of the clinically observed mutations contain the 78-98 aa sequence required for AP2 binding and CME function, we are confident that this defect contributed to the disease. Thus, we are including the data on the CCDC32(1-54) mutant, as we believe these results provide a valuable physiological context to our studies. 

(3) The frameshift caused by the CFNDS mutations (especially the one studied) will likely lead to nonsense mediated RNA decay (NMD). The frameshift is well within the rules where NMD generally kicks in. Therefore, I am unsure about the functional insights of expressing a diseaserelated protein which is likely not present in patients.

We thank the reviewer for bringing up this concern. However, as shown in new Figure S1, the mutant protein is expressed at comparable levels as the WT, suggesting that NMD is not occurring.

(4) Coiled coils generally form stable dimers. The typically hydrophobic core of these structures is not suitable for transient interactions. This complicates the interpretation of the results regarding the role of this region as the place where the interaction to AP2 occurs. If the coiled coil holds a stable CCDC32 dimer, disrupting this dimer could reduce the affinity to AP2 (by reduced avidity) to the actual binding site. A construct with an orthogonal dimeriser or a pulldown of the delta78-98 protein with of the GST AP2a-AD could be a good way to sort this issue.

We were unable to model a stable dimer (or other oligomer) of this protein with high confidence using Alphafold 3.0. Moreover, we were unable to detect endogenous CCDC32 coimmunoprecipitating with eGFP-CCDC32 (Fig. S6C). Thus, we believe that the moniker, based solely on the alpha-helical content of the protein is a misnomer.  We have explained this in the main text.

Minor comments:

(1) The authors interchangeably use the term "flat CCPs" and "flat clathrin lattices". While these are indeed related, flat clathrin lattices have been also used to refer to "clathrin plaques". To avoid confusion, I suggest sticking to the term "flat CCPs" to refer to the CCPs which are in their early stages of maturation.

Agreed. Thank you for the suggestion. We have renamed these structures flat clathrin assemblies, as they do not acquire the curvature needed to classify them as pits, and do not grow to the size that would classify then as plaques. 

Significance

General assessment:

CME drives the internalisation of hundreds of receptors and surface proteins in practically all tissues, making it an essential process for various physiological processes. This versatility comes at the cost of a large number of molecular players and regulators. To understand this complexity, unravelling all the components of this process is vital. The manuscript by Yang et al. gives an important contribution to this effort as it describes a new CME regulator, CCDC32, which acts directly at the main CME adaptor AP2. The link to disease is interesting, but the authors need to refine their experiments. The requirement for endogenous knockdown for recruitment of the tagged CCDC32 is unusual and requires further exploration.

Advance:

The increased frequency of abortive events presented by CCDC32 knockdown cells is very interesting, as it hints to an active mechanism that regulates the stabilisation and growth of clathrin coated pits. The exact way clathrin coated pits are stabilised is still an open question in the field.

Audience:

This is a basic research manuscript. However, given the essential role of CME in physiology and the growing number of CME players involved in disease, this manuscript can reach broader audiences.

We thank the referee for recognizing the ‘interesting’ advances our studies have made and for considering these studies as ‘an important contribution’ to ‘an essential process for various physiological processes’ and able ‘to reach broader audiences’. We have addressed and reconciled the reviewer’s concerns in our revised manuscript. 

Field of expertise of the reviewer:

Clathrin mediated endocytosis, cell biology, microscopy, biochemistry.

Reviewer #2:

Evidence, reproducibility and clarity

In this manuscript, the authors demonstrate that CCDC32 regulates clathrin-mediated endocytosis (CME). Some of the findings are consistent with a recent report by Wan et al. (2024 PNAS), such as the observation that CCDC32 depletion reduces transferrin uptake and diminishes the formation of clathrin-coated pits. The primary function of CCDC32 is to regulate AP2 assembly, and its depletion leads to AP2 degradation. However, this study did not examine AP2 expression levels. CCDC32 may bind to the appendage domain of AP2 alpha, but it also binds to the core domain of AP2 alpha.

We thank the reviewer for drawing our attention to the Wan et al. paper, that appeared while this work was under review.  However, our in vivo data are not fully consistent with the report from Wan et al. The discrepancies reveal a dual function of CCDC32 in CME that was masked by complete knockout vs siRNA knockdown of the protein, and also likely affected by the position of the GFP-tag (C- vs N-terminal) on this small protein. Thus:

-  Contrary to Wan et al., we do not detect any loss of AP2 expression (see new Figure S3A-B) upon siRNA knockdown. Most likely the ~40% residual CCDC32 present after siRNA knockdown is sufficient to fulfill its catalytic chaperone function but not its structural role in regulating CME beyond the AP2 assembly step.  

- Contrary to Wan et al., we have shown that CCDC32 indeed interacts with intact AP2 complex (Figure S3C and 6B,C) showing that all 4 subunits of the AP2 complex co-IP with full length eGFP-CCDC32. Interestingly, whereas the full length CCDC32 pulls down the intact AP2 complex, co-IP of the ∆78-98 mutant retains its ability to pull down the β2-µ2 hemicomplex, its interactions with α:σ2 are severely reduced.  While this result is consistent with the report of Wan et al that CCDC32 binds to the α:σ2 hemi-complex, it also suggests that the interactions between CCDC32 and AP2 are more complex and will require further studies.

- Contrary to Wan et al., we provide strong evidence that CCDC32 is recruited to CCPs. Interestingly, modeling with AlphaFold 3.0 identifies a highly probably interaction between alpha helices encoded by residues 66-91 on CCDC32 and residues 418-438 on α. The latter are masked by µ2-C in the closed confirmation of the AP2 core, but exposed in the open confirmation triggered by cargo binding, suggesting that CCDC32 might only bind to membrane-bound AP2.

Thus, our findings are indeed novel and indicate striking multifunctional roles for CCDC32 in CME, making the protein well worth further study. 

(1) Besides its role in AP2 assembly, CCDC32 may potentially have another function on the membrane. However, there is no direct evidence showing that CCDC32 associates with the plasma membrane.

We disagree, our data clearly shows that CCDC32 is recruited to CCPs (Fig. 1B) and that CCPs that fail to recruit CCDC32 are short-lived and likely abortive (Fig. 1C). Wan et al. did not observe any colocalization of C-terminally tagged CCDC32 to CCPs, whereas we detect recruitment of our N-terminally tagged construct, which we also show is functional (Fig. 6F).  Further, we have demonstrated the importance of the C-terminal region of CCDC32 in membrane association (see new Fig. S7).  Thus, we speculate that a C-terminally tagged CCDC32 might not be fully functional. Indeed, SIM images of the C-terminally-tagged CCDC32 in Wan et al., show large (~100 nm) structures in the cytosol, which may reflect aggregation. 

(2) CCDC32 binds to multiple regions on AP2, including the core domain. It is important to distinguish the functional roles of these different binding sites.

We have localized the AP2-ear binding region to residues 78-99 and shown these to be critical for the functions we have identified. As described above we now include data that are complementary to those of Wan et al. However, our data also clearly points to additional binding modalities. We agree that it will be important and map these additional interactions and identify their functional roles, but this is beyond the scope of this paper.  

(3) AP2 expression levels should be examined in CCDC32 depleted cells. If AP2 is gone, it is not surprising that clathrin-coated pits are defective.

Agreed and we have confirmed this by western blotting (Figure S3A-B) and detect no reduction in levels of any of the AP2 subunits in CCDC32 siRNA knockdown cells. As stated above this could be due to residual CCDC32 present in the siRNA KD vs the CRISPR-mediated gene KO.

(4) If the authors aim to establish a secondary function for CCDC32, they need to thoroughly discuss the known chaperone function of CCDC32 and consider whether and how CCDC32 regulates a downstream step in CME.

Agreed. We have described the Wan et al paper, which came out while our manuscript was in review, in our Introduction.  As described above, there are areas of agreement and of discrepancies, which are thoroughly documented and discussed throughout the revised manuscript.  

(5) The quality of Figure 1A is very low, making it difficult to assess the localization and quantify the data.

The low signal:noise in Fig. 1A the reviewer is concerned about is due to a diffuse distribution of CCDC32 on the inner surface of the plasma membrane. We now, more explicitly describe this binding, which we believe reflects a specific interaction mediated by the C-terminus of CCDC32; thus the degree of diffuse membrane binding we observe follows: eGFP-CCDC32(FL)> eGFPCCDC32(∆78-98)>eGFP-CCDC32(1-54)~eGFP/background (see new Fig. S7). Importantly, the colocalization of CCDC32 at CCPs is confirmed by the dynamic imaging of CCPs (Fig 1B).

(6) In Figure 6, why aren't AP2 mu and sigma subunits shown?

Agreed. Not being aware of CCDC32’s possible dual role as a chaperone, we had assumed that the AP2 complex was intact.  We have now added this data in Figure 6 B,C and Fig. S3C, as discussed above. 

Page 5, top, this sentence is confusing: "their surface area (~17 x 10 nm²) remains significantly less than that required for the average 100 nm diameter CCV (~3.2 x 103 nm²)."

Thank you for the criticism. We have clarified the sentence and corrected a typo, which would definitely be confusing.  The section now reads,  “While the flat CCSs we detected in CCDC32 knockdown cells were significantly larger than in control cells (Fig. 4D, mean diameter of 147 nm vs. 127 nm, respectively), they are much smaller than typical long-lived flat clathrin lattices (d≥300 nm)(Grove et al., 2014). Indeed, the surface area of the flat CCSs that accumulate in CCDC32 KD cells (mean ~1.69 x 10⁴ nm²) remains significantly less than the surface area of an average 100 nm diameter CCV (~3.14 x 10⁴ nm²). Thus, we refer to these structures as ‘flat clathrin assemblies’ because they are neither curved ‘pits’ nor large ‘lattices’. Rather, the flat clathrin assemblies represent early, likely defective, intermediates in CCP formation.” 

Significance

Overall, while this work presents some interesting ideas, it remains unclear whether CCDC32 regulates AP2 beyond the assembly step.

Our responses above argue that we have indeed established that CCDC32 regulates AP2 beyond the assembly step. We have also identified several discrepancies between our findings and those reported by Wan et al., most notably binding between CCDC32 and mature AP2 complexes and the AP2-dependent recruitment of CCDC32 to CCPs.  It is possible that these discrepancies may be due to the position of the GFP tag (ours is N-terminal, theirs is C-terminal; we show that the N-terminal tagged CCDC32 rescues the knockdown phenotype, while Wan et al., do not provide evidence for functionality of the C-terminal construct). 

Reviewer #3: 

Evidence, reproducibility and clarity (Required): 

In this manuscript, Yang et al. characterize the endocytic accessory protein CCDC32, which has implications in cardio-facio-neuro-developmental syndrome (CFNDS). The authors clearly demonstrate that the protein CCDC32 has a role in the early stages of endocytosis, mainly through the interaction with the major endocytic adaptor protein AP2, and they identify regions taking part in this recognition. Through live cell fluorescence imaging and electron microscopy of endocytic pits, the authors characterize the lifetimes of endocytic sites, the formation rate of endocytic sites and pits and the invagination depth, in addition to transferrin receptor (TfnR) uptake experiments. Binding between CCDC32 and CCDC32 mutants to the AP2 alpha appendage domain is assessed by pull down experiments. Together, these experiments allow deriving a phenotype of CCDC32 knock-down and CCDC32 mutants within endocytosis, which is a very robust system, in which defects are not so easily detected. A mutation of CCDC32, known to play a role in CFNDS, is also addressed in this study and shown to have endocytic defects.

We thank the reviewer for their positive remarks regarding the quality of our data and the strength of our conclusions.  

In summary, the authors present a strong combination of techniques, assessing the impact of CCDC32 in clathrin mediated endocytosis and its binding to AP2, whereby the following major and minor points remain to be addressed: 

- The authors show that CCDC32 depletion leads to the formation of brighter and static clathrin coated structures (Figure 2), but that these were only prevalent to 7.8% and masked the 'normal' dynamic CCPs. At the same time, the authors show that the absence of CCDC32 induces pits with shorter life times (Figure 1 and Figure 2), the 'majority' of the pits.

Clarification is needed as to how the authors arrive at these conclusions and these numbers. The authors should also provide (and visualize) the corresponding statistics. The same statement is made again later on in the manuscript, where the authors explain their electron microscopy data. Was the number derived from there? 

These points are critical to understanding CCDC32's role in endocytosis and is key to understanding the model presented in Figure 8. The numbers of how many pits accumulate in flat lattices versus normal endocytosis progression and the actual time scales could be included in this model and would make the figure much stronger. 

Thank you for these comments.  We understand the paradox between the visual impression and the reality of our dynamic measurements. We have been visually misled by this in previous work (Chen et al., 2020), which emphasizes the importance of unbiased image analysis afforded to us through the well-documented cmeAnalysis pipeline, developed by us (Aguet et al., 2013) and now used by many others (e.g. (He et al., 2020)). 

The % of static structures was not derived from electron microscopy data, but quantified using cmeAnalysis, which automatedly provides the lifetime distribution of CCPs. We have now clarified this in the manuscript and added a histogram (Fig. S4) quantifying the fraction of CCPs in lifetime cohorts  <20s, 21-60s, 61-100s, 101-150s and >150s (static). 

- In relation to the above point, the statistics of Figure 2E-G and the analysis leading there should also be explained in more detail: For example, what are the individual points in the plot (also in Figures 6G and 7G)? The authors should also use a few phrases to explain software they use, for example DASC, in the main text. 

Each point in these bar graphs represents a movie, where n≥12. These details have been added to the respective figure legend. We have also added a brief description of DASC analysis in the text. 

-  There are several questions related to the knock-down experiments that need to be addressed:

Firstly, knock-down of CCDC32 does not seem to be very strong (Figure S2B). Can the level of knock-down be quantified? 

We have now quantified the KD efficiency. It is ~60%. This turns out to be fortuitous (see responses to reviewer 2), as a recent publication, which came out after we completed our study, has shown by CRISPR-mediated knockout, that CCD32 also plays an essential chaperone function required for AP2 assembly.  We do not see any reduction in AP2 levels or its complex formation under our conditions (see new Supplemental Figure S3), which suggests that the effects of CCDC32 on CCP dynamics are more sensitive to CCDC32 concentration than its roles as a chaperone. Our phenotypes would have been masked by more efficient depletion of CCDC32.  

In page 6 it is indicated that the eGFP-CCDC32(1-54) and eGFP-CCDC32(∆78-98) constructs are siRNA-resistant. However in Fig S2B, these proteins do not show any signal in the western blot, so it is not clear if they are expressed or simply not detected by the antibody. The presence of these proteins after silencing endogenous CCDC32 needs to be confirmed to support Figures 6 and Figures 7, which critically rely on the presence of the CCDC32 mutants. 

Unfortunately, the C-terminally truncated CCDC32 proteins are not detected because they lack the antibody epitope, indeed even the ∆78-98 deletion is poorly detected (compare the GFP blot in new S1A with the anti-CCDC32 blot in S1B).  However, these constructs contain the same siRNA-resistance mutation as the full length protein. That they are expressed and siRNA resistant can be seen in Fig. S2A (now Fig. S1A) blotting for GFP.

In Figures 6 and 7, siRNA knock-down of CCDC32 is only indicated for sub-figures F to G. Is this really the case? If not, the authors should clarify. The siRNA knock-down in Figure 1 is also only mentioned in the text, not in the figure legend. The authors should pay attention to make their figure legends easy to understand and unambiguous. 

No, it is not the case.  Thank you for pointing out the uncertainty. We have added these details to the Figure legends and checked all Figure legends to ensure that they clearly describe the data shown.  

- It is not exactly clear how the curves in Figure 3C (lower panel) on the invagination depth were obtained. Can the authors clarify this a bit more? For example, what are kT and kE in Figure 3A? What is I0? And how did the authors derive the logarithmic function used to quantify the invagination depth? In the main text, the authors say that the traces were 'logarithmically transformed'. This is not a technical term. The authors should refer to the actual equation used in the figure. 

This analysis was developed by the Kirchhausen lab (Saffarian and Kirchhausen, 2008). We have added these details and reference them in the Figure legend and in the text. We also now use the more accurate descriptor ‘log-transformed’.

- In the discussion, the claim 'The resulting dysregulation of AP2 inhibits CME, which further results in the development of CFNDS.' is maybe a bit too strong of a statement. Firstly, because the authors show themselves that CME is perturbed, but by no means inhibited. Secondly, the molecular link to CFNDS remains unclear. Even though CCDC32 mutants seem to be responsible for CFNDS and one of the mutant has been shown in this study to have a defect in endocytosis and AP2 binding, a direct link between CCDC32's function in endocytosis and CFNDS remains elusive. The authors should thus provide a more balanced discussion on this topic. 

We have modified and softened our conclusions, which now read that the phenotypes we see likely “contribute to” rather than “cause” the disease.

- In Figure S1, the authors annotate the presence of a coiled-coil domain, which they also use later on in the manuscript to generate mutations. Could the authors specify (and cite) where and how this coiled-coil domain has been identified? Is this predicted helix indeed a coiled-coil domain, or just a helix, as indicated by the authors in the discussion?

See response to Reviewer 1, point 4.  We have changed this wording to alpha-helix. The ‘coiled-coil’ reference is historical and unlikely a true reflection of CCDC32 structure. AlphaFold 3.0 predictions were unable to identify with certainly any coiled-coil structures, even if we modelled potential dimers or trimers; and we find no evidence of dimerization of CCDC32 in vivo. We have clarified this in the text.

Minor comments

- In general, a more detailed explanation of the microscopy techniques used and the information they report would be beneficial to provide access to the article also to non-expert readers in the field. This concerns particularly the analysis methods used, for example: 

How were the cohort-averaged fluorescence intensity and lifetime traces obtained? 

How do the tools cmeAnalysis and DASC work? A brief explanation would be helpful. 

We have expanded Methods to add these details, and also described them in the main text. 

- The axis label of Figure 2B is not quite clear. What does 'TfnR uptake % of surface bound' mean? Maybe the authors could explain this in more detail in the figure legend? Is the drop in uptake efficiency also accessible by visual inspection of the images? It would be interesting to see that. 

This is a standard measure of CME efficiency. 'TfnR uptake % of surface bound' = Internalized TfnR/Surface bound TfnR. Again, images may be misleading as defects in CME lead to increased levels of TfnR on the cell surface, which in turn would result in more Tfn uptake even if the rate of CME is decreased.

- Figure 4: How is the occupancy of CCPs in the plasma membrane measured? What are the criteria used to divide CCSs into Flat, Dome or Sphere categories? 

We have expanded Methods to add these details. Based on the degree of invagination, the shapes of CCSs were classified as either: flat CCSs with no obvious invagination; dome-shaped CCSs that had a hemispherical or less invaginated shape with visible edges of the clathrin lattice; and spherical CCSs that had a round shape with the invisible edges of clathrin lattice in 2D projection images. In most cases, the shapes were obvious in 2D PREM images. In uncertain cases, the degree of CCS invagination was determined using images tilted at ±10–20 degrees. The area of CCSs were measured using ImageJ and used for the calculation of the CCS occupancy on the plasma membrane.

- Figure 5B: Can the authors explain, where exactly the GFP was engineered into AP2 alpha? This construct does not seem to be explained in the methods section. 

We have added this information. The construct, which corresponds to an insertion of GFP into the flexible hinge region of AP2, at aa649, was first described by (Mino et al., 2020) and shown to be fully functional.  This information has been added to the Methods section.

- Figure S1B: The authors should indicate the colour code used for the structural model.

We have expanded our structural modeling using AlphaFold 3.0 in light of the recent publication suggesting the CCDC32 interacts with the µ2 subunit and does not bind full length AP2. These results are described in the text. The color coding now reflects certainty values given by AlphaFold 3.0 (Fig. S6B, D). 

- The list of primers referred to in the materials and methods section does not exist. There is a Table S1, but this contains different data. The actual Table S1 is not referenced in the main text. This should be done. 

We apologize for this error. We have now added this information in Table S2.

Significance (Required):

In this study, the authors analyse a so-far poorly understood endocytic accessory protein, CCDC32, and its implication for endocytosis. The experimental tool set used, allowing to quantify CCP dynamics and invagination is clearly a strength of the article that allows assessing the impact of an accessory protein towards the endocytic uptake mechanism, which is normally very robust towards mutations. Only through this detailed analysis of endocytosis progression could the authors detect clear differences in the presence and absence of CCDC32 and its mutants. If the above points are successfully addressed, the study will provide very interesting and highly relevant work allowing a better understanding of the early phases in CME with implication for disease. 

The study is thus of potential interest to an audience interested in CME, in disease and its molecular reasons, as well as for readers interested in intrinsically disordered proteins to a certain extent, claiming thus a relatively broad audience. The presented results may initiate further studies of the so-far poorly understood and less well known accessory protein CCDC32.

We thank the reviewer for their positive comments on the significance of our findings and the importance of our detailed phenotypic analysis made possible by quantitative live cell microscopy. We also believe that our new structural modeling of CCDC32 and our findings of complex and extensive interactions with AP2 make the reviewers point regarding intrinsically disordered proteins even more interesting and relevant to a broad audience.  We trust that our revisions indeed address the reviewer’s concerns. 

The field of expertise of the reviewer is structural biology, biochemistry and clathrin mediated endocytosis. Expertise in cell biology is rather superficial.

References:

Aguet, F., Costin N. Antonescu, M. Mettlen, Sandra L. Schmid, and G. Danuser. 2013. Advances in Analysis of Low Signal-to-Noise Images Link Dynamin and AP2 to the Functions of an Endocytic Checkpoint. Developmental Cell. 26:279-291.

Chen, Z., R.E. Mino, M. Mettlen, P. Michaely, M. Bhave, D.K. Reed, and S.L. Schmid. 2020. Wbox2: A clathrin terminal domain–derived peptide inhibitor of clathrin-mediated endocytosis. Journal of Cell Biology. 219.

Grove, J., D.J. Metcalf, A.E. Knight, S.T. Wavre-Shapton, T. Sun, E.D. Protonotarios, L.D. Griffin, J. Lippincott-Schwartz, and M. Marsh. 2014. Flat clathrin lattices: stable features of the plasma membrane. Mol Biol Cell. 25:3581-3594.

He, K., E. Song, S. Upadhyayula, S. Dang, R. Gaudin, W. Skillern, K. Bu, B.R. Capraro, I. Rapoport, I. Kusters, M. Ma, and T. Kirchhausen. 2020. Dynamics of Auxilin 1 and GAK in clathrinmediated traffic. J Cell Biol. 219.

Mino, R.E., Z. Chen, M. Mettlen, and S.L. Schmid. 2020. An internally eGFP-tagged α-adaptin is a fully functional and improved fiduciary marker for clathrin-coated pit dynamics. Traffic. 21:603-616.

Saffarian, S., and T. Kirchhausen. 2008. Differential evanescence nanometry: live-cell fluorescence measurements with 10-nm axial resolution on the plasma membrane. Biophys J. 94:23332342.

Author response:

Reviewer #1 (Evidence, reproducibility and clarity):

Minor comments:

In the results section (lines 498-499), the authors describe free kinetochores in many cells without associated spindle microtubules. However, some nuclei appear to have kinetochores, as presented in Figure 6. Could the authors clarify how this conclusion was derived using transmission electron microscopy (TEM) without serial sectioning, as this is not explicitly mentioned in the materials and methods?

We observed free kinetochores in the ALLAN-KO parasites with no associated spindle microtubules (see Fig. 6Gh), while kinetochores are attached to spindle microtubules in WT-GFP cells (see Fig. 6Gc). To provide further evidence we analysed additional images and found that ALLAN-KO cells have free kinetochores in the centre of nucleus, unattached to spindle microtubules. We provide some more images clearly showing free kinetochores in these cells (new supplementary Fig. S11).

However, in the ALLAN mutant, this difference is not absolute: in a search of over 50 cells, one example of a cell with a “normal” nuclear spindle and attached kinetochores was observed.

The use of serial sectioning has limitations for examining small structures like kinetochores in whole cells. The limitations of the various techniques (for example, SBF-SEM vs tomography) are highlighted in our previous study (Hair et al 2022; PMID: 38092766), and we consider that examining a population of randomly sectioned cells provides a better understanding of the overall incidence of specific features.

Discussion Section:

Could the authors expand on why SUN1 and ALLAN are not required during asexual replication, even though they play essential roles during male gametogenesis?

We observed no phenotype in asexual blood stage parasites associated with the sun1 and allan gene deletions. Several other Plasmodium berghei gene knockout parasites with a phenotype in sexual stages, for example CDPK4 (PMID: 15137943), SRPK (PMID: 20951971), PPKL (PMID: 23028336) and kinesin-5 (PMID: 33154955) have no phenotype in blood stages, so perhaps this is not surprising. One explanation may be the substantial differences in the mode of cell division between these two stages. Asexual blood stages produce new progeny (merozoites) over 24 hours with closed mitosis and asynchronous karyokinesis during schizogony, while male gametogenesis is a rapid process, completed within 15 min to produce eight flagellated gametes. During male gametogenesis the nuclear envelope must expand to accommodate the increased DNA content (from 1N to 8N) before cytokinesis. Furthermore, male gametogenesis is the only stage of the life cycle to make flagella, and axonemes must be assembled in the cytoplasm to produce the flagellated motile male gametes at the end of the process. Thus, these two stages of parasite development have some very different and specific features.

Lines 611-613 states: "These loops serve as structural hubs for spindle assembly and kinetochore attachment at the nuclear MTOC, separating nuclear and cytoplasmic compartments." Could the authors elaborate on the evidence supporting this statement?

We observed the loops/folds in the nuclear envelope (NE) as revealed by SUN1-GFP and 3D TEM images during male gametogenesis. These folds/loops occur mainly in the vicinity of the nuclear MTOC where the spindles are assembled (as visualised by EB1 fluorescence) and attached to kinetochores (as visualised by NDC80 fluorescence). These loops/folds may form due to the contraction of the spindle pole back to the nuclear periphery, inducing distortion of the NE. Since there is no physical segregation of chromosomes during the three rounds of mitosis (DNA increasing from 1N to 8N), we suggest that these folds provide additional space for spindle and kinetochore dynamics within an intact NE to maintain separation from the cytoplasm (as shown by location of kinesin-8B).

In lines 621-622, the authors suggest that ALLAN may have a broader role in NE remodelling across the parasite's lifecycle. Could they reflect on or remind readers of the finding that ALLAN is not essential during the asexual stage?

ALLAN-GFP is expressed throughout the parasite life cycle but as the reviewer points out, a functional role is more pronounced during male gametogenesis. This does not mean that it has no role at other stages of the life cycle even if there is no obvious phenotype following deletion of the gene during the asexual blood stage. The fact that ALLAN is not essential during the asexual blood stage is noted in lines 628-29.

Reviewer #2 (Evidence, reproducibility and clarity):

Introduction

Line 63: The authors stat: "NE is integral to mitosis, supporting spindle formation, kinetochore attachment, and chromosome segregation..". Seemingly at odds, they also say (Line 69) that 'open' "mitosis is "characterized by complete NE disassembly".

The authors could explain better the ideas presented in their quoted review from Dey and Baum, which points out that truly 'open' and 'closed' topologies may not exist and that even in 'open' mitosis, remnants of the NE may help support the mitotic spindle.

We have modified the sentence in which we discuss current opinions about ‘open’ and ‘closed’ mitosis. It is believed that there is no complete disassembly of the NE during open mitosis and no completely intact NE during closed mitosis, respectively. In fact, the NE plays a critical role in the different modes of mitosis during MTOC organisation and spindle dynamics. Please see the modified lines 64-71.

Results

Fig 7 is the final figure; but would be more useful upfront.

We have provided a new introductory figure (Fig 1) showing a schematic of conventional /canonical LINC complexes and evidence of SUN protein functions in model eukaryotes and compare them to what is known in apicomplexans.

Fig 1D. The authors generated a C-terminal GFP-tagged SUN1 transfectants and used ultrastructure expansion microscopy (U-ExM) and structured illumination microscopy (SIM) to examine SUN1-GFP in male gametocytes post-activation. The immuno-labelling of SUN1-GFP in these fixed cells appears very different to the live cell images of SUN1-GFP. The labelling profile comprises distinct punctate structures (particularly in the U-ExM images), suggesting that paraformaldehyde fixation process, followed by the addition of the primary and secondary antibodies has caused coalescing of the SUN1-GFP signal into particular regions within the NE.

We agree with the reviewer. Fixation with paraformaldehyde (PFA) results in a coalescence of the SUN1-GFP signal. We have also tried methanol fixation (see new Fig. S2), but a similar problem was encountered.

Given these fixation issues, the suggestion that the SUN1-GFP signal is concentrated at the BB/ nuclear MTOC and "enriched near spindle poles" needs further support.

These statements seem at odd with the data for live cell imaging where the SUN1-GFP seems evenly distributed around the nuclear periphery. Can the observation be quantitated by calculating the percentage of BB/ nuclear MTOC structures with associated SUN1-GFP puncta? If not, I am not convinced these data help understand the molecular events.

We agree with the reviewer that whilst the live cell imaging showed an even distribution of SUN1-GFP signal, after fixation with either PFA or methanol, then SUN1-GFP puncta are observed in addition to the peripheral location around the stained DNA (Hoechst) (See Fig. S2; puncta are indicated by arrows). These SUN1-GFP labelled puncta were observed at the junction of the nuclear MTOC and the basal body (Fig. 2F). Quantification of the distribution showed that these SUN1-GFP puncta are associated with nuclear MTOC in more than 90 % of cells (18 cells examined). Live cell imaging of the dual labelled parasites; SUN1xkinesin-8B (Fig. 2H) and SUN1x EB1 (Fig. 2I) provides further support for the association of SUN1-GFP puncta with BB (kinesin-8B) /nuclear MTOC (EB1).

The authors then generated dual transfectants and examined the relative locations of different markers in live cells. These data are more informative.

The authors state; " ..SUN1-GFP marked the NE with strong signals located near the nuclear MTOCs situated between the BB tetrads". The nuclear MTOCs are not labelled in this experiment. The SUN1-GFP signal between the kinesin-8B puncta is evident as small puncta on regions of NE distortion. I would prefer to not describe this signal as "strong". The signal is stronger in other regions of the NE.

We have modified the sentence on line 213 to accommodate this suggestion.

Line 219. The authors state; "..SUN1-GFP is partially colocalized with spindle poles as indicated by EB1,.. it shows no overlap with kinetochores (NDC80)." The authors should provide an analysis of the level of overlap at a pixel by pixel level to support this statement.

We now provide the overlap at a pixel-by-pixel level for representative images, and we have quantified more cells (n>30), as documented in the new Fig. S4A. We have also modified the sentence on line 219 to reflect these additions.

The SUN1 construct is C-terminally GFP-tagged. By analogy with human SUN1, the C-terminal SUN domain is expected to be in the NE lumen. That is in a different compartment to EB1, which is located in the nuclear lumen (on the spindle). Thus, the overlap of signal is expected to be minimal.

We agree with the reviewer that the overlap between EB1 and Sun1 signals is expected to be minimal. We have quantified the data and included it in Supplementary Fig. S4A.

Similarly, given that EB1 and NDC80 are known to occupy overlapping locations on the spindle, it seems unlikely that SUN1 can overlap with one and not the other.

We agree with the reviewer’s analysis that EB1 and NDC80 occupy overlapping locations on the spindle, although the length of NDC80 is less at the ends of spindles (see Author response image 1A) as shown in our previous study where we compared the locations of two spindle proteins, ARK2 and EB1, with that of NDC80 (Zeeshan et al, 2022; PMID: 37704606). In the present study we observed that Sun1-GFP partially overlaps with EB1 at the ends of the spindle, but not with NDC80. Please see Author response image 1B.

Author response image 1.

I note on Line 609, the authors state "Our study demonstrates that SUN1 is primarily localized to the nuclear side of the NE.." As per Fig 7D, and as discussed above, the bulk of the protein, including the SUN1 domain, is located in the space between the INM and the ONM.

We appreciate the reviewer’s correction; we have now modified the sentence to indicate that the protein is largely localized in the space between the INM and the ONM on line 617.

Interestingly, as the authors point out, nuclear membrane loops are evident around EB1 and NDC80 focal regions. The data suggests that the contraction of the spindle pole back to the nuclear periphery induces distortion of the NE.

We agree with the reviewer’s suggestion that the data indicate that contraction of spindle poles back to the nuclear periphery may induce distortion of the NE.

The author should discuss further the overlap of findings of this study with that from a recent manuscript (https://doi.org/10.1016/j.cels.2024.10.008). That Sayers et al. study identified a complex of SUN1 and ALLC1 as essential for male fertility in P. berghei. Sayers et al. also provide evidence that this complex particulate in the linkage of the MTOC to the NE and is needed for correct mitotic spindle formation during male gametogenesis.

We thank the reviewer for this suggestion. The study by Sayers et al, (2024) was published while our manuscript was under preparation. It was interesting to see that these complementary studies have similar findings about the role of SUN1 and the novel complex of SUN1-ALLAN. Our study contains a more detailed, in-depth analysis both by Expansion and TEM of SUN1. We include additional studies on the role of ALLAN.  We discuss the overlap in the findings of the two studies in lines 590-605.

While the work is interesting, the conclusions may need to be tempered. The authors suggestion that in the absence of KASH-domain proteins, the SUN1-ALLAN complex forms a non-canonical LINC complex (that is, a connection across the NE), that "achieves precise nuclear and cytoskeletal coordination".

We have toned down the wording of this conclusion in lines 665-677.

In other organisms, KASH interacts with the C-terminal domain on SUN1, which as mentioned above is located between the INM and ONM. By contrast, ALLAN interacts with the N-terminal domain of SUN1, which is located in the nuclear lumen. The SUN1-ALLAN interaction is clearly of interest, and ALLAN might replace some of the roles of lamins. However, the protein that functionally replaces KASH (i.e. links SUN1 to the ONM) remains unidentified.

We agree with reviewer, and future studies will need to focus on identifying the KASH replacement that links SUN1 to the ONM.

It may also be premature to suggest that the SUN1-ALLAN complex is promising target for blocking malaria transmission. How would it be targeted?

We have deleted the sentence that raised this suggestion.

While the above datasets are interesting and internally consistent, there are two other aspects of the manuscript that need further development before they can usefully contribute to the molecular story.

The authors undertook a transcriptomic analysis of Δsun1 and WT gametocytes, at 8 and 30 min post-activation, revealing moderate changes (~2-fold change) in different genes. GO-based analysis suggested up-regulation of genes involved in lipid metabolism. Given the modest changes, it may not be correct to conclude that "lipid metabolism and microtubule function may be critical functions for gametogenesis that can be perturbed by sun1 deletion." These changes may simply be a consequence of the stalled male gametocyte development.

Following the reviewer’s suggestion we have moved these data to the supplementary information (Fig. S5D-I) and toned down their discussion in the results and discussion sections.

The authors have then undertaken a detailed lipid analysis of the Δsun1 and WT gametocytes, before and after activation. Substantial changes in lipid metabolites might not be expected in such a short period of time. And indeed, the changes appear minimal. Similarly, there are only minor changes in a few lipid sub-classes between Δsun1 and WT gametocytes. In my opinion, the data are not sufficient to support the authors conclusion that "SUN1 plays a crucial role, linking lipid metabolism to NE remodelling and gamete formation."

In agreement with the reviewer’s comments we have moved  these data to supplementary information (Fig. S6) and substantially toned down the conclusions based on these findings.

Reviewer #3 (Evidence, reproducibility and clarity):

Major comments:

My main concern with this manuscript is that the authors do conclude not only that SUN1 is important for spindle formation and basal body segregation, but also that it influences for lipid metabolism and NE dynamics. I don't think the data supports this conclusion, for several reasons listed below. I would suggest to remove this claim from the manuscript or at least tone it down unless more supporting data are provided, in particular showing any change in NE dynamics in the SUN1-KO. Instead I would recommend to focus on the more interesting role of SUN1-ALLAN in bipartite MTOC organisation, which likely explains all observed phenotypes (including those in later stages of the parasite life cycle). In addition, some aspects of the knockout phenotype should be quantified to a bit deeper level.

In more detail:

- The lipidomics analysis is clearly the weakest point of the manuscript: The authors state that there are significant changes in some lipid populations between WT and sun1-KO, and between activated and non-activated cells, yet no statistical analysis is shown and the error bars are quite high compared to only minor changes in the means. For some discussed lipids, the result text does not match the graphs, e.g. PA, where the increase upon activation is more pronounced in the SUN1-KO vs WT (contrary to the text), or MAG, which is reduced in the SUN1-KO vs WT (contrary to the text). I don't see the discussed changes in arachidonic acid levels and myristic acid levels in the data either. Even if the authors find after analysis some statistically significant differences between some groups, they should carefully discuss the biological significance of these differences. As it is, I do not think the presented data warrants the conclusion that deletion of SUN1 changes lipid homeostasis, but rather shows that overall lipid homeostasis is not majorly affected by gametogenesis or SUN1 deletion. As a minor comment, if you decide to keep the lipidomics analysis in the manuscript, please state how many replicates were done.

As detailed above we have moved the lipidomics data to supplementary information (Fig. S6) and substantially toned down the discussion of these data in the results and discussion sections.

- I can't quite follow the logic why the authors performed transcriptomic analysis of the SUN1 and how they chose their time points. Their data up to this point indicate that SUN1 has a structural or coordinating role in the bipartite MTOC during male gametogenesis. Based on that it is rather unlikely that SUN1 KO directly leads to transcriptional changes within the 8 min of exflagellation. Isn't it more likely that transcriptional differences are purely a downstream effect of incomplete/failed gametogenesis? This is particularly true for the comparison at 30 min, which compares a mixture of exflagellated/emerged gametes and zygotes in WT to a mixture of aberrant, arrested gametes in the knockout, which will likely not give any meaningful insight. The by far most significant GO-term is then also nuclear-transcribed mRNA catabolic process, which is likely not related at all to SUN1 function (and the authors do not even comment on this in the main text). I would therefore suggest removing the 30 min data set from this manuscript. As a minor point, I would suggest highlighting some of the top de-regulated gene IDs in the volcano plots and stating their function. Also, please state how you prepared the cells for the transcriptomes and in how many replicates this was done.

As suggested by the reviewer we have removed the 30 min post activation data from the manuscript. We have also moved the rest of the transcriptomics data to supplementary information (Fig. S5) and toned down the presentation of this aspect of the work in the results and discussion sections.

- Live-cell imaging of SUN1-GFP does nicely visualise the NE during gametogenesis, showing a highly dynamic NE forming loops and folds, which is very exciting to see. It would be beneficial to also show a video from the life-cell imaging.

We have now added videos to the manuscript as suggested by the reviewer. Please see the supplementary Videos S1 and S2.

In their discussion, the authors state multiple times that NE dynamics are changed upon SUN1 KO. Yet, they do not provide data supporting this claim, i.e. that the extended loops and folds found in the nuclear envelope during gametogenesis are affected in any way by the knockout of SUN1 or ALLAN. What happens to the NE in absence of SUN1? Are there less loops and folds? In absence of a reliable NE marker this may not be entirely easy to address, but at least some SBF-SEM images of the sun1-KO gametocytes could provide insight.

It was difficult to provide SBF-SEM images as that work is beyond the scope of this manuscript. We will consider this approach in our future work. We re-examined many of our TEM images of SUN1-KO and ALLAN-KO parasites and did find some micrographs showing aberrant nuclear membrane folding (<5%) (Please see Author response image 2). However, we also observed similar structures in some of the WT-GFP samples (<5%), so we do not think this is a strong phenotype of the SUN1 or ALLAN mutants.

Author response image 2.

- I think the exciting part of the manuscript is the cell biological role of SUN1 on male gametogenesis, which could be carved out a bit more by a more detailed phenotyping. Specifically it would be good to quantify

(1) If DNA replication to an octoploid state still occurs in SUN1-KO and ALLAN-KO,

DNA replication is not affected in the SUN1-KO and ALLAN-KO mutants: DNA content increases to 8N (data added in Fig. 3J and Fig. S10F).

(2) The proportion of anucleated gametes in WT and the KO lines

We have added these data in Fig. 3K and Fig. S10G

(3) A quantification of the BB clustering phenotype (in which proportion of cells do the authors see this phenotype). This could be addressed by simple fixed immunofluorescence images of the respective WT/KO lines at various time points after activation (or possibly by reanalysis of the already obtained images) and would really improve the manuscript.

We have reanalysed the BB clustering phenotype and added the quantitative data in Fig. 4E and Fig. S7.

Especially the claim that emerged SUN1-KO gametes lack a nucleus is currently only based on single slices of few TEM cells and would benefit from a more thorough quantification in both SUN1- and ALLAN-Kos

We have examined many microgametes (100+ sections). In WT parasites a small proportion of gametes can appear to lack a nucleus if it does not extend all the way to the apical and basal ends (Hair et al. 2022). However, the proportion of microgametes that appear to lack a nucleus (no nucleus seen in any section) was much higher in the SUN1 mutant. In contrast, this difference was not as clear cut in the ALLAN mutant with a small proportion of intact (with axoneme and nucleus) microgametes being observed.

We have done additional analysis of male gametes, looking for the presence of the nucleus by live cell imaging after DNA staining with Hoechst. These data are added in Fig. 3K (for Sun1-KO) and Fig. S10G (for Allan-KO).

- The TEM suggests that in the SUN1-KO, kinetochores are free in the nucleus. Are all kinetochores free or do some still associate to a (minor/incorrectly formed) spindle? The authors could address this by tagging NDC80 in the KO lines.

Our observation and quantification of the data indicated that 100% of kinetochores were attached to spindle microtubules and that 0% were unattached kinetochores in the WT parasites. However, the exact opposite was found for the SUN1 mutant with 100% unattached kinetochores and 0% attached. The result was not quite as clear cut in the ALLAN mutant, with 98% unattached and 2% attached. An important observation was the lack of separation of the nuclear poles and any spindle formation. Spindle formation was never or very rarely observed in the mutants.

- Finally, I think it is curious that in contrast to SUN1, ALLAN seems to be less important, with some KO parasite completing the life cycle. Maybe a more detailed phenotyping as above gives some more hints to where the phenotypic difference between the two proteins lies. I would assume some ALLAN-KO cells can still segregate the basal body. Can the authors speculate/discuss in more detail why these two proteins seems to have slightly different phenotypes?

We agree with the reviewer. Overall, the ALLAN-KO has a less prominent phenotype than that of the Sun1-KO. The main difference is that in the ALLAN-KO mutant some basal body segregation can occur, leading to the production of some fertile microgametocytes, and ookinetes, and oocyst formation (Fig. 8). Approximately 5% of oocysts sporulated to release infective sporozoites that could infect mice in bite back experiments and complete the life cycle. In contrast the Sun1-KO mutant made no healthy oocysts, or infective sporozoites, and could not complete the life cycle in bite back experiments. We have analysed the phenotype in detail and provide quantitative data for gametocyte stages by EM and ExM in Figs. 4 and S8 (SUN1) and Figs. 7 and S11 (ALLAN). We have also performed detailed analysis of oocyst and sporozoite stages and included the data in Fig. 3 (SUN1) and S10 (ALLAN).

Based on the location, and functional and interactome data, we think that SUN1 plays a central role in coordinating nucleoplasm and cytoplasmic events as a key component of the nuclear membrane lumen, whereas ALLAN is located in the nucleoplasm. Deleting the SUN1 gene may disrupt the connection between INM and ONM whereas the deletion of ALLAN may affect only the INM.

Some additional points where the data is not entirely sound yet or could be improved:

- Localisation of SUN1: There seems to be a discrepancy between SUN1-GFP location as observed by live cell microscopy, and by Expansion Microscopy (ExM), similar for ALLAN-GFP. By live-cell microscopy, the SUN1 localisation is much more evenly distributed around the NE, while the localisation in ExM is much more punctuated, and e.g. in Figure 1E seems to be within the nucleus. Do the authors have an explanation for this? Also, in Fig. 1D there are two GFP foci at the cell periphery (bottom left of the image), which I would think are not SUN1-Foci, as they seem to be outside of the cell. Is the antibody specific? Was there a negative control done for the antibody (WT cells stained with GFP antibodies after ExM)?

High resolution SIM and expansion microscopy showed that the SUN1-GFP molecules coalesce to form puncta, in contrast to the more uniform distribution observed by live cell imaging. This apparent difference may be due to a better resolution that could not be achieved by live cell imaging. We agree with the reviewer that the two green foci are outside of the cell. As a negative control we have used WT-ANKA cells (which contain no GFP) and the anti-GFP antibody, which gave no signal. This confirms the specificity of the antibody (please see the new Fig. S3). 

- The authors argue that SIM gave unexpected results due to PFA fixation leading to collapse of the NE loops. However, they also fix their ExM cells and their EM cells with PFA and do not observe a collapse, at least from what I see in the two presented images and in the 3D reconstruction. Is there something else different in the sample preparation?

There was no difference in the fixation process for samples examined by SIM and ExM, but we used an anti-GFP antibody in ExM to visualise the SUN1-GFP, while in SIM the images of GFP signal were collected directly after fixation.  We used both PFA and methanol as fixative, and both methods showed a coalescing of the SUN1-GFP signal (please see the new Fig. S2 and S3).

Can the authors trace their NE in ExM according to the NHS-Ester signal?

We could trace the NE in the ExM by the NHS-ester signal and observed that the SUN1-GFP signal was largely coincident with the NE (Please see the new Fig. S3B).

- Fig 2D: It would be good to not just show images of oocysts but actually quantify their size from images. Also, have the authors determined the sporozoite numbers in SUN1-KO?

We have measured oocyst size (data added in new Fig. 3) and added the sporozoite quantification data in Fig. 3D.

- Line 481-483: the authors state that oocyst size is reduced in ALLAN-KO but do not show the data. Please quantify oocyst size or at least show representative images. Also the drastic decrease in sporozoite numbers (Fig. 6D, E) is not mentioned in the text. Please add reference to Fig S7D when talking about the bite back data.

We have added the oocyst size data in Fig. S10. We mention the changes in sporozoite numbers (now  shown in Fig. 7D, E), and refer to  the bite back data shown in current Fig. 7E.

- Fig S1C, 6C: Both WB images are stitched, but this is not clearly indicated e.g. by leaving a small gap between the lanes. Also please show a loading control along with the western blots. Also there seems to be a (unspecific?) band in the control, running at the same height as Allan-GFP WB. What exactly is the control?

We have provided the original blot showing the bands of ALLAN-GFP and SUN1-GFP. As a positive control, we used an RNA associated protein (RAP-GFP) that is highly expressed in Plasmodium and regularly used in our lab for this purpose.

- Regarding the crossing experiment: The authors conclude from this cross that SUN1 is only needed in males, yet for this conclusion they would need to also show that a cross with a female line does not rescue the phenotype. The authors should repeat the cross with a male-deficient line to really test if the phenotype is an exclusively male phenotype. In addition, line 270-272 states that no oocysts/sporozoites were detected in sun1-ko and nek4-ko parasites. However, the figure 2E shows only oocysts, not sporozoites, and shows also that sun1-ko does form oocysts, albeit dead ones.

We have now performed the experiment of crossing the Sun1-KO parasite line with a male deficient line (Hap2-KO) and added the data in Fig. 3I. We have added images showing sporozoites in oocysts.

- In Fig S1 the authors show that they also generated a SUN1-mCherry line, yet they do not use it in any of the presented experiments (unless I missed it). Would it be beneficial to cross the SUN1-mCherry line with the Allan1-GFP line to test colocalisation (possibly also by expansion microscopy)?

We did generate a SUN1-mCherry line, with the intent to cross ALLAN-GFP and SUN1-mCherry lines and observe the co-location of the proteins. Despite multiple attempts this cross was unsuccessful. This may have been due to their close proximity such that the addition of both GFP and mCherry was difficult to facilitate a proper protein-protein interaction between either of the proteins.

- Line 498: "In a significant proportion of cells" - What was the proportion of cells, and what does significant mean in this context?

Approximately 67% of cells showed the clumping of BBs. We have now added the numbers in Figs. 6H and S11I.

- The authors should discuss a bit more how their work relates to the work of Sayers et al. 2024, which also identified the SUN1-ALLAN complex. The paper is cited, but only very briefly commented on.

We have extended this discussion now in lines 590-605.

Suggestions how to improve the writing and data presentation.

- General presentation of microscopy images: Considering that large parts of the manuscript are based on microscopy data, their presentation could be improved. Single-channel microscopy images would benefit from being depicted in gray scale instead of color, which would make it easier to see the structures and intensities (especially for blue channels).

Whilst we agree with the reviewer, sometimes it is difficult to see the features in the merged images. Therefore, we would like to request to be allowed to retain the colours, which can be easily followed in both individual and merged images.

Also, it would be good to harmonize in which panels arrows are shown (e.g. Fig 1G, where some white arrows are in the SUN1-GFP panel, while others are in the merge panel, but they presumably indicate the same thing.). At the same time, Fig 1H doesn't have any with arrows, even though the figure legend states so.

We apologise for this lack of consistency, and we have now added arrows wherever they are missing to harmonise in the presentations.

Fig 3A and S4 show the same experiment but are coloured in different colours (NHS-Eester in green vs grey scale).

- Are the scale bars of all expansion microscopy images adjusted for the expansion factor?

Yes, the scale bars are adjusted accordingly.

- The figure legends would benefit from streamlining, as they have very different style between figures (eg Fig. 6 which has a concise figure legend vs microscopy figures where figure legends are very long and describe not only the figure but the results)

The figure legends have been streamlined, with removal of the description of results.

- Line 155-156: The text makes it sound like the expression only happens after activation. is that the case? Are these images activated or non-activated gametocytes?

They are expressed before activation, but the signal intensifies after activation. Images from before and after activation of gametocytes have been added in Fig. S1F.

- Line 267: Reference to the original nek4-KO paper missing

This reference is now included.

- Line 301: The reference to Figure 2J seems to be a bit arbitrarily placed. Also, this schematic of lipid metabolism is never discussed in relation to the transcriptomic or lipidomic data.

We have moved these data to supplementary information and modified the text.

- Line 347-349 states that gametes emerged, but the referenced figure shows activated gametocytes before exflagellation.

We have corrected the text to the start of exflagellation.

- Line 588: Spelling mistake in SUN1-domain

Corrected.

- Line 726/731: i missing in anti-GFP

Corrected.

- Line 787-789: statement of scale bar and number of cells imaged is not at the right position in the figure legend.

Moved to right place

- Line 779, 783: "shades of green" should be just "green". Same goes for line 986, 989 with "shades of grey"

Changed.

- Line 974, 976: please correct to WT-GFP and dsun1

Corrected.

- Line 1041, 1044: WT-GFP instead of WTGFP.

Corrected to WT-GFP.

- Fig 1B, D, E, Fig S1G, H: What are the time points of imaging?

We have added the time points to the images in these figures.

- Fig 1D/Line 727: the scale of the scale bar on the inset is missing.

We have added the scale bar.

- Fig 3 E-G and 6H-J: Please indicate total number of cells/images analysed per quantification, either in the graphs themselves or in the figure legend.

We indicate now the number of cells analysed in individual figures and also in Fig. S5C and S8C, respectively.

- Fig 5B: What is NP

Nuclear Pole (NP), also known as the nuclear/acentriolar MTOC (Zeeshan et al 2022; PMID: 35550346).

- Fig S1B/D: The legend states that there is an arrow indicating the band, but there is none.

We have added the arrow.

- Fig S2C: Is the scale bar really the same for the zygote and the ookinete?

We have checked this and used the same for both zygote and ookinete.

- Fig S3C, S7C: which stages was qRT-PCR done on?

Gametocytes activated for 8 min.

- Fig. S3D, S7D: According to the figure legend, three independent experiments were performed. How many mice were used per experiment? It would be good to depict the individual data points instead of the bar graph. For S7D, 3 data points are depicted (one in WT, two in allan-KO), what do they mean?

The bite back experiment was performed using 15-20 mosquitoes infected with WT-GFP and gene knockout lines to feed on one naïve mouse each, in three different experiments. We have now included the data points in the bar diagrams.

- Fig S3: Panel letters E and G are missing

We have updated the lettering in current Fig. S5

- Fig 3D: Please indicate what those boxes are. I presume that these are the insets show in b, e and j, but it is never mentioned. J is not even larger than i. Also, f is quite cropped, it would be good to see the large-scale image it comes from to see where in the nucleus these kinetochores are placed. Were there unbound kinetochores found in WT?

We mention the boxes in the figure legends. It is rare to find unbound kinetochores in WT parasite. We provide large scale and zoomed-in images of free kinetochores in Fig. S8.

- Fig S4: Insets are not mentioned in the figure legend. Please add scale bar to zoom-ins

We now describe the insets in the figure legends and have added scale bars to the zoomed-in images.

- Fig S5A, B: Please indicate which inset belongs to which sub-panel. Where does Ac stem from?

We have now included the full image showing the inset (new Fig. S8).

- Fig S5C and S8C: Change "DNA" to "Nucleus".

We have changed “DNA” to “Nucleus”. Now they are Fig. S8K and S11I.

Reviewer #3 (Significance):

Yet, the statement that SUN1 is also important for lipid homoeostasis and NE dynamics is currently not backed up by sufficient data. I believe that the manuscript would benefit from removing the less convincing transcriptomic and lipidomic datasets and rather focus on more deeply characterising the cell biology of the knockouts. This way, the results would be interesting not only for parasitologists, but also for more general cell biologists.

We have moved the lipidomics and transcriptomics data to supplementary information and toned down the emphasis on these data to make the manuscript more focused on the cell biology and analysis of the genetic KO data.

Author response:

We thank the reviewers for recognizing the strengths of our work, as well as for their thoughtful and constructive feedback. In this provisional response, we focus on the main concern raised—namely, the need for stronger evidence that the effect is specific to suicide. A full revision of the manuscript will follow, in which we will address this point in greater depth and respond carefully to all additional comments in a point-by-point manner.

More specifically, reviewer 3 points out that “The main analyses control for illness duration and medication but not for symptom severity. The supplementary analysis in Figure S11 is insufficient as it mistakes the absence of evidence (i.e., p > 0.05) for evidence of absence.”. This is indeed an important point that we address below.

(1) Correction for symptom severity.

To address the request for evidence on specificity to suicidality beyond general symptom severity, we performed separate linear regressions to explain in gambling behaviour, value-insensitive approach parameter (β_gain), and mood sensitivity to certain rewards (β_CR) with group as a predictor (1 for S⁺ group and 0 for S^- group) and scores for anxiety and depression as covariates. Results remained significant after controlling anxiety and depression (ps < 0.027).

Author response table 1.

Given high correlations among anxiety and depression questionnaires (rs > 0.753, ps < 0.001), we performed Principal Components Analysis (PCA) on the clinical questionnaire to extract the orthogonal components, where each component explained 86.95%, 7.09%, 3.27%, and 2.68% variance, respectively. We then performed linear regressions using these components as covariates to control for anxiety and depression. Our main results remained significant (ps < 0.027).

Author response table 2.

We believe that these analyses provide evidence that the main effects on gambling and on mood were specific to suicide.

(2) Evidence of absence of effect of symptom severity

Based on clinical interviews, we included patients with and without suicidality (S⁺ and S^- groups). However, in line with suicidal-related literature (e.g., Tsypes et al., 2024), S⁺ and S^- differed substantially in the severity of symptoms (see Table 1). Although we median-split patients by the scores of general symptoms (e.g., depression and anxiety) and verified no significant differences in these severities (Figure S11), the “absence of evidence” cannot provide insights of “evidence of absence”. We, therefore, additionally conducted Bayesian statistics in gambling behavior, value-insensitive approach parameter, and mood sensitivity to certain rewards. BF₀₁ is a Bayes factor comparing the null model (M₀) to the alternative model (M₁), where M₀ assumes no group difference. BF₀₁ > 1 indicates that evidence favors M₀. As can be seen below, most results supported null hypothesis, suggesting that general symptoms of anxiety and depression overall did not influence our main results.

Author response table 3.

Overall, we believe that these analyses provide compelling evidence for the specificity of the effect to suicide, above and beyond depression and anxiety.

Author Response

eLife assessment

This paper by Aitchison and colleagues describes nanobody neutralizing and binding activity against various SARS-CoV-2 variants of concern. The findings are important in that the described nanobodies may have broad therapeutic relevance against current and future variants of concern and may be able to avoid significant resistance. The claims are incomplete: while the study is well-executed and uses a nice balance of biochemical and cellular assays, the efficacy of the proposed nanobody library against VOCs is not completely supported as IC50 values appear to increase against newer variants and are higher than previously used therapeutic bNAbs, animal data showing in vivo efficacy is lacking, and protection against future possible variants is not proven.

This manuscript is a follow-up of our previous eLife manuscript “Highly synergistic combinations of nanobodies that target SARS-CoV-2 and are resistant to escape” https://elifesciences.org/articles/73027 where we described an “impressive collection of hundreds of new nanobodies binding SARS-CoV-2 spike by combining in vivo antibody affinity maturation and proteomics. [Editor’s evaluation]”. As a follow-up this submission extends the findings of our previous eLife publication and thus focuses on how our repertoire functions in the context of a rapidly evolving SARS-CoV-2 virus, relying on the established methodologies and approaches of the original paper. We explore how nanobody functions have been influenced by the emergence of SARS-CoV-2 variants containing extensive mutations in spike protein, which largely reduced the usefulness of therapeutic monoclonal antibody therapeutics. Our findings show that while some nanobodies lost efficacy in binding to and neutralizing these evolved spikes, a surprising number of nanobodies retained their binding and neutralization activity. This is an important finding, because these efficacious nanobodies target regions that appear rarely targetable by monoclonal antibodies. We also provide experimental validation of the importance of the interplay between binding and neutralization in synergy experiments, where even weakened binding still contributed to strongly enhancing the neutralization.

Reviewer #1 (Public Review):

Summary:

In this manuscript, Ketaren, Mast, Fridy et al. assessed the ability of a previously generated llama nanobody library (Mast, Fridy et al. 2021) to bind and neutralize SARS-CoV-2 delta and omicron variants. The authors identified multiple nanobodies that retain neutralizing and/or binding capacity against delta, BA.1 and BA.4/5. Nanobody epitope mapping on spike proteins using structural modeling revealed possible mechanisms of immune evasion by viral variants as well as mechanisms of cross-variant neutralization by nanobodies. The authors additionally identified two nanobody pairs involving non-neutralizing nanobodies that exhibited synergy in neutralization against the delta variant. These results enabled the refinement of target epitopes of the nanobody repertoire and the discovery of several pan-variant nanobodies for further preclinical development.

Strengths:

Overall, this study is well executed and provides a valuable framework for assessing the impact of emerging SARS-CoV-2 variants on nanobodies using a combination of in vitro biochemical and cellular assays as well as computational approaches. There are interesting insights generated from the epitope mapping analyses, which offer possible explanations for how delta and omicron variants escape nanobody responses, as well as how some nanobodies exhibit cross-variant neutralization capacity. These analyses laid out a clear path forward for optimizing these promising next-gen therapeutics, particularly in the face of rapidly emerging SARS-CoV-2 variants. This work will be of interest to researchers in the fields of antibody/nanobody engineering, SARS-CoV-2 therapeutics, and host-virus interaction.

Weaknesses:

A main weakness of the study is that the efficacy statement is not thoroughly supported. While the authors comprehensively characterized the neutralizing ability of nanobodies in vitro, there is no animal data involving mice or hamsters to demonstrate the real protective efficacy in vivo. Yet, in the title and throughout the manuscript, the authors repeatedly used phrases like "retains efficacy" or "remains efficacious" to describe the nanobodies' neutralization or binding capacities.

This claim is not well supported by the data and underestimates the impact of variants on the nanobodies, especially the omicron sublineages. For example, the authors showed that S1-RBD-15 had a ~100-fold reduction in neutralization titer against Omicron, with an IC50 at around 1 uM. This is much higher than the IC50 value of a typical anti-ancestral RBD nanobody reported in the previous study (Mast, Fridy et al. 2021). In fact, the authors themselves ascribe nanobodies with an IC50 above 1 uM as weak neutralizers. And there were many in the range of 0.1-1 uM.

Furthermore, many nanobodies selected for affinity measurement against BA.4/5 had no detectable binding.

Without providing in vivo protection data or including monoclonal antibodies that are known to be efficacious against variants in the in vitro assays as a benchmark, it is difficult to evaluate the efficacy just with the IC50 values.

We respectfully disagree with the reviewer on several aspects of this critique.

As to our use of the word efficacy - the quality of being successful in producing an intended result; effectiveness - we were specific to nanobody binding and in vitro neutralization of the variant spike proteins tested in the manuscript. Indeed, our manuscript made no claim of efficacy outside of this intended meaning. However, to prevent misinterpretation we will modify the final paragraph of our introduction to state explicitly that the nanobody repertoire retains efficacy in binding and neutralizing variants of spike. The final paragraph of the Introduction will include the following:

“Here, we demonstrate that a subset of our previously published repertoire of nanobodies, generated against spike from the ancestral SARS-CoV-2 virus (Mast, Fridy et al. 2021), retains binding and in vitro neutralization efficacy against circulating variants of concern (VoC), including omicron BA.4/BA.5.”

We agree that in vivo neutralization data would be an important complement to the in vitro binding and neutralization data. Experiments along these lines are ongoing, but are not considered part of a follow-up to our original paper where in vivo data were not included.

We disagree with the Reviewer that “This claim is not well supported by the data and underestimates the impact of variants on the nanobodies, especially the omicron sublineages.” As we specifically state: “In comparison, groups I, I/II, I/IV, V, VII, VIII and the anti-S2 nanobodies contained the majority of omicron BA.1 neutralizers, though here the neutralization potency of many nanobodies was decreased compared to wild-type. This decrease in neutralization potency largely correlates with the accumulation of omicron BA.1 specific mutations throughout the RBD, which likely alters the epitope-binding site of these nanobodies, weakening their interaction with BA.1 spike (Fig. 1B). (emphasis added)”

Naturally, we expected that some of our nanobodies would lose the ability to bind BA.4/BA.5. This enabled us to determine which areas on spike remained susceptible to our nanobodies. We show that 10/29 nanobodies tested retained binding to BA.4/5. We did not test our entire repertoire, just a subset was selected for. We stated the following:

“Of the nanobodies that neutralized both delta and omicron BA.1, representatives from each of the nanobody epitope groups were selected for SPR analysis, where S1 binders with mapped epitopes that neutralized one or both variants well, were prioritized.”

Reviewer #2 (Public Review):

Summary:

Interest in using nanobodies for therapeutic interventions in infectious diseases is growing due to their ability to bind hidden or cryptic epitopes that are inaccessible to conventional immunoglobulins. In the present study, the authors were posed (sic) to characterize nanobodies derived from the library produced earlier with the Wuhan strain of SARS-CoV-2, map their epitopes on SARS-CoV-2 spike protein, and demonstrate that some nanobodies retain binding and even neutralization against antigenically distant Variants of Concern (VOCs) that are currently circulating.

Strengths:

The authors demonstrate that some nanobodies - despite being obtained against the ancestral virus strain - retain high affinity binding to antigenically distant SARS-CoV-2 strains. This is despite the majority of the repertoire losing binding. Although limited to only two nanobody combinations, the demonstration of synergy in virus neutralization between nanobodies targeting different epitopes is compelling.

We thank the Reviewer for this positive summary of the strengths of our study. In our previous work, we applied stringent criteria for the down-selection of nanobodies based on their affinity and diversity, as elaborated on in https://elifesciences.org/articles/73027. The current dataset is a further judiciously curated subset, featuring 41 nanobodies chosen to represent and inform on the 10 structurally mapped epitope groups that we initially identified. This subset is but the tip of an iceberg. For each nanobody demonstrating high-affinity binding and neutralization, we possess multiple sequence variants, offering alternative avenues for investigation. Moreover, our repertoire has since been further elaborated by use of a yeast display library (Cross et al., 2023 JBC) providing additional nanobodies capable of targeting the same epitopes. Our findings presented here, thus serve as a heuristic, enabling us to distill the much larger repertoire into manageable and informative clusters of data. We will modify our manuscript to be more explicit of these facts.

Weaknesses:

The authors imply that nanobodies that retain binding/neutralization of early Omicron sublineages will be active against currently circulating and future virus strains. Unfortunately, no reasoning for such a conclusion nor data supporting this prediction are provided.

The nanobodies we propose to retain binding to current and emerging omicron sublineages at the time (Fig. 4) are those that still bind to omicron BA.1, BA.4/5. The structures of XBB and BQ.1 are not divergent enough from these aforementioned omicron sublineages in the regions we propose our nanobodies retain binding (Fig. 4) to result in loss of binding. Thus, we hypothesize that the epitopes where these nanobodies bind or are predicted to bind (outlined in black (Fig. 4)), represent regions on spike vulnerable to nanobody intervention. Importantly, we also now have further experimental data to support our predictions that these nanobodies in Fig. 4 will retain binding (see plot in Author response image 1). We will provide additional data and complements to key figures to help illustrate this in the revised manuscript.

Author response image 1.

Author response:

eLife assessment

This study is a detailed investigation of how chromatin structure influences replication origin function in yeast ribosomal DNA, with focus on the role of the histone deacetylase Sir2 and the chromatin remodeler Fun30. Convincing evidence shows that Sir2 does not affect origin licensing but rather affects local transcription and nucleosome positioning which correlates with increased origin firing. However, the evidence remains incomplete as the methods employed do not rigorously establish a key aspect of the mechanism, fully address some alternative models, or sufficiently relate to prior results. Overall, this is a valuable advance for the field that could be improved to establish a more robust paradigm.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This paper presents a mechanistic study of rDNA origin regulation in yeast by SIR2. Each of the ~180 tandemly repeated rDNA gene copies contains a potential replication origin. Early-efficient initiation of these origins is suppressed by Sir2, reducing competition with origins distributed throughout the genome for rate-limiting initiation factors. Previous studies by these authors showed that SIR2 deletion advances replication timing of rDNA origins by a complex mechanism of transcriptional de-repression of a local PolII promoter causing licensed origin proteins (MCMcomplexes) to re-localize (slide along the DNA) to a different (and altered) chromatin environment. In this study, they identify a chromatin remodeler, FUN30, that suppresses the sir2∆ effect, and remarkably, results in a contraction of the rDNA to about one-quarter it's normal length/number of repeats, implicating replication defects of the rDNA. Through examination of replication timing, MCM occupancy and nucleosome occupancy on the chromatin in sir2, fun30, and double mutants, they propose a model where nucleosome position relative to the licensed origin (MCM complexes) intrinsically determines origin timing/efficiency. While their interpretations of the data are largely reasonable and can be interpreted to support their model, a key weakness is the connection between Mcm ChEC signal disappearance and origin firing. While the cyclical chromatin association-dissociation of MCM proteins with potential origin sequences may be generally interpreted as licensing followed by firing, dissociation may also result from passive replication and as shown here, displacement by transcription and/or chromatin remodeling.

While it is true that both transcription and passive replication can cause the signal of MCM-ChEC to disappear, neither can cause selective disappearance of the displaced complex without affecting the non-displaced complex.  Indeed, in the case of transcription, RNA polymerase transcribing C-pro would have to first dislodge the normally positioned MCM complex before even reaching the displaced complex.  Furthermore, deletion of FUN30 leads to both more C-pro transcription and less disappearance of the displaced MCM complex.  It is important to keep in mind that this cannot somehow reflect continuous replenishment of displaced MCMs with newly loaded MCMs, since the cells are in S phase and licensing is restricted to G1. 

Moreover, linking its disappearance from chromatin in the ChEC method with such precise resolution needs to be validated against an independent method to determine the initiation site(s). Differences in rDNA copy number and relative transcription levels also are not directly accounted for, obscuring a clearer interpretation of the results.

Copy number reduction of the magnitude caused by deletion of SIR2 and FUN30 does not suppress the sir2D effect (i.e. early replication of the rDNA), but rather exacerbates it.  In particular, deletion of SIR2 and FUN30 causes the rDNA to shrink to approximately 35 copies.  Kwan et al., 2023 (PMID: 36842087) have shown that reduction of rDNA copy number to 35 causes a dramatic acceleration of rDNA replication in a SIR2 strain.  Thus, the effect of rDNA size on replication timing reinforces our conclusion that deletion of FUN30 suppresses rDNA replication.

However, to address this concern directly, in the revision we will include 2 D gels in fob1 strains with equal number of repeats that allows to conclude that the effect of FUN30 deletion in suppressing rDNA origin firing is independent of either rDNA size or FOB1. The figure of the critical 2 D gels is shown below in the reply to reviewer 2.

Nevertheless, this paper makes a valuable advance with the finding of Fun30 involvement, which substantially reduces rDNA repeat number in sir2∆ background. The model they develop is compelling and I am inclined to agree, but I think the evidence on this specific point is purely correlative and a better method is needed to address the initiation site question. The authors deserve credit for their efforts to elucidate our obscure understanding of the intricacies of chromatin regulation. At a minimum, I suggest their conclusions on these points of concern should be softened and caveats discussed. Statistical analysis is lacking for some claims.

Strengths are the identification of FUN30 as suppressor, examination of specific mutants of FUN30 to distinguish likely functional involvement. Use of multiple methods to analyze replication and protein occupancies on chromatin. Development of a coherent model.

Weaknesses are failure to address copy number as a variable; insufficient validation of ChEC method relationship to exact initiation locus; lack of statistical analysis in some cases. 

The two potential initiation sites that one would monitor (non-displaced and displaced) are separated by less than 150 base pairs, and other techniques simply do not have the resolution necessary to distinguish such differences.  Furthermore, as we suggest in the manuscript, our results are consistent with a model in which it is only the displaced MCM complex that is activated, whether in sir2 or WT.  If no genotype-dependent difference in initiation sites is even expected, it would be hard to interpret even the most precise replication-based assays.  However, the reviewer is correct that this is a novel technique and that confirmation with a well-established technique is comforting, therefore we are performing ChIP experiments to corroborate, to the extent possible, the conclusions that we reached with ChEC. 

We appreciate the reviewer pointing out that some statistical analyses were lacking, and we will correct this in a revised manuscript.

Additional background and discussion for public review:

This paper broadly addresses the mechanism(s) that regulate replication origin firing in different chromatin contexts. The rDNA origin is present in each of ~180 tandem repeats of the rDNA sequence, representing a high potential origin density per length of DNA (9.1kb repeat unit). However, the average origin efficiency of rDNA origins is relatively low (~20% in wild-type cells), which reduces the replication load on the overall genome by reducing competition with origins throughout the genome for limiting replication initiation factors. Deletion of histone deacetylase SIR2, which silences PolII transcription within the rDNA, results in increased early activation or the rDNA origins (and reduced rate of overall genome replication). Previous work by the authors showed that MCM complexes loaded onto the rDNA origins (origin licensing) were laterally displaced (sliding) along the rDNA, away from a well-positioned nucleosome on one side. The authors' major hypothesis throughout this work is that the new MCM location(s) are intrinsically more efficient configurations for origin firing. The authors identify a chromatin remodeling enzyme, FUN30, whose deletion appears to suppress the earlier activation of rDNA origins in sir2∆ cells. Indeed, it appears that the reduction of rDNA origin activity in sir2∆ fun30∆ cells is severe enough to results in a substantial reduction in the rDNA array repeat length (number of repeats); the reduced rDNA length presumably facilitates it's more stable replication and maintenance.

Analysis of replication by 2D gels is marginally convincing, using 2D gels for this purpose is very challenging and tricky to quantify. The more quantitative analysis by EdU incorporation is more convincing of the suppression of the earlier replication caused by SIR2 deletion.

To address the mechanism of suppression, they analyze MCM positioning using ChEC, which in G1 cells shows partial displacement of MCM from normal position A to positions B and C in sir2∆ cells and similar but more complete displacement away from A to positions B and C in sir2fun30 cells. During S-phase in the presence of hydroxyurea, which slows replication progression considerably (and blocks later origin firing) MCM signals redistribute, which is interpreted to represent origin firing and bidirectional movement of MCMs (only one direction is shown), some of which accumulate near the replication fork barrier, consistent with their interpretation. They observe that MCMs displaced (in G1) to sites B or C in sir2∆ cells, disappear more rapidly during S-phase, whereas the similar dynamic is not observed in sir2∆fun30∆. This is the main basis for their conclusion that the B and C sites are more permissive than A. While this may be the simplest interpretation, there are limitations with this assay that undermine a rigorous conclusion (additional points below). The main problem is that we know the MCM complexes are mobile so disappearance may reflect displacement by other means including transcription which is high is the sir2∆ background. Indeed, the double mutant has greater level of transcription per repeat unit which might explain more displaced from A in G1. Thus, displacement might not always represent origin firing. Because the sir2 background profoundly changes transcription, and the double mutant has a much smaller array length associated with higher transcription, how can we rule out greater accessibility at site A, for example in sir2∆, leading to more firing, which is suppressed in sir2 fun30 due to greater MCM displacement away from A?

I think the critical missing data to solidly support their conclusions is a definitive determination of the site(s) of initiation using a more direct method, such as strand specific sequencing of EdU or nascent strand analysis. More direct comparisons of the strains with lower copy number to rule out this facet. As discussed in detail below, copy number reduction is known to suppress at least part of the sir2∆ effect so this looms over the interpretations. I think they are probably correct in their overall model based on the simplest interpretation of the data but I think it remains to be rigorously established. I think they should soften their conclusions in this respect.

Reviewer #2 (Public Review):

Summary:

In this manuscript, the authors follow up on their previous work showing that in the absence of the Sir2 deacetylase the MCM replicative helicase at the rDNA spacer region is repositioned to a region of low nucleosome occupancy. Here they show that the repositioned displaced MCMs have increased firing propensity relative to non-displaced MCMs. In addition, they show that activation of the repositioned MCMs and low nucleosome occupancy in the adjacent region depend on the chromatin remodeling activity of Fun30.

Strengths:

The paper provides new information on the role of a conserved chromatin remodeling protein in the regulation of origin firing and in addition provides evidence that not all loaded MCMs fire and that origin firing is regulated at a step downstream of MCM loading.

Weaknesses:

The relationship between the author's results and prior work on the role of Sir2 (and Fob1) in regulation of rDNA recombination and copy number maintenance is not explored, making it difficult to place the results in a broader context. Sir2 has previously been shown to be recruited by Fob1, which is also required for DSB formation and recombination-mediated changes in rDNA copy number. Are the changes that the authors observe specifically in fun30 sir2 cells related to this pathway? Is Fob1 required for the reduced rDNA copy number in fun30 sir2 double mutant cells? 

Strains lacking SIR2 have unstable rDNA size, and FOB1 deletion stabilizes rDNA size in sir2 background. Likewise, FOB1 deletion influences the kinetics  rDNA size reduction in sir2 fun30 cells. However, the main effect of Fun30 in sir2 cells we were interested in, suppression of rDNA replication, is preserved in fob1 background, arguing that the observed effect is independent of Fob1 (see figure below). Given that the main focus of the paper is regulation of rDNA origins activity and that these changes were independent of Fob1, we had elected not to include these results in the original manuscript but will gladly include them in the revision.

Besides refuting the possible role of Fob1 in the FUN30-mediated activation of rDNA origin firing in sir2 cells, the use of fob1 background enabled us compare the activation of rDNA origins in the sir2 and sir2 fun30 strains with equally short rDNA size. The 2-D gels demonstrate a dramatic suppression of rDNA origin activity upon deletion of FUN30 in the sir2 fob1 strains with 35 rDNA copies.

Author response image 1.

The deletion of FUN30 diminishes the replication bubble signal in a fob1 sir2 strain with 35 rDNA copies by more than tenfold. The single rARS signal, marked with the arrow, originates from the rightmost rDNA repeat. This specific rightmost rDNA NheI fragment is approximately 25 kb in size, distinctly larger than the 4.7 kb NheI 1N rARS-containing fragments that originate from the internal rDNA repeats.

Reviewer #3 (Public Review):

Summary:

Heterochromatin is characterized by low transcription activity and late replication timing, both dependent on the NAD-dependent protein deacetylase Sir2, the founding member of the sirtuins. This manuscript addresses the mechanism by which Sir2 delays replication timing at the rDNA in budding yeast. Previous work from the same laboratory (Foss et al. PLoS Genetics 15, e1008138) showed that Sir2 represses transcription-dependent displacement of the Mcm helicase in the rDNA. In this manuscript, the authors show convincingly that the repositioned Mcms fire earlier and that this early firing partly depends on the ATPase activity of the nucleosome remodeler Fun30. Using read-depth analysis of sorted G1/S cells, fun30 was the only chromatin remodeler mutant that somewhat delayed replication timing in sir2 mutants, while nhp10, chd1, isw1, htl1, swr1, isw2, and irc5 had not effect. The conclusion was corroborated with orthogonal assays including two-dimensional gel electrophoresis and analysis of EdU incorporation at early origins. Using an insightful analysis with an Mcm-MNase fusion (Mcm-ChEC), the authors show that the repositioned Mcms in sir2 mutants fire earlier than the Mcm at the normal position in wild type. This early firing at the repositioned Mcms is partially suppressed by Fun30. In addition, the authors show Fun30 affects nucleosome occupancy at the sites of the repositioned Mcm, providing a plausible mechanism for the effect of Fun30 on Mcm firing at that position. However, the results from the MNAse-seq and ChEC-seq assays are not fully congruent for the fun30 single mutant. Overall, the results support the conclusions providing a much better mechanistic understanding how Sir2 affects replication timing at rDNA.

The reason that the results for the fun30 single mutant appear incongruent, with a larger signal of the +2 nucleosome in the MNase-seq plot but a negligible signal in the ChEC-seq plot is the paucity of displaced Mcm in the fun30 single mutant. Given the relative absence of displaced MCMs, the MCM-MNase fusion protein can't "light up" the +2 nucleosome.  We will comment on this in the revision to clarify this. 

Strengths

(1) The data clearly show that the repositioned Mcm helicase fires earlier than the Mcm in the wild type position.

(2) The study identifies a specific role for Fun30 in replication timing and an effect on nucleosome occupancy around the newly positioned Mcm helicase in sir2 cells.

Weaknesses

(1) It is unclear which strains were used in each experiment.

(2) The relevance of the fun30 phospho-site mutant (S20AS28A) is unclear.

(3) For some experiments (Figs. 3, 4, 6) it is unclear whether the data are reproducible and the differences significant. Information about the number of independent experiments and quantitation is lacking. This affects the interpretation, as fun30 seems to affect the +3 nucleosome much more than let on in the description.

We appreciate the reviewer pointing out places in which our manuscript omitted key pieces of information (items 1 and 3), and we will fix these oversights in our revision. 

With regard to point 2, we had written: 

“Fun30 is also known to play a role in the DNA damage response; specifically, phosphorylation of Fun30 on S20 and S28 by CDK1 targets Fun30 to sites of DNA damage, where it promotes DNA resection (Chen et al. 2016; Bantele et al. 2017). To determine whether the replication phenotype that we observed might be a consequence of Fun30's role in the DNA damage response, we tested non-phosphorylatable mutants for the ability to suppress early replication of the rDNA in sir2; these mutations had no effect on the replication phenotype (Figure 2B), arguing against a primary role for Fun30

in DNA damage repair that somehow manifests itself in replication.”

We will expand on this to clarify our point in the revision.

Author response:

Reviewer #1 (Public review):

Summary:

Argunşah et al. describe and investigate the mechanisms underlying the differential response dynamics of barrel vs septa domains of the whisker-related primary somatosensory cortex (S1). Upon repeated stimulation, the authors report that the response ratio between multi- and single-whisker stimulation increases in layer (L) 4 neurons of the septal domain, while remaining constant in barrel L4 neurons. This difference is attributed to the short-term plasticity properties of interneurons, particularly somatostatin-expressing (SST+) neurons. This claim is supported by the increased density of SST+ neurons found in L4 of the septa compared to barrels, along with a stronger response of (L2/3) SST+ neurons to repeated multi- vs single-whisker stimulation. The role of the synaptic protein Elfn1 is then examined. Elfn1 KO mice exhibited little to no functional domain separation between barrel and septa, with no significant difference in single- versus multi-whisker response ratios across barrel and septal domains. Consistently, a decoder trained on WT data fails to generalize to Elfn1 KO responses. Finally, the authors report a relative enrichment of S2- and M1-projecting cell densities in L4 of the septal domain compared to the barrel domain.

Strengths:

This paper describes and aims to study a circuit underlying differential response between barrel columns and septal domains of the primary somatosensory cortex. This work supports the view that barrel and septal domains contribute differently to processing single versus multi-whisker inputs, suggesting that the barrel cortex multiplexes sensory information coming from the whiskers in different domains.

We thank the reviewer for the very neat summary of our findings that barrel cortex multiplexes converging information in separate domains.

Weaknesses:

While the observed divergence in responses to repeated SWS vs MWS between the barrel and septal domains is intriguing, the presented evidence falls short of demonstrating that short-term plasticity in SST+ neurons critically underpins this difference. The absence of a mechanistic explanation for this observation limits the work's significance. The measurement of SST neurons' response is not specific to a particular domain, and the Elfn1 manipulation does not seem to be specific to either stimulus type or a particular domain.

We appreciate the reviewer’s perspective. Although further research is needed to understand the circuit mechanisms underlying the observed phenomenon, we believe our data suggest that altering the short-term dynamics of excitatory inputs onto SST neurons reduces the divergent spiking dynamics in barrels versus septa during repetitive single- and multi-whisker stimulation. Future work could examine how SST neurons, whose somata reside in barrels and septa, respond to different whisker stimuli and the circuits in which they are embedded. At this time, however, the authors believe there is no alternative way to test how the short-term dynamics of excitatory inputs onto SST neurons, as a whole, contribute to the temporal aspects of barrel versus septa spiking.

The study's reach is further constrained by the fact that results were obtained in anesthetized animals, which may not generalize to awake states.

We appreciate the reviewer’s concern regarding the generalizability of our findings from anesthetized animals to awake states. Anesthesia was employed to ensure precise individual whisker stimulation (and multi-whisker in the same animal), which is challenging in awake rodents due to active whisking. While anesthesia may alter higher-order processing, core mechanisms, such as short and long term plasticity in the barrel cortex, are preserved under anesthesia (Martin-Cortecero et al., 2014; Mégevand et al., 2009).

The statistical analysis appears inappropriate, with the use of repeated independent tests, dramatically boosting the false positive error rate.

Thank you for your feedback on our analysis using independent rank-based tests for each time point in wild-type (WT) animals. To address concerns regarding multiple comparisons and temporal dependencies (for Figure 1F and 4D for now but we will add more in our revision), we performed a repeated measures ANOVA for WT animals (13 Barrel, 8 Septa, 20 time points), which revealed a significant main effect of Condition (F(1,19) = 16.33, p < 0.001) and a significant Condition-Time interaction (F(19,361) = 2.37, p = 0.001). Post-hoc tests confirmed significant differences between Barrel and Septa at multiple time points (e.g., p < 0.0025 at times 3, 4, 6, 7, 8, 10, 11, 12, 16, 19 after Bonferroni posthoc correction), supporting a differential multi-whisker vs. single-whisker ratio response in WT animals. In contrast, a repeated measures ANOVA for knock-out (KO) animals (11 Barrel, 7 Septa, 20 time points) showed no significant main effect of Condition (F(1,14) = 0.17, p = 0.684) or Condition-Time interaction (F(19,266) = 0.73, p = 0.791), indicating that the Barrel-Septa difference observed in WT animals is absent in KO animals.

Furthermore, the manuscript suffers from imprecision; its conclusions are occasionally vague or overstated. The authors suggest a role for SST+ neurons in the observed divergence in SWS/MWS responses between barrel and septal domains. However, this remains speculative, and some findings appear inconsistent. For instance, the increased response of SST+ neurons to MWS versus SWS is not confined to a specific domain. Why, then, would preferential recruitment of SST+ neurons lead to divergent dynamics between barrel and septal regions? The higher density of SST+ neurons in septal versus barrel L4 is not a sufficient explanation, particularly since the SWS/MWS response divergence is also observed in layers 2/3, where no difference in SST+ neuron density is found.

Moreover, SST+ neuron-mediated inhibition is not necessarily restricted to the layer in which the cell body resides. It remains unclear through which differential microcircuits (barrel vs septum) the enhanced recruitment of SST+ neurons could account for the divergent responses to repeated SWS versus MWS stimulation.

We fully appreciate the reviewer’s comment. We currently do not provide any evidence on the contribution of SST neurons in the barrels versus septa in layer 4 on the response divergence of spiking observed in SWS versus MWS. We only show that these neurons differentially distribute in the two domains in this layer. It is certainly known that there is molecular and circuit-based diversity of SST-positive neurons in different layers of the cortex, so it is plausible that this includes cells located in the two domains of vS1, something which has not been examined so far. Our data on their distribution are one piece of information that SST neurons may have a differential role in inhibiting barrel stellate cells versus septa ones. Morphological reconstructions of SST neurons in L4 of the somatosensory barrel cortex has shown that their dendrites and axons project locally and may confine to individual domains, even though not specifically examined (Fig. 3 of Scala F et al., 2019). The same study also showed that L4 SST cells receive excitatory input from local stellate cells) and is known that they are also directly excited by thalamocortical fibers (Beierlein et al., 2003; Tan et al., 2008), both of which facilitate.

As shown in our supplementary figure, the divergence is also observed in L2/3 where, as the reviewer also points out, where we do not have a differential distribution of SST cells, at least based on a columnar analysis extending from L4. There are multiple scenarios that could explain this “discrepancy” that one would need to examine further in future studies. One straightforward one is that the divergence in spiking in L2/3 domains may be inherited from L4 domains, where L4 SST act on. Another is that even though L2/3 SST neurons are not biased in their distribution their input-output function is, something which one would need to examine by detailed in vitro electrophysiological and perhaps optogenetic approaches in S1. Despite the distinctive differences that have been found between the L4 circuitry in S1 and V1 (Scala F et al., 2019), recent observations indicate that small but regular patches of V1 marked by the absence of muscarinic receptor 2 (M2) have high temporal acuity (Ji et al., 2015), and selectively receive input from SST interneurons (Meier et al., 2025). Regions lacking M2 have distinct input and output connectivity patterns from those that express M2 (Meier et al., 2021; Burkhalter et al., 2023). These findings, together with ours, suggest that SST cells preferentially innervate and regulate specific domains -columns- in sensory cortices.

Regardless of the mechanism, the Elfn1 knock-out mouse line almost exclusively affects the incoming excitability onto SST neurons (see also reply to comment below), hence what can be supported by our data is that changing the incoming short-term synaptic plasticity onto these neurons brings the spiking dynamics between barrels and septa closer together.

The Elfn1 KO mouse model seems too unspecific to suggest the role of the short-term plasticity in SST+ neurons in the differential response to repeated SWS vs MWS stimulation across domains. Why would Elfn1-dependent short-term plasticity in SST+ neurons be specific to a pathway, or a stimulation type (SWS vs MWS)? Moreover, the authors report that Elfn1 knockout alters synapses onto VIP+ as well as SST+ neurons (Stachniak et al., 2021; previous version of this paper)-so why attribute the phenotype solely to SST+ circuitry? In fact, the functional distinctions between barrel and septal domains appear largely abolished in the Elfn1 KO.

Previous work by others and us has shown that globally removing Elfn1 selectively removes a synaptic process from the brain without altering brain anatomy or structure. This allows us to study how the temporal dynamics of inhibition shape activity, as opposed to inhibition from particular cell types. We will nevertheless update the text to discuss more global implications for SST interneuron dynamics and include a reference to VIP interneurons that contain Elfn1.

When comparing SWS to MWS, we find that MWS replaces the neighboring excitation which would normally be preferentially removed by short-term plasticity in SST interneurons, thus providing a stable control comparison across animals and genotypes. On average, VIP interneurons failed to show modulation by MWS. We were unable to measure a substantial contribution of VIP cells to this process and also note that the Elfn1 expressing multipolar neurons comprise only ~5% of VIP neurons (Connor and Peters, 1984; Stachniak et al., 2021), a fraction that may be lost when averaging from 138 VIP cells. Moreover, the effect of Elfn1 loss on VIP neurons is quite different and marginal compared to that of SST cells, suggesting that the primary impact of Elfn1 knockout is mediated through SST+ interneuron circuitry. Therefore, even if we cannot rule out that these 5% of VIP neurons contribute to barrel domain segregation, we are of the opinion that their influence would be very limited if any.

Reviewer #2 (Public review):

Summary:

Argunsah and colleagues demonstrate that SST-expressing interneurons are concentrated in the mouse septa and differentially respond to repetitive multi-whisker inputs. Identifying how a specific neuronal phenotype impacts responses is an advance.

Strengths:

(1) Careful physiological and imaging studies.

(2) Novel result showing the role of SST+ neurons in shaping responses.

(3) Good use of a knockout animal to further the main hypothesis.

(4) Clear analytical techniques.

We thank the reviewer for their appreciation of the study.

Weaknesses:

No major weaknesses were identified by this reviewer. Overall, I appreciated the paper but feel it overlooked a few issues and had some recommendations on how additional clarifications could strengthen the paper. These include:

(1) Significant work from Jerry Chen on how S1 neurons that project to M1 versus S2 respond in a variety of behavioral tasks should be included (e.g. PMID: 26098757). Similarly, work from Barry Connor's lab on intracortical versus thalamocortical inputs to SST neurons, as well as excitatory inputs onto these neurons (e.g. PMID: 12815025) should be included.

We thank the reviewer for these valuable resources that we overlooked. We will include Chen et al. (2015), Cruikshank et al. (2007) and Gibson et al. (1999) to contextualize S1 projections and SST+ inputs, strengthening the study’s foundation as well as Beierlein et al. (2003) which nicely show both local and thalamocortical facilitation of excitatory inputs onto L4 SST neurons, in contrast to PV cells. The paper also shows the gradual recruitment of SST neurons by thalamocortical inputs to provide feed-forward inhibition onto stellate cells (regular spiking) of the barrel cortex L4 in rat.

(2) Using Layer 2/3 as a proxy to what is happening in layer 4 (~line 234). Given that layer 2/3 cells integrate information from multiple barrels, as well as receiving direct VPm thalamocortical input, and given the time window that is being looked at can receive input from other cortical locations, it is not clear that layer 2/3 is a proxy for what is happening in layer 4.

We agree with the reviewer that what we observe in L2/3 is not necessarily what is taking place in L4 SST-positive cells. The data on L2/3 was included to show that these cells, as a population, can show divergent responses when it comes to SWS vs MWS, which is not seen in L2/3 VIP neurons. Regardless of the mechanisms underlying it, our overall data support that SST-positive neurons can change their activation based on the type of whisker stimulus and when the excitatory input dynamics onto these neurons change due to the removal of Elfn1 the recruitment of barrels vs septa spiking changes at the temporal domain. Having said that, the data shown in Supplementary Figure 3 on the response properties of L2/3 neurons above the septa vs above the barrels (one would say in the respective columns) do show the same divergence as in L4. This suggests that a circuit motif may exist that is common to both layers, involving SST neurons that sit in L4, L5 or even L2/3. This implies that despite the differences in the distribution of SST neurons in septa vs barrels of L4 there is an unidentified input-output spatial connectivity motif that engages in both L2/3 and L4. Please also see our response to a similar point raised by reviewer 1.

(3) Line 267, when discussing distinct temporal response, it is not well defined what this is referring to. Are the neurons no longer showing peaks to whisker stimulation, or are the responses lasting a longer time? It is unclear why PV+ interneurons which may not be impacted by the Elfn1 KO and receive strong thalamocortical inputs, are not constraining activity.

We thank the reviewer for their comment and will clarify the statement.

This convergence of response profiles was further clear in stimulus-aligned stacked images, where the emergent differences between barrels and septa under SWS were largely abolished in the KO (Figure 4B). A distinction between directly stimulated barrels and neighboring barrels persisted in the KO. In addition, the initial response continued to differ between barrel and septa and also septa and neighbor (Figure 4B). This initial stimulus selectivity potentially represents distinct feedforward thalamocortical activity, which includes PV+ interneuron recruitment that is not directly impacted by the Elfn1 KO (Sun et al., 2006; Tan et al., 2008). PV+ cells are strongly excited by thalamocortical inputs, but these exhibit short-term depression, as does their output, contrasting with the sustained facilitation observed in SST+ neurons. These findings suggest that in WT animals, activity spillover from principal barrels is normally constrained by the progressive engagement of SST+ interneurons in septal regions, driven by Elfn1-dependent facilitation at their excitatory synapses. In the absence of Elfn1, this local inhibitory mechanism is disrupted, leading to longer responses in barrels, delayed but stronger responses in septa, and persistently stronger responses in unstimulated neighbors, resulting in a loss of distinction between the responses of barrel and septa domains that normally diverge over time (see Author response image 1 below).

Author response image 1.

A) Barrel responses are longer following whisker stimulation in KO. B) Septal responses are slightly delayed but stronger in KO. C) Unstimulated neighbors show longer persistent responses in KO.

(4) Line 585 "the earliest CSD sink was identified as layer 4..." were post-hoc measurements made to determine where the different shank leads were based on the post-hoc histology?

Post hoc histology was performed on plane-aligned brain sections which would allow us to detect barrels and septa, so as to confirm the insertion domains of each recorded shank. Layer specificity of each electrode therefore could therefore not be confirmed by histology as we did not have coronal sections in which to measure electrode depth.

(5) For the retrograde tracing studies, how were the M1 and S2 injections targeted (stereotaxically or physiologically)? How was it determined that the injections were in the whisker region (or not)?

During the retrograde virus injection, the location of M1 and S2 injections was determined by stereotaxic coordinates (Yamashita et al., 2018). After acquiring the light-sheet images, we were able to post hoc examine the injection site in 3D and confirm that the injections were successful in targeting the regions intended. Although it would have been informative to do so, we did not functionally determine the whisker-related M1 and whisker-related S2 region in this experiment.

(6) Were there any baseline differences in spontaneous activity in the septa versus barrel regions, and did this change in the KO animals?

Thank you for this interesting question. Our previous study found that there was a reduction in baseline activity in L4 barrel cortex of KO animals at postnatal day (P)12, but no differences were found at P21 (Stachniak et al., 2023).

Reviewer #3 (Public review):

Summary:

This study investigates the functional differences between barrel and septal columns in the mouse somatosensory cortex, focusing on how local inhibitory dynamics, particularly involving Elfn1-expressing SST⁺ interneurons, may mediate temporal integration of multi-whisker (MW) stimuli in septa. Using a combination of in vivo multi-unit recordings, calcium imaging, and anatomical tracing, the authors propose that septa integrate MW input in an Elfn1-dependent manner, enabling functional segregation from barrel columns.

Strengths:

The core hypothesis is interesting and potentially impactful. While barrels have been extensively characterized, septa remain less understood, especially in mice, and this study's focus on septal integration of MW stimuli offers valuable insights into this underexplored area. If septa indeed act as selective integrators of distributed sensory input, this would add a novel computational role to cortical microcircuits beyond what is currently attributed to barrels alone. The narrative of this paper is intellectually stimulating.

We thank the reviewer for finding the study intellectually stimulating.

Weaknesses:

The methods used in the current study lack the spatial and cellular resolution needed to conclusively support the central claims. The main physiological findings are based on unsorted multi-unit activity (MUA) recorded via low-channel-count silicon probes. MUA inherently pools signals from multiple neurons across different distances and cell types, making it difficult to assign activity to specific columns (barrel vs. septa) or neuron classes (e.g., SST⁺ vs. excitatory).

The recording radius (~50-100 µm or more) and the narrow width of septa (~50-100 µm or less) make it likely that MUA from "septal" electrodes includes spikes from adjacent barrel neurons.

The authors do not provide spike sorting, unit isolation, or anatomical validation that would strengthen spatial attribution. Calcium imaging is restricted to SST⁺ and VIP⁺ interneurons in superficial layers (L2/3), while the main MUA recordings are from layer 4, creating a mismatch in laminar relevance.

We thank the reviewer for pointing out the possibility of contamination in septal electrodes. Importantly, it may not have been highlighted, although reported in the methods, but we used an extremely high threshold (7.5 std, in methods, line 583) for spike detection in order to overcome the issue raised here, which restricts such spatial contaminations. Since the spike amplitude decays rapidly with distance, at high thresholds, only nearby neurons contribute to our analysis, potentially one or two. We believe that this approach provides a very close approximation of single unit activity (SUA) in our reported data. We will include a sentence earlier in the manuscript to make this explicit and prevent further confusion.

Regarding the point on calcium imaging being performed on L2/3 SST and VIP cells instead of L4. Both reviewer 1 and 2 brought up the same issue and we responded as follows. As shown in our supplementary figure, the divergence is also observed in L2/3 where we do not have a differential distribution of SST cells, at least based on a columnar analysis extending from L4. There are multiple scenarios that could explain this “discrepancy” that one would need to examine further in future studies. One straightforward one is that the divergence in spiking in L2/3 domains may be inherited from L4 domains, where L4 SST act on. Another is that even though L2/3 SST neurons are not biased in their distribution their input-output function is, something which one would need to examine by detailed in vitro electrophysiological and perhaps optogenetic approaches in S1. Despite the distinctive differences that have been found between the L4 circuitry in S1 and V1 (Scala F et al., 2019), recent observations indicate that small but regular patches of V1 marked by the absence of muscarinic receptor 2 (M2) have high temporal acuity (Ji et al., 2015), and selectively receive input from SST interneurons (Meier et al., 2025). Regions lacking M2 have distinct input and output connectivity patterns from those that express M2 (Meier et al., 2021; Burkhalter et al., 2023). These findings, together with ours, suggest that SST cells preferentially innervate and regulate specific domains -columns- in sensory cortices.

Furthermore, while the role of Elfn1 in mediating short-term facilitation is supported by prior studies, no new evidence is presented in this paper to confirm that this synaptic mechanism is indeed disrupted in the knockout mice used here.

We thank Reviewer #3 for noting the absence of new evidence confirming Elfn1’s disruption of short-term facilitation in our knockout mice. We acknowledge that our study relies on previously strong published data demonstrating that Elfn1 mediates short-term synaptic facilitation of excitatory inputs onto SST+ interneurons (Sylwestrak and Ghosh, 2012; Tomioka et al., 2014; Stachniak et al., 2019, 2023). These studies consistently show that Elfn1 knockout abolishes facilitation in SST+ synapses, leading to altered temporal dynamics, which we hypothesize underlies the observed loss of barrel-septa response divergence in our Elfn1 KO mice (Figure 4). Nevertheless, to address the point raised, we will clarify in the revised manuscript (around lines 245-247 and 271-272) that our conclusions are based on these established findings, stating: “Building on prior evidence that Elfn1 knockout disrupts short-term facilitation in SST+ interneurons (Sylwestrak and Ghosh, 2012; Tomioka et al., 2014; Stachniak et al., 2019, 2023), we attribute the abolished barrel-septa divergence in Elfn1 KO mice to altered SST+ synaptic dynamics, though direct synaptic measurements were not performed here.”

Additionally, since Elfn1 is constitutively knocked out from development, the possibility of altered circuit formation-including changes in barrel structure and interneuron distribution, cannot be excluded and is not addressed.

We thank Reviewer #3 for raising the valid concern that constitutive Elfn1 knockout could potentially alter circuit formation, including barrel structure and interneuron distribution. To address this, we will clarify in the revised manuscript (around line ~271 and in the Discussion) that in our previous studies that included both whole-cell patch-clamp in acute brain slices ranging from postnatal day 11 to 22 (P11 - P21) and in vivo recordings from barrel cortex at P12 and P21, we saw no gross abnormalities in barrel structure, with Layer 4 barrels maintaining their characteristic size and organization, consistent with wild-type (WT) mice (Stachniak et al., 2019, 2023). While we cannot fully exclude subtle developmental changes, prior studies indicate that Elfn1 primarily modulates synaptic function rather than cortical cytoarchitecture (Tomioka et al., 2014). Elfn1 KO mice show no gross morphological or connectivity differences and the pattern and abundance of Elfn1 expressing cells (assessed by LacZ knock in) appears normal (Dolan and Mitchell, 2013).

We will add the following to the Discussion: “Although Elfn1 is constitutively knocked out, we find here and in previous studies that barrel structure is preserved (Stachniak et al., 2019, 2023). Further, the distribution of Elfn1 expressing interneurons is not different in KO mice, suggesting minimal developmental disruption (Dolan and Mitchell, 2013). Nonetheless, we acknowledge that subtle circuit changes cannot be ruled out without the usage of time-depended conditional knockout of the gene.”

References

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(5) Cruikshank, S. J., Lewis, T. J. & Connors, B. W. (2007). Synaptic basis for intense thalamocortical activation of feedforward inhibitory cells in neocortex. Nat. Neurosci. 10, 462–468.

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Author response:

eLife Assessment:

This important study investigates the propensity of the intravacuolar pathogen, Leishmania, to scavenge lipids which it utilizes for its accelerated growth within macrophages. Although some of the data compellingly links increased lipid acquisition to parasite growth, data to support the underlying mechanism to describe the proposed model is incomplete. The study adds to other work that has implicated pathogen-derived processes in the selective recruitment of vesicles to the pathogen-containing vacuole, based on the content of the cargo.

We appreciate the time and effort that Editor and Reviewers have provided to provide the assessment of our work (eLife: eLife-RP-RA-2024-102857). We thank them all for this assessment.

Regarding some of the concerns raised by Reviewer 1, particularly the lack of data on NPC-1 knockdown, we would like to clarify that this information was included in our original submission (as elaborated in detail in the following section). Additionally, we acknowledge that one of the major concerns about the completeness of our work stems from Reviewer 1’s comments on the isolation and purity of the parasitophorous vacuole (PV). Reviewer 2 has also emphasized the importance of this experiment in strengthening the technical rigor of our study, and we fully agree with this recommendation. We acknowledge that this is a very appropriate suggestion by both the Reviewers and we will include this data in the subsequent revision of this work for revaluation of assessment. Also, ahead of a full revision of the paper, we would like to address the concerns raised by the reviewers outlining our revision plans.

Public Reviews:

Reviewer #1 (Public review):

Although the use of antimony has been discontinued in India, the observation that there are Leishmania parasites that are resistant to antimony in circulation has been cited as evidence that these resistant parasites are now a distinct strain with properties that ensure their transmission and persistence. It is of interest to determine what are the properties that favor the retention of their drug resistance phenotype even in the absence of the selective pressure that would otherwise be conferred by the drug. The hypothesis that these authors set out to test is that these parasites have developed a new capacity to acquire and utilize lipids, especially cholesterol which affords them the capacity to grow robustly in infected hosts.

We sincerely appreciate Reviewer 1's thoughtful and positive evaluation of our manuscript. We acknowledge that the reviewer has a few major concerns, and we would like to address them one by one in the following section of this initial response before submitting a full revision of our work.

Major issues:

(1) There are several experiments for which they do not provide sufficient details, but proceed to make significant conclusions.

Experiments in section 5 are poorly described. They supposedly isolated PVs from infected cells. No details of their protocol for the isolation of PVs are provided. They reference a protocol for PV isolation that focused on the isolation of PVs after L. amazonensis infection. In the images of infection that they show, by 24 hrs, infected cells harbor a considerable number of parasites. Is it at the 24 hr time point that they recover PVs? What is the purity of PVs? The authors should provide evidence of the success of this protocol in their hands. Earlier, they mentioned that using imaging techniques, the PVs seem to have fused or interconnected somehow. Does this affect the capacity to recover PVs? If more membranes are recovered in the PV fraction, it may explain the higher cholesterol content.

We would like to thank the reviewer for correctly pointing out lack of details regarding PV isolation and its purity. There are multiple questions raised by the reviewer and we will answer them one by one in a point wise manner:

Firstly, “Is it at the 24 hr time point that they recover PVs?”

In the ‘Methods’ section of the original submission (Line number-606-611), there is a separate section on “Parasitophorous vacuole (PV) Isolation and cholesterol measurement”, where it is clearly mentioned, “24Hrs LD infected KCs were lysed by passing through a 22-gauge syringe needle to release cellular contents. Parasitophorous vacuoles (PV) were then isolated using a previously outlined protocol [Ref: 73].” However, we do acknowledge further details might be useful to enrich this section, and hence we would like to include the following details in the revised manuscript, “10⁷ KCs were seeded in a 100 mm plate and allowed to adhere for 24 hours. Following infection with Leishmania donovani (LD) for 24 hours, the infected KCs were harvested by gentle scraping and lysed through five successive passages through an insulin needle to ensure membrane disruption while preserving organelle integrity. The lysate was centrifuged at 200 × g for 10 minutes at 4°C to remove intact cells and large debris. The resulting supernatant was carefully collected and subjected to a discontinuous sucrose density gradient (60%, 40%, and 20%). The gradient was centrifuged at 700 × g for 25 minutes at 4°C to facilitate organelle separation. The interphase between the 40% and 60% sucrose layers, enriched with PVs, was carefully collected and subjected to a final centrifugation step at 12,000 × g for 25 minutes at 4°C. The supernatant was discarded, and the resulting pellet was enriched for purified parasitophorous vacuoles, suitable for downstream biochemical and molecular analyses.”

Secondly, What is the purity of PVs? Earlier, they mentioned that using imaging techniques, the PVs seem to have fused or interconnected somehow. Does this affect the capacity to recover PVs? If more membranes are recovered in the PV fraction, it may explain the higher cholesterol content.

We appreciate the reviewer for pointing this critical lack of data in the current version of the manuscript. We will be providing data on the purity of isolated fraction by performing western blot against PV and cytoplasmic fraction in the Revised manuscript. We admit, as rightly pointed out by the reviewer we need to access the purity of isolated PV in our experiment and we plan to show this is in the Revised manuscript along with a biochemical quantification of total PV membrane isolated under different experimental condition using Amplex Red kit (Invitrogen™ A12216) or similar other methods.

(2) In section 6 they evaluate the mechanism of LDL uptake in macrophages. Several approaches and endocytic pathway inhibitors are employed. The authors must be aware that the role of cytochalasin D in the disruption of fluid phase endocytosis is controversial. Although they reference a study that suggests that cytochalasin D has no effect on fluid-phase endocytosis, other studies have found the opposite (doi: 10.1371/journal.pone.0058054). It wasn't readily evident what concentrations were used in their study. They should consider testing more than 1 concentration of the drug before they make their conclusions on their findings on fluid phase endocytosis.

We thank the reviewer for this insightful comment and we apologise for missing out mentioning Cytochalasin D concentration. To clarify, LDL uptake by LD-R infected KCs is LDL-receptor independent as clearly shown in Section 6, Figure 4A, Figure S4A, Figure S4B i and Figure S4B ii in the Submitted manuscript. In (Figure 4F and Figure S4D) of the Submitted manuscript, as referred by the Reviewer, Cytochalasin D was used at a concentration of 2.5µg/ml. At this concentration, we did not observe any effect of Cytochalsin D on LDL-receptor independent fluid phase endocytosis as intracellular LD-R amastigotes was able to uptake LDL successfully and proliferate in infected Kupffer cells, unlike Latranculin-A (5µM) treatment which completely inhibited intracellular proliferation of LD-R amastigotes by blocking only receptor independent Fluid phase endocytosis (Movie 2A and 2B and Figure 4E in the Submitted manuscript). In fact, the study referred by the reviewer (doi: 10.1371/journal.pone.0058054), used a concentration of 4µg/ml Cytochalasin D which did affect both LDL-receptor dependent and also receptor independent endocytosis in bone marrow derived macrophages. We would also like to clarify that in this work during our preliminary experiments we have also tested higher concentration Cytochalasin-D (5µg/ml). However, even at this higher concentration there were no significant effect of Cytochalasin-D on LD-R induced LDL-receptor independent fluid phase endocytosis as observed from intracellular LD-R amastigote count represented in Author response image 1. Thus, we strongly believe that Cytochalasin D does not have any impact on LD-R induced fluid phase endocytosis even at higher concentration. We will include this in the discussion section of the revised manuscript to clear out any confusion that readers might have, and also concentration of all the inhibitors used in the study will be mentioned in the Result section, as well as in the revised Figure legends.

Author response image 1.

A. Giemsa-stained images illustrating the impact of concentrations of CYT-D (2.5 and 5 µg/ml) on LD-R-infected Kupffer cells. Black arrow showing intracellular amastigotes. Scale bar 10µM. B. Graphical representation depicting the effect of varying concentrations of CYT-D on the intracellular growth of LD-R. ‘ns’ depicts no significant change.

(3) In Figure 5 they present a blot that shows increased Lamp1 expression from as early as 4 hrs after infection with LD-R and by 12 hrs after infection of both LD-S and LD-R. Increased Lamp1 expression after Leishmania infection has not been reported by others. By what mechanism do they suggest is causing such a rapid increase (at 4hrs post-infection) in Lamp-1 protein? As they report, their RNA seq data did not show an increase in LAMP1 transcription (lines 432 - 434).

We would like to express our gratitude to the reviewer for highlighting the novelty of this observation. Indeed, to the best of our knowledge, no similar findings have been reported previously in primary macrophages infected with Leishmania donovani (LD). Firstly, we would like to point out, as stated in the Methods section (lines 562–566) of the Submitted manuscript: "Flow-sorted metacyclic LD promastigotes were used at a MOI of 1:10 (with variations of 1:5 and 1:20 in some cases) for 4 hours, which was considered the 0th point of infection. Macrophages were subsequently washed to remove any extracellular loosely attached parasites and incubated further as per experimental requirements.” This indicates that our actual study points correspond to approximately the 8th hour post-infection”. We just wanted to clarify this to prevent any potential confusion.

Now regarding LAMP1 expression, although we could not find any previous reports of its expression in LD infected primary macrophages, we would like to mention that a previous report (doi.org/10.1128/mBio.01464-20), has shown a similar punctuated LAMP-1 upregulation (as observed by us in Figure 5A i of the Submitted manuscript) in response to leishmania infection in non-phagocytic fibroblast. It is tempting to speculate that increased LAMP-1 expression observed in response to LD-R infected macrophages might be due to increased lysosomal biogenesis, required for degrading increased endocytosed-LDL into bioavailable cholesterol.  However, since no change in LAMP-1 expression in RNA seq data (Figure 6, of the Submitted manuscript), we can only speculate that this is happening due to some post transcriptional or post translational modifications. But further work will definitely require to investigate this mechanism in details which is beyond the scope of this work. That is why, in the Submitted manuscript, (Line 432-435), we have discussed this, “Although available RNAseq analysis (Figure 6) did not support this increased expression of lamp-1 in the transcript level, it did reflect a notable upregulation of vesicular fusion protein (VSP) vamp8 and stx1a in response to LD-R-infection. LD infection can regulate LAMP-1 expression, and the role of VSPs in LDL-vesicle fusion with LD-R-PV is worthy of further investigation.”

However, we agree with the reviewer that this might not be enough for the clarification. Hence in the revised manuscript we plan to update this part as follows, “Although available RNAseq analysis (Figure 6) did not support this increased expression of lamp-1 in the transcript level, it did reflect a notable upregulation of vesicular fusion protein (VSP) vamp8 and stx1a in response to LD-R-infection. How, LD infection can regulate LAMP-1 expression, and the role of VSPs in LDL-vesicle fusion with LD-R-PV is worthy of further investigation. It is possible and has been earlier reported that LD infection can regulate host proteins expression through post transcriptional and post translational modifications (doi.org/10.1111/pim.12156, doi.org/10.3389/fmicb.2017.00314, doi: 10.3389/fimmu.2023.1287539). It is tempting to speculate that LD-R amastigote might be promoting an increased lysosomal biogenesis through any such mechanism to increase supply of bioavailable cholesterol through action of lysosomal acid hydrolases on LDL.”

(4) In Figure 6, amongst several assays, they reported on studies where SPC-1 is knocked down in PECs. They failed to provide any evidence of the success of the knockdown, but nonetheless showed greater LD-R after NPC-1 was knocked down. They should provide more details of such experiments.

Although we do understand the concern raised by the reviewer, this statement in question is factually incorrect. We would like to point out that in Figure 6 F i, of the Submitted manuscript, we have demonstrated decreased NPC-1 staining following transfection with NPC-1-specific siRNA, whereas no such reduction was observed with scrambled RNA. Similar immunofluorescence data confirming LDL-receptor knockdown has also been provided in Figure S4B i of the Submitted manuscript. However, we acknowledge that the reviewer may be referring to the lack of quantitative validation of the knockdown via Western blot. We would like to clarify although, we already had this data, but we did not include it to avoid duplication to reduce the data density of the manuscript. But as suggested by the reviewer, we will be including western blot for both NPC-1 and LDL-receptor knock down in the revised manuscript as represented in Author response image 2. Additionally, as suggested by the reviewer, we also noticed lack of details in Methods section of the submitted manuscript, concerning siRNA mediated Knock down (KD). Therefore, we plan to include more details in the revised manuscript, which will read as, “For all siRNA transfections, Lipofectamine® RNAiMAX Reagent (Life Technologies, 13778100) specifically designed for knockdown assays in primary cells was used according to the manufacturer's instructions with slight modifiction. PECs were seeded into 24-well plates at a density of 1x10⁵ per well, and incubated at 37°C with 5% CO2. The transfection complex, comprising (1µl Lipofectamine® RNAiMAX and 50µl Opti MEM) and (1 µl siRNA and 50µl Opti MEM) mixed together directly added to the incubated PECs. Gene silencing was checked by IFA and by Western blot as mentioned previously”.

Author response image 2.

SiRNA-mediated gene knockdown analysis. (A-i, A-ii) Representative immunofluorescence microscopy image and corresponding Western blot analysis demonstrating the knockdown efficiency of NPC1 following SiRNA-mediated gene silencing, scale bar 10µm. (B-i, B-ii) Immunofluorescence image and Western blot confirming LDLr knockdown upon SiRNA treatment. Scrambled RNA (ScRNA) was used as a negative control, while Small Interfering RNA (SiRNA) specifically targeted NPC1 and LDLr transcripts, scale bar 10µm. TR-1 and TR-2 represent independent experimental trials. β-Actin was used as an endogenous loading control for Western blot normalization.

Minor issues

(1) There is an implication that parasite replication occurs well before 24hrs post-infection? Studies on Leishmania parasite replication have reported on the commencement of replication after 24hrs post-infection of macrophages (PMCID: PMC9642900). Is this dramatic increase in parasite numbers that they observed due to early parasite replication?

We thank the reviewer for this insightful comment and appreciate the opportunity to clarify our findings. Indeed, as rightly assumed by the Reviewer, as our data suggest, and we also believe that this increase intracellular amastigotes number is a consequence of early replication of Leishmania donovani.  As already mentioned in response to Point number 3 raised by Reviewer 1, we would again like to highlight that in the Methods section (lines 562–566), it is clearly stated: "Flow-sorted metacyclic LD promastigotes were used at a MOI of 1:10 (with variations of 1:5 and 1:20 in some cases) for 4 hours, which was considered the 0th point of infection. Macrophages were subsequently washed to remove any extracellular loosely attached parasites and incubated further as per experimental requirements.” This effectively means that our actual study points correspond to approximately the 8th and 28th hours post-infection and we just want to mention it to avoid any confusion.

Now, regarding specific concern, the study referred by the reviewer on the commencement of replication after 24hrs, was conducted on Leishmania major, which may differ significantly from Leishmania donovani owing to its species and strain-specific characteristics.  In fact, doubling time of Leishmania donovani (LD) has been previously reported to be approximately 11.4 hours (doi: 10.1111/j.1550-7408. 1990.tb01147.x).  Moreover, multiple studies have indicated an exponential increase in intracellular LD amastigote number (more than two-fold increase) by 24hrs post infection. However, by 48hrs post-infection, the replication rate appeared to slow down, with amastigote numbers not increasing (doubling) proportionally (doi:10.1128/AAC.01196-07, doi.org/10.1016/j.ijpara.2011.07.013). We also have a similar observation for both infected PEC and KC as depicted in Figure 1Ci and Figure S1Ci in the Submitted manuscript) along with Author response image 3. Hence it was an informed decision from our side to focus on 24 hours’ time point to perform the analysis on intracellular proliferation.

Author response image 3.

Graph representing number of intracellular LD-R (MHOM/IN/2009/BHU575/0) parasite burden at different time points post-infection. *** signifies p value < 0.0001, * signifies p value < 0.05.

(2) Several of the fluorescence images in the paper are difficult to see. It would be helpful if a blown-up (higher magnification image of images in Figure 1 (especially D) for example) is presented.

We apologise for the inconvenience. Although we have provided Zoomed images for several Figures in the Submitted manuscript, like Figure 4, Figure 5, Figure 6 and Figure 8. However, this was not always doable for all the figures (like for Figure 1D), due to lack of space and Figure arrangements requirements. However, to accommodate Reviewer’s request we would like to provide a blown-up image for Figure 1D as represented in Author response image 4 in the Revised version. If the reviewer similar representation for any other particular Figures, we will be happy to perform a similar presentation.

Author response image 4.

Three-Dimensional morphometric representation of Parasitophorous Vacuoles (PVs) in Leishmania infected Kupffer Cells at 24 Hours Post-Infection: Confocal 3D reconstruction illustrating the spatial distribution of parasitophorous vacuoles (PVs) in Kupffer cells (KCs) infected for 24 hours. ATP6V0D2, a lysosomal vacuolar ATPase subunit, is visualized in magenta, while the nucleus is depicted in cyan. The final panel highlights PV structural grooves outlined in red solid lines, with intracellular Leishmania donovani (LD) amastigotes indicated by white arrows. Higher magnification of Figure 1D further emphasizes the increased abundance of PVs in LD-R infected cells, suggesting enhanced intracellular replication and adaptation mechanisms of drug-resistant strains. Scale bar 5µM. Both yellow and magenta solid line box represents the same area of the image.

(3) The times at which they choose to evaluate their infections seem arbitrary. It is not clear why they stopped analysis of their KC infections at 24 hrs. As mentioned above, several studies have shown that this is when intracellular amastigotes start replicating. They should consider extending their analyses to 48 or 72 hrs post-infection. Also, they stop in vitro infection of Apoe-/- mice at 11 days. Why? No explanation is given for why only 1 point after infection.

Reviewer has raised two independent concerns and we would like to address them individually.

Firstly, “The times at which they choose to evaluate their infections seem arbitrary. It is not clear why they stopped analysis of their KC infections at 24 hrs. As mentioned above, several studies have shown that this is when intracellular amastigotes start replicating. They should consider extending their analyses to 48 or 72 hrs post-infection.”

We have already provided a detail justification for time point selection in our response to Reviewer Minor Comment 1. As mentioned already we observed a significant and sharp rise in the number of intracellular amastigotes between 4 and 24Hrs post-infection (Author response image 4), with replication rate appeared to be not increaseing proportionally after that. This early stage of rapid replication of LD amastigotes, therefore likely coincides with a critical period of lipid acquisition by intracellular amastigotes (Movie 2A and 2B and Figure 4E in the submitted manuscript) and thus 24hrs infected KC was specifically selected. In this regard, we would also like to add that at 72hrs post-infection, we noticed a notable number of infected Kupffer cells began detaching from the wells with extracellular amastigotes probably egressing out from the infected KCs. This phenomenon potentially reflects the severe impact of prolonged infection on Kupffer cell viability and adhesion properties as shown in Author response image 5 and Author Response Video 1. This point further influenced our decision to conclude all infection studies in Kupffer cells by the 48Hrs post-infection, which necessitate to complete the infection time point at 24 Hrs, for allowing treatment of Amp-B for another 24 Hrs (Figure 8, and Figure S5, in the Submitted manuscript). We acknowledge that we should have been possibly more clear on our selection of time points and as the Reviewer have suggested we plan to include this information in the revised manuscript for clear understanding of the reader.

Author response image 5.

Representative images of Kupffer cells infected with Leishmania donovani at 72Hrs post-infection showing a significant morphological changes. Infected cells exhibit a rounded morphology and progressive detachment. Scale bar 10µm.

Secondly “Also, they stop in vitro infection of Apoe-/- mice at 11 days. Why? No explanation is given for why only 1 point after infection.”

We apologize for not providing an explanation regarding the selection of the 11-day time point for Apoe-/- experiments (Figure 2 of the Submitted manuscript). Our rationale for this choice is based on both previous literature and the specific objectives of our study. Previous report suggests that Leishmania donovani infection in Apoe-/- mice triggers a heightened inflammatory response at approximately six weeks’ post-infection compared to C57BL/6 mice, leading to more efficient parasite clearance. This is owing to unique membrane composition of Apoe-/- which rectifies leishmania mediated defective antigen presentation at a later stage of infection (DOI 10.1194/jlr.M026914). Additionally, previous studies (doi: 10.1128/AAC.47.5.1529-1535.2003) have also indicated that Leishmania donovani infection is well-established in vivo within 6 to 11 days post-infection in murine models. Given that in this experiment we particularly aimed to assess the early infection status (parasite load) in diet-induced hypercholesterolemic mice, we would like to argue that the selection of the 11-day time point was intentional and well-aligned with our study objectives as this time point within this window are optimal for capturing initial parasite burden depending on initial lipid utilization, before host-driven immune clearance mechanisms could significantly alter infection dynamics. We will include this explanation in the Revised manuscript as suggested by the Reviewer.

Reviewer #2 (Public review):

Summary:

This study by Pradhan et al. offers critical insights into the mechanisms by which antimony-resistant Leishmania donovani (LD-R) parasites alter host cell lipid metabolism to facilitate their own growth and, in the process, acquire resistance to amphotericin B therapy. The authors illustrate that LD-R parasites enhance LDL uptake via fluid-phase endocytosis, resulting in the accumulation of neutral lipids in the form of lipid droplets that surround the intracellular amastigotes within the parasitophorous vacuoles (PV) that support their development and contribute to amphotericin B treatment resistance. The evidence provided by the authors supporting the main conclusions is compelling, presenting rigorous controls and multiple complementary approaches. The work represents an important advance in understanding how intracellular parasites can modify host metabolism to support their survival and escape drug treatment.

We would like to sincerely thank the reviewer for appreciating our work and find the evidence compelling to address the issue of emergence of drug resistance in infection with intracellular protozoan pathogens. Before we submit a full revision of the paper, we would like to provide a primary response addressing the concerns of the reviewer.

Strengths:

(1) The study utilizes clinical isolates of antimony-resistant L. donovani and provides interesting mechanistic information regarding the increased LD-R isolate virulence and emerging amphotericin B resistance.

(2) The authors have used a comprehensive experimental approach to provide a link between antimony-resistant isolates, lipid metabolism, parasite virulence, and amphotericin B resistance. They have combined the following approaches:

(a) In vivo infection models involving BL/6 and Apoe-/- mice.

(b) Ex-vivo infection models using primary Kupffer cells (KC) and peritoneal exudate macrophages (PEC) as physiologically relevant host cells.

(c) Various complementary techniques to ascertain lipid metabolism including GC-MS, Raman spectroscopy, microscopy.

(d) Applications of genetic and pharmacological tools to show the uptake and utilization of host lipids by the infected macrophage resident L. donovani amastigotes.

(3) The outcome of this study has clear clinical significance. Additionally, the authors have supported their work by including patient data showing a clear clinical significance and correlation between serum lipid profiles and treatment outcomes.

(4) The present study effectively connects the basic cellular biology of host-pathogen interactions with clinical observations of drug resistance.

(5) Major findings in the study are well-supported by the data:

(a) Intracellular LD-R parasites induce fluid-phase endocytosis of LDL independent of LDL receptor (LDLr).

(b) Enhanced fusion of LDL-containing vesicles with parasitophorous vacuoles (PV) containing LD-R parasites both within infected KCs and PECs cells.

(c) Intracellular cholesterol transporter NPC1-mediated cholesterol efflux from parasitophorous vacuoles is suppressed by the LD-R parasites within infected cells.

(d) Selective exclusion of inflammatory ox-LDL through MSR1 downregulation.

(e) Accumulation of neutral lipid droplets contributing to amphotericin B resistance.

Weaknesses:

The weaknesses are minor:

(1) The authors do not show how they ascertain that they have a purified fraction of the PV post-density gradient centrifugation.

(2) The study could have benefited from a more detailed analysis of how lipid droplets physically interfere with amphotericin B access to parasites.

We have addressed both these concerns as our preliminary response in details in subsequent “Recommendations for the Authors section” before we submit a complete Revised manuscript,

Impact and significance:

This work makes several fundamental advances:

(1) The authors were able to show the link between antimony resistance and enhanced parasite proliferation.

(2) They were also able to reveal how parasites can modify host cell metabolism to support their growth while avoiding inflammation.

(3) They were able to show a certain mechanistic basis for emerging amphotericin B resistance.

(4) They suggest therapeutic strategies combining lipid droplet inhibitors with current drugs.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) Experimental suggestions:

a) The authors could have provided a more detailed analysis of lipid droplet composition. This is a critically missing piece in this nice study.

We completely agree with the reviewer on this, a more detailed analysis of lipid droplets composition, dynamics of its formation and mechanism of lipid transfer to amastigotes residing within the PV would be worthy of further investigation.  To answer the reviewers, we are already conducting investigation in this direction and have very promising initial results which we are willing to share with the reviewer as unpublished data if requested. Since, we plan to address these questions independently, we hope reviewer will understand our hesitation to include these data into the present work which is already immensely data dense. We sincerely believe existence of lipid droplet contact sites with the PV along with the specific lipid type transfer to amastigotes and its mechanism requires special attention and could stand out as an independent work by itself.

b) The macrophages (PEC, KC) could have been treated with latex beads as a control, which would indicate that cholesterol and lipids are indeed utilized by the Leishmania parasitophorous vacuole (PV) and essential for its survival and proliferation.

We thank the reviewer for this nice suggestion, which we believe will further strengthen the conclusion of this work. This has also been suggested by Reviewer 1 and we are planning to conduct this experiment and will include this data in the revised version of this manuscript.

c) HMGCoA reductase is an important enzyme for the mevalonate pathway and cholesterol synthesis. The authors have not commented on this enzyme in either host or parasite. Additionally, western blots of these enzymes along with SREBP2 could have been performed.

We appreciate the concern and do see the point why reviewer is suggesting this. We would like to mention that regarding HMGCoA we already do have real time qPCR data which perfectly aligns with our RNAseq data (Figure 6 Ai, in the Submitted manuscript), showing significant downregulation specifically in LD-R infected KC as compared to uninfected control. We are including this data as Author response image 6.  However, we did not proceed with checking the level of HMGCoA at the protein level as we noticed several previous reports have suggested that HMGCoA remains under transcriptional control of SERBP2(doi.org/10.1016/j.cmet.2011.03.005,doi: 10.1194/jlr.C066712,doi:10.1194/jlr.RA119000201), which acts the master regulator of mevalonate pathway and cholesterol synthesis (doi.org/10.1161/ATVBAHA.122.317320).  However, as suggested by the Reviewer, we will perform this experiment and will update the Revised manuscript with the expression data on HMGCoA probably in the Supplementary section

Author response image 6.

qPCR Analysis of HMGCR Expression Following Leishmania donovani Infection: Quantitative PCR analysis showing the relative expression of hmgcr (3-hydroxy-3-methylglutaryl-CoA reductase) in Kupffer cells after 24 hours of Leishmania donovani (LD) infection compared to uninfected control cells. Gene expression levels are normalized to β-actin as an internal control, and fold change is represented relative to the uninfected condition.

d) The authors should discuss the expression pattern of any enzyme of the mevalonate pathway that they have found to be dysregulated in the transcript data.

As per the reviewer’s suggestion, we have already looked into the RNA seq data and observed that apart from hmgcr, hmgcs (_3-hydroxy-3-methylglutaryl-CoA synthase), another key enzyme in the mevalonate pathway, is significantly downregulated in host PECs in response to LD-R infection compared to the LD-S infection.  We will update this in the Discussion section of the Revised manuscript, which will read as “Further analysis of RNA sequencing data revealed a significant downregulation of _hmgcs (3-hydroxy-3-methylglutaryl-CoA synthase) in LD-R infected PECs as compared to LD-S infecton. HMGCS which catalyzes the condensation of acetyl-CoA with acetoacetyl-CoA to form 3-hydroxy-3-methylglutaryl-CoA (HMG-CoA), which serves as an intermediate in both cholesterol biosynthesis and ketogenesis. The downregulation of hmgcs further supports our observation that LD-R-infected PECs preferentially rely on endocytosed low-density lipoprotein (LDL)-derived cholesterol rather than de novo synthesized cholesterol for their metabolic needs.”

e) The authors have followed a previously published protocol by Real F (reference 73) to enrich for parasitophorous vacuole (PV). However, they do not show how they ascertain that they have a purified fraction of the PV post-density gradient centrifugation. The authors should at least show Western blot data for LAMP1 for different fractions of density gradient from which they enriched the PV.

As we previously stated in our response to Reviewer 1, the Revised manuscript will include a detailed analysis of purity for different fractions during PV isolation. We sincerely appreciate the reviewer for highlighting this important concern and for suggesting an approach to conduct the experiment. We believe this experiment is crucial and will further reinforce the conclusions of our study.

(2) Presentation improvements:

a) Add a clear timeline for infection experiments.

Sure. We will be including a schematic of Timelines in the revised figures 2 and 7

b) Provide more details on patient sample collection and analysis.

We plan to include more details on the sample collection in the Method section of the Revised manuscript as follows, “Blood samples were collected from a total of 22 individuals spanning a diverse age range (8 to 70 years) by RMRI, Bihar, India. Among these, nine samples were obtained from healthy individuals residing in endemic regions to serve as controls. Serum was isolated from each blood sample through centrifugation, and the lipid profile was subsequently analysed using a specialized diagnostic kit (Coral Clinical System) following the manufacturer's protocol.”

c) Consider reorganizing figures to better separate mechanistic and clinical findings.

We would like to thank the reviewer for this suggestion. However, we feel that the arrangement of the Figures as presented in the Original Submission is really helping a smooth flow of the story and hence, we would not want to disturb that. However, having said that, if the reviewer has specific suggestion regarding rearrangement of any particular figure, we will be happy to consider that.

(3) Technical clarifications needed:

a) Specify exact concentrations used for inhibitors.

We apologise for this unwanted and unnecessary mistake. Please note we will clearly mention the concentration of all the inhibitors used in this study in Result section and in Revised Figure legends. The revised section will read as, “Finally, we infected the KCs with GFP expressing LD-R for 4Hrs, washed and allowed the infection to proceed in presence of fluorescent red-LDL and Latrunculin-A ( 5µM), a compound  which specifically inhibits fluid phase endocytosis by inducing actin depolymerization [41]. Real-time fluorescence tracking demonstrated that Latrunculin-A treatment not only prevented the uptake of fluorescent red-LDL but also severely impacted intracellular proliferation of LD-R amastigotes (Movie 2A and 2B and Figure 4E). In contrast, treatment with Cytochalasin-D (2.5µg/ml), which alters cellular F-actin organization but does not affect fluid phase endocytosis”

b) Include more details on image analysis methods.

Please note that in specific sections like in Line numbers 574-579, 653-658, 1047-1049 of the Submitted manuscript, we have put special attention in describing the Image analysis process. However, we agree that in some particular cases more details will be appreciated by the reader. Hence we will be including an additional section of Image Analysis in the Methods section of the revised manuscript. This section will read as, “Image processing and analysis were conducted using Fiji (ImageJ). For optimal visualization, Giemsa-stained macrophages (MΦs) were represented in grayscale to enhance contrast and structural clarity. To improve the distinction of different fluorescent signals, pseudo-colors were assigned to fluorescence images, ensuring better differentiation between various cellular components. For colocalization analysis (Figures 3, 5, 6, and S2), we utilized the RGB profile plot plugin in ImageJ, which allows for the precise assessment of signal overlap by generating fluorescence intensity profiles across selected regions of interest. This approach provided quantitative insights into the spatial relationship between labeled molecules within infected cells. Additionally, for analyzing the distribution of cofilin in Figure 4, the ImageJ surface plot plugin was employed. This tool enabled three-dimensional visualization of fluorescence intensity variations, facilitating a more detailed examination of cofilin localization and its potential reorganization in response to infection.”

c) Clarify statistical analysis procedures.

Response: We have already provided a dedicated section of Statistical Analysis in the Methods section and also have also shown the groups being compared to determine the statistical analysis in the Figure and in the Figure Legends of the Submitted manuscript. Furthermore, we plan to add additional clarification regarding the statistical analysis performed Revised manuscript. For example, in the Revised manuscript this section will read as, “All statistical analyses were performed using GraphPad Prism 8 on raw datasets to ensure robust and reproducible results. For datasets involving comparisons across multiple conditions, one-way or two-way analysis of variance (ANOVA) was conducted, followed by Tukey’s post hoc test to assess pairwise differences while controlling for multiple comparisons. A 95% confidence interval (CI) was applied to determine the statistical reliability of the observed differences. For non-parametric comparisons across multiple groups, Wilcoxon rank-sum tests were employed, maintaining a 95% confidence interval, which is particularly useful for analysing skewed data distributions. In cases where only two groups were compared, Student’s t-test was used to determine statistical significance, ensuring an accurate assessment of mean differences. All quantitative data are represented as mean ± standard error of the mean (SEM) to illustrate variability within experimental replicates. Statistical significance was determined at P ≤ 0.05. Notation for significance levels: *P ≤ 0.05; **P ≤ 0.001; ***P ≤ 0.0001.”

(4) Minor corrections:

a) Methods section could benefit from more details on Raman spectroscopy analysis.

We agree with this suggestion of the Reviewer. For providing more clarity we will incorporate additional details in the Methodology for the Raman section of the Revised manuscript. The updated section will read as follows in the revised manuscript. “For confocal Raman spectroscopy, spectral data were acquired from individual cells at 1000× magnification using a 100 × 100 μm scanning area, following previously established specifications. After spectral acquisition, distinct Raman shifts corresponding to specific biomolecular signatures were extracted for further analysis. These included: Cholesterol (535–545 cm⁻¹), Nuclear components (780–790 cm⁻¹), Lipid structures (1262–1272 cm⁻¹), Fatty acids (1436–1446 cm⁻¹) Following spectral extraction, pseudo-color mapping was applied to highlight the spatial distribution of each biomolecular component within the cell. These processed spectral images are presented in Figure 3D1, where the first four panels illustrate the individual biomolecular distributions. A merged composite image was then generated to visualize the co-localization of these biomolecules within the cellular microenvironment, with the final panel specifically representing the spatial distribution of key biomolecules.”

b) In the methods section line 609, page 14, the authors cite Real F protocol as reference 73 for PV enrichment. However, in the very next section on GC-MS analysis (lines 615-616, page 15), they state they have used reference 74 for PV enrichment. Can they explain why a discrepancy in PV isolation references this? Reference 74 does not mention anything related to PV isolation.

We would like to sincerely apologise for this confusion which probably raised from our writing of this section. We would like to confirm that our PV isolation protocol is based on the published work of Real F protocol (reference 73). However, in the next section of the submitted manuscript, GC-MS analysis was described and that was performed based on protocol referenced in 74. In the Revised manuscript, we will avoid this confusion and made correction by putting the references in the proper places. Revised section will read as,

“GC-MS analysis of LD-S and LD-R-PV

Following a 24Hrs infection period, KCs were harvested, washed with phosphate-buffered saline (PBS), and pelleted. Subsequent to this, PV isolation was carried out using the previously described method [73]. The resulting parasitophorous vacuole (PV) pellet was processed for sterol isolation for GC_MS analysis following a previously established protocol [74], with slight modification. Briefly, the PV pellet was resuspended in 20 ml of dichloromethane:methanol (2:1, vol/vol) and incubated at 4°C for 24hours. After centrifugation (11,000 g, 1 hour, 4°C), the supernatant was checked through thin layer chromatography (TLC) and subsequently evaporated under vacuum. The residue and pellet were saponified with 30% potassium hydroxide (KOH) in methanol at 80°C for 2 hours. Sterols were extracted with n-hexane, evaporated, and dissolved in dichloromethane. A portion of the clear yellow sterol solution was treated with N, O-bis(trimethylsilyl)trifluoroacetamide (BSTFA) and heated at 80°C for 1 hour to form trimethylsilyl (TMS) ethers. Gas chromatography/mass spectrometry (GC/MS) analysis was performed using a Varian model 3400 chromatograph equipped with DB5 columns (methyl-phenylsiloxane ratio, 95/5; dimensions, 30 m by 0.25 mm). Helium was used as the gas carrier (1 ml/min). The column temperature was maintained at 270°C, with the injector and detector set at 300°C. A linear gradient from 150 to 180°C at 10°C/min was used for methyl esters, with MS conditions set at 280°C, 70 eV, and 2.2 kV.”

Author response:

Public Reviews:

Reviewer #1 (Public Review):

In the manuscript by Su et al., the authors present a massively parallel reporter assay (MPRA) measuring the stability of in vitro transcribed mRNAs carrying wild-type or mutant 5' or 3' UTRs transfected into two different human cell lines. The goal presented at the beginning of the manuscript was to screen for effects of disease-associated point mutations on the stability of the reporter RNAs carrying partial human 5' or 3' UTRs. However, the majority of the manuscript is dedicated to identifying sequence components underlying the differential stability of reporter constructs. This shows that TA dinucleotides are the most predictive feature of RNA stability in both cell lines and both UTRs.

The effect of AU rich elements (AREs) on RNA stability is well established in multiple systems, and the present study confirms this general trend but points out variability in the consequence of seemingly similar motifs on RNA stability. For example, the authors report that a long stretch of Us has extreme opposite effects on RNA stability depending on whether it is preceded by an A (strongly destabilizing) or followed by an A (strongly stabilizing). While the authors interpretation of a context- dependence of the effect is certainly well-founded, it seems counterintuitive that the preceding or following A would be the (only) determining factor. This points to a generally reductionist approach taken by the authors in the analysis of the data and in their attempt to dissect the contribution of "AU rich sequences" to RNA stability, with a general tendency to reduce the size and complexity of the features (e.g. to dinucleotides). While this certainly increases the statistical power of the analysis due to the number of occurrences of these motifs, it limits the interpretability of the results. How do TA dinucleotides per se contribute to destabilizing the RNA, both in 5' and 3' UTRs, but (according to limited data presented) not in coding sequences? What is the mechanism? RBPs binding to TA dinucleotide containing sequences are suggested to "mask" the destabilizing effect, thereby leading to a more stable RNA. Gain of TA dinucleotides is reported to have a destabilizing effect, but again no hypothesis is provided as to the underlying molecular mechanism. In addition to reducing the motif length to dinucleotides, the notion of "context dependence" is used in a very narrow sense; especially when focusing on simple and short motifs, a more extensive analysis of the interdependence of these features (beyond the existing analysis of the relationship between TA- diNTs and GC content) could potentially reveal more of the context dependence underlying the seemingly opposite behavior of very similar motifs.

The contribution of coding region sequence to RNA stability has been extensively discussed (For example: doi.org/10.1016/j.molcel.2022.03.032; doi.org/10.1186/s13059-020-02251-5; doi.org/10.15252/embr.201948220; doi.org/10.1371/journal.pone.0228730; doi.org/10.7554/eLife.45396). While TA content at the third codon position (wobble position) has been implicated as a pro-degradation signal, codon optimality has emerged as the most prominent determinant for RNA stability. This indicates that the role of coding regions in RNA stability differs from that of UTRs due to the involvement of translation elongation. We did not intend to suggest that TA-dinucleotides in UTRs and coding regions have the same effect.

We hypothesize that TA-dinucleotide may recruit endonucleases RNase A family, whose catalytic pockets exhibit a strong bias for TA dinucleotide (doi.org/10.1016/j.febslet.2010.04.018). Structures or protein bindings that blocks this recognition might stabilize RNAs. To gain further insight into the motif interactions, we plan to investigate the interactions between TA and other 15 dinucleotides through more detailed analyses.

The present MPRAs measures the effect of UTR sequences in one specific reporter context and using one experimental approach (following the decay of in vitro transcribed and transfected RNAs). While this approach certainly has its merits compared to other approaches, it also comes with some caveats: RNA is delivered naked, without bound RBPs and no nuclear history, e.g. of splicing (no EJCs), editing and modifications. One way to assess the generalizability of the results as well as the context dependence of the effects is to perform the same analysis on existing datasets of RNA stability measurements obtained through other methods (e.g. transcription inhibition). Are TA dinucleotides universally the most predictive feature of RNA half-lives?

Our system studies the stability control of RNA synthesized in vitro and delivered into human cells. While we did not intend to generalize our conclusions to endogenous RNAs, our approach contributes to the understanding of in vitro synthesized RNA used for cellular expression, such as in vaccines. It is known that endogenous RNAs undergo very different regulation. The most prominent factors controlling endogenous RNA stability are the density of splice junctions and the length of UTRs (doi.org/10.1186/s13059-022-02811-x; doi.org/10.1186/s12915-021-00949-x). To decipher the sequence regulation, these factors are controlled in our experiments. Therefore we do not expect the dinucleotide features found by our approach to be generalized as the most predictive feature of RNA half-life in vivo.

The authors conclude their study with a meta-analysis of genes with increased TA dinucleotides in 5' and 3'UTRs, showing that specific functional groups are overrepresented among these genes. In addition, they provide evidence for an effect of disease-associated UTR mutations on endogenous RNA stability. While these elements link back to the original motivation of the study (screening for effects of point mutations in 5' and 3' UTRs), they provide only a limited amount of additional insights.

We utilized the Taiwan Biobank to investigate whether mutations significantly affecting RNA stability also impact human biochemical measurements. Our findings indicate that these mutations indeed have a significant effect on various biochemical indices. This highlights the importance of our study, as it bridges basic science with potential applications in precision medicine. By linking specific UTR mutations with measurable changes in biochemical indices, our research underscores the potential for these findings to inform targeted medical interventions in the future.

In summary, this manuscript presents an interesting addition to the long-standing attempts at dissecting the sequence basis of RNA stability in human cells. The analysis is in general very comprehensive and sound; however, at times the goal of the authors to find novelty and specificity in the data overshadows some analyses. One example is the case where the authors try to show that TA-dinucleotides and GC content are decoupled and not merely two sides of the same coin. They claim that the effect of TA dinucleotides is different between high- and low-GC content contexts but do not control for the fact that low GC-content regions naturally will contain more TA dinucleotides and therefore the effect sizes and the resulting correlation between TA-diNT rate and stability will be stronger (Fig. 5A). A more thorough analysis and greater caution in some of the claims could further improve the credibility of the conclusions.

Low GC content implies a higher TA content but does not directly equate to a high TA-diNT rate. For instance, the sequence ATTGAACCTT has a lower GC content (0.3) compared to TATAGGCCGC (0.6), yet it also has a lower TA-diNT rate (0 vs. 0.22). To address this concern more rigorously, we performed a stratified analysis based on TA-diNT rate. As shown in our Fig. S7C, even after stratifying by TA-diNT rate (upper panel high TA-diNT rate / lower panel low TA-diNT rate), we still observe that the destabilizing effect of TA is stronger in the low GC content group.

Reviewer #2 (Public Review):

Summary of goals:

Untranslated regions are key cis-regulatory elements that control mRNA stability, translation, and translocation. Through interactions with small RNAs and RNA binding proteins, UTRs form complex transcriptional circuitry that allows cells to fine-tune gene expression. Functional annotation of UTR variants has been very limited, and improvements could offer insights into disease relevant regulatory mechanisms. The goals were to advance our understanding of the determinants of UTR regulatory elements and characterize the effects of a set of "disease-relevant" UTR variants.

Strengths:

The use of a massively parallel reporter assay allowed for analysis of a substantial set (6,555 pairs) of 5' and 3' UTR fragments compiled from known disease associated variants. Two cell types were used.

The findings confirm previous work about the importance of AREs, which helps show validity and adds some detailed comparisons of specific AU-rich motif effects in these two cell types.

Using a Lasso regression, TA-dinucleotide content is identified as a strong regulator of RNA stability in a context dependent manner based on GC content and presence of RNA binding protein binding motifs. The findings have potential importance, drawing attention to a UTR feature that is not well characterized.

The use of complementary datasets, including from half-life analyses of RNAs and from random sequence library MRPA's, is a useful addition and supports several important findings. The finding the TA dinucleotides have explanatory power separate from (and in some cases interacting with) GC content is valuable.

The functional enrichment analysis suggests some new ideas about how UTRs may contribute to regulation of certain classes of genes.

Weaknesses:

It is difficult to understand how the calculations for half-life were performed. The sequencing approach measures the relative frequency of each sequence at each time point (less stable sequences become relatively less frequent after time 0, whereas more stable sequences become relatively more frequent after time 0). Since there is no discussion of whether the abundance of the transfected RNA population is referenced to some external standard (e.g., housekeeping RNAs), it is not clear how absolute (rather than relative) half-lives were determined.

We estimated decay constant λ and half-life () by the following equations:

where Ci(t) and Ci(t=0) are read count values of the ith replicate at time points  and  (see also Methods). The absolute abundance was not required for the half-life calculation.

Fig. S1A and B are used to assess reproducibility. They show that read counts at a given time point correlate well across replicate experiments. However, this is not a good way to assess reproducibility or accuracy of the measurements of t1/2 are. (The major source of variability in read counts in these plots - especially at early time points - is likely the starting abundance of each RNA sequence, not stability.) This creates concerns about how well the method is measuring t1/2. Also creating concern is the observation that many RNAs are associated with half-lives that are much longer than the time points analyzed in the study. For example, based upon Figure S1 and Table S1 correctly, the median t1/2 for the 5' UTR library in HEK cells appears to be >700 minutes. Given that RNA was collected at 30, 75, and 120 minutes, accurate measurements of RNAs with such long half lives would seem to be very difficult.

We estimated the half-life based on the following equations:

Where Ci(t) and Ci(t=0) are read count values of the ith replicate at time points  and  (see also Methods). The calculation of the half-life involves first determining the decay constant 𝜆, which represents a constant rate of decay. Since 𝜆 is a constant, it is possible to accurately calculate it without needing data over the entire decay range. Our experimental design considers this by selecting appropriate time points to ensure a reliable estimation of 𝜆, and thus, the half-life. To determine the most suitable time points, we conducted preliminary experiments using RT-PCR. These experiments indicated that 30, 75, and 120 minutes provided an effective range for capturing the decay dynamics of the transcripts.

There is no direct comparison of t1/2 between the two cell types studied for the full set of sequences studied. This would be helpful in understanding whether the regulatory effects of UTRs are generally similar across cell lines (as has been shown in some previous studies) or whether there are fundamental differences. The distribution of t1/2's is clearly quite different in the two cell lines, but it is important to know if this reflects generally slow RNA turnover in HEK cells or whether there are a large number of sequence-specific effects on stability between cell lines. A related issue is that it is not clear whether the relatively small number of significant variant effects detected in HEK cells versus SH-SY5Y cells is attributable to real biological differences between cell types or to technical issues (many fewer read counts and much longer half lives in HEK cells).

For both cell lines, we selected oligonucleotides with R2 > 0.5 and mean squared error (MSE) < 1 for analysis when estimating half-life (λ) by linear regression. This selection criterion was implemented to minimize the effect of experimental noise. Additionally, we will further analyze the MSE distribution to determine if the two cell lines exhibit significantly different levels of experimental noise. We will also provide a direct comparison of half-lives between the two cell lines to assess the similarity in stability regulation.

The general assertion is made in many places that TA dinucleotides are the most prominent destabilizing element in UTRs (e.g., in the title, the abstract, Fig. 4 legend, and on p. 12). This appears to be true for only one of the two cell lines tested based on Fig. 3.

TA-dinucleotides and other TA-rich sequences exhibit similar effects on RNA stability, as illustrated in Fig. S5A-C. In two cell lines, TA-dinucleotide and WWWWWW sequences were representatives of the same stability-affecting cluster. While the impact of TA-dinucleotides can be generalized, we will rephrase some statements for clarification to avoid any potential misunderstanding.

Appraisal and impact:

The work adds to existing studies that previously identified sequence features, including AREs and other RNA binding protein motifs, that regulate stability and puts a new emphasis on the role of "TA" (better "UA") dinucleotides. It is not clear how potential problems with the RNA stability measurements discussed above might influence the overall conclusions, which may limit the impact unless these can be addressed.

It is difficult to understand whether the importance of TA dinucleotides is best explained by their occurrence in a related set of longer RBP binding motifs (see Fig 5J, these motifs may be encompassed by the "WWWWWW cluster") or whether some other explanation applies. Further discussion of this would be helpful. Does the LASSO method tend to collapse a more diverse set of longer motifs that are each relatively rare compared to the dinucleotide? It remains unclear whether TA dinucleotides are associated with less stability independent of the presence of the known larger WWWWWWW motif. As noted above, the importance of TA dinucleotides in the HEK experiments appears to be less than is implied in the text.

To ensure the representativeness of the features entered into the LASSO model, we pre-selected those with an occurrence greater than 10% among all UTRs. There is no evidence to support a preference for dinucleotides by LASSO. To address whether the destabilizing effect of TA dinucleotides is part of the broader WWWWWW motif, we will divide TA dinucleotides into two groups: those within the WWWWWW motif and those outside of it. We will then examine whether TA dinucleotides in these two groups exhibit the same destabilizing effect.

The inclusion of more than a single cell type is an acknowledgement of the importance of evaluating cell type-specific effects. The work suggests a number of cell type-specific differences, but due to technical issues (especially with the HEK data, as outlined above) and the use of only two cell lines, it is difficult to understand cell type effects from the work.

The inclusion of both 3' and 5' UTR sequences distinguishes this work from most prior studies in the field. Contrasting the effects of these regions on stability is of interest, although the role of these UTRs (especially the 5' UTR) in translational regulation is not assessed here.

We examined the role of UTR and UTR variants in translation regulation using polysome profiling. By both univariate analysis and an elastic regression model, we identified motifs of short repeated sequences, including SRSF2 binding sites, as mutation hotspots that lead to aberrant translation. Furthermore, these polysome-shifting mutations had a considerable impact on RNA secondary structures, particularly in upstream AUG-containing 5’ UTRs. Integrating these features, our model achieved high accuracy (AUROC > 0.8) in predicting polysome-shifting mutations in the test dataset. Additionally, metagene analysis indicated that pathogenic variants were enriched at the upstream open reading frame (uORF) translation start site, suggesting changes in uORF usage underlie the translation deficiencies caused by these mutations. Illustrating this, we demonstrated that a pathogenic mutation in the IRF6 5’ UTR suppresses translation of the primary open reading frame by creating a uORF. Remarkably, site-directed ADAR editing of the mutant mRNA rescued this translation deficiency. Because the regulation of translation and stability does not converge, we illustrate these two mechanisms in two separate manuscripts (this one and doi.org/10.1101/2024.04.11.589132).

Reviewer #3 (Public Review):

Summary:

In their manuscript titled "Multiplexed Assays of Human Disease‐relevant Mutations Reveal UTR Dinucleotide Composition as a Major Determinant of RNA Stability" the authors aim to investigate

the effect of sequence variations in 3'UTR and 5'UTRs on the stability of mRNAs in two different human cell lines.

To do so, the authors use a massively parallel reporter assay (MPRA). They transfect cells with a set of mRNA reporters that contain sequence variants in their 3' or 5' UTRs, which were previously reported in human diseases. They follow their clearance from cells over time relative to the matching non-variant sequence. To analyze their results, they define a set of factors (RBP and miRNA binding sites, sequence features, secondary structure etc.) and test their association with differences in mRNA stability. For features with a significant association, they use clustering to select a subset of factors for LASSO regression and identify factors that affect mRNA stability.

They conclude that the TA dinucleotide content of UTRs is the strongest destabilizing sequence feature. Within that context, elevated GC content and protein binding can protect susceptible mRNAs from degradation. They also show that TA dinucleotide content of UTRs affects native mRNA stability, and that it is associated with specific functional groups. Finally, they link disease associated sequence variants with differences in mRNA stability of reporters.

Strengths:

(1) This work introduces a different MPRA approach to analyze the effect of genetic variants. While previous works in tissue culture use DNA transfections that require normalization for transcription efficiency, here the mRNA is directly introduced into cells at fixed amounts, allowing a more direct view of the mRNA regulation.

(2) The authors also introduce a unique analysis approach, which takes into account multiple factors that might affect mRNA stability. This approach allows them to identify general sequence features that affect mRNA stability beyond specific genetic variants, and reach important insights on mRNA stability regulation. Indeed, while the conclusions to genetic variants identified in this work are interesting, the main strength of the work involve general effect of sequence features rather than specific variants.

(3) The authors provide adequate supports for their claims, and validate their analysis using both their reporter data and native genes. For the main feature identified, TA di-nucleotides, they perform follow-up experiments with modified reporters that further strengthen their claims, and also validate the effect on native cellular transcripts (beyond reporters), demonstrating its validity also within native scenarios.

(4) The work provides a broad analysis of mRNA stability, across two mRNA regulatory segments (3'UTR and 5'UTR) and is performed in two separate cell-types. Comparison between two different cell-types is adequate, and the results demonstrate, as expected, the dependence of mRNA stability on the cellular context. Analysis of 3'UTR and 5'UTR regulatory effects also shows interesting differences and similarities between these two regulatory regions.

Weaknesses:

(1) The authors fail to acknowledge several possible confounding factors of their MPRA approach in the discussion.

First, while transfection of mRNA directly into cells allows to avoid the need to normalize for differences in transcription, the introduction of naked mRNA molecules is different than native cellular mRNAs and could introduce biases due to differences in mRNA modifications, protein associations etc. that may occur co-transcriptionally.

Second, along those lines, the authors also use in-vitro polyadenylation. The length of the polyA tail of the transfected transcripts could potentially be very different than that of native mRNAs and also affect stability.

The transcripts used in our study were polyadenylated in vitro with approximately 100 nucleotides  (Fig. S1C), similar to the polyA tail lengths typically observed in vivo  (dx.doi.org/10.1016/j.molcel.2014.02.007).  Additionally, these transcripts were capped to emulate essential mRNA characteristics and to minimize immune responses in recipient cells. This design allows us to study RNA decay for in vitro-synthesized RNA delivered into human cells, akin to RNA vaccines, but it does not necessarily extend to endogenous RNAs. As mentioned, endogenous RNAs undergo nuclear processing and are decorated by numerous trans factors, resulting in distinct regulatory mechanisms. We will provide a more in-depth discussion on these differences and their implications in the revised manuscript.

(2) The analysis approach used in this work for identifying regulatory features in UTRs was not previously used. As such, lack of in-depth details of the methodology, and possibly also more general validation of the approach, is a drawback in convincing the reader in the validity of this approach and its results.

In particular, a main point that is not addressed is how the authors decide on the set of "factors" used in their analysis? As choosing different sets of factors might affect the results of the analysis.

In our study, we employed the calculation of the Variance Inflation Factor (VIF) as a basis for selecting variables. This well-established method is widely used to detect variables with high collinearity, thus ensuring the robustness and reliability of our analysis. By identifying and excluding highly collinear variables, we aimed to minimize multicollinearity and improve the accuracy of our regression models. For more detailed information on the use of VIF in regression analysis, please refer to Akinwande, M., Dikko, H., and Samson, A. (2015). Variance Inflation Factor: As a Condition for the Inclusion of Suppressor Variable(s) in Regression Analysis. Open Journal of Statistics, 5, 754-767. doi: 10.4236/ojs.2015.57075. We will include the method details in the revised manuscript.

For example, the choice to use 7-mer sequences within the factors set is not explained, particularly when almost all motifs that are eventually identified (Figure 3B-E) are shorter.

The known RBP motifs are primarily 6-mer. To explore the possibility of discovering novel motifs that could significantly impact our model, we started with 7-mer sequences. However, our analysis revealed that including these additional variables did not improve the explanatory power of the model; instead, it reduced it. Consequently, our final model focuses on motifs shorter than 7-mer. We will explain the motif selections in the revised manuscript.

In addition, the authors do not perform validations to demonstrate the validity of their approach on simulated data or well-established control datasets. Such analysis would be helpful to further convince the reader in the usefulness and robustness of the analysis.

We acknowledge the importance of validating our approach on simulated data or well-established control datasets to demonstrate its robustness and reliability. However, to the best of our knowledge, there are currently no well-established control datasets available that perfectly correspond to our specific study context. Despite this, we will continue to search for any relevant datasets that could be utilized for this purpose in future work. This effort will help to further reinforce the confidence in our methodology and its findings.

(3) The analysis and regression models built in this work are not thoroughly investigated relative to native genes within cells. The effect of sequence "factors" on native cellular transcripts' stability is not investigated beyond TA di-nucleotides, and it is unclear to what degree do other predicted factors also affect native transcripts.

Our system studies the stability control of RNA synthesized in vitro and delivered into human cells. While we validated the UTR TA-dinucleotide effect in vivo, we did not intend to conclude that this is the most influential regulation for endogenous RNAs. It is known that endogenous RNAs undergo very different regulation. The most prominent factors controlling endogenous RNA stability are the density of splice junctions and the length of UTRs (doi.org/10.1186/s13059-022-02811-x; doi.org/10.1186/s12915-021-00949-x). To decipher the sequence regulation, we controlled for these factors in our experiments. Therefore, we acknowledge that several endogenous features, which were excluded by our approach, may serve as predictive features of RNA half-life in vivo.

Author Response

Reviewer #1 (Public Review):

Summary:

The Roco proteins are a family of GTPases characterized by the conserved presence of an ROC-COR tandem domain. How GTP binding alters the structure and activity of Roco proteins remains unclear. In this study, Galicia C et al. took advantage of conformation-specific nanobodies to trap CtRoco, a bacterial Roco, in an active monomeric state and determined its high-resolution structure by cryo-EM. This study, in combination with the previous inactive dimeric CtRoco, revealed the molecular basis of CtRoco activation through GTP-binding and dimer-to-monomer transition.

Strengths:

The reviewer is impressed by the authors' deep understanding of the CtRoco protein. Capturing Roco proteins in a GTP-bound state is a major breakthrough in the mechanistic understanding of the activation mechanism of Roco proteins and shows similarity with the activation mechanism of LRRK2, a key molecule in Parkinson's disease. Furthermore, the methodology the authors used in this manuscript - using conformation-specific nanobodies to trap the active conformation, which is otherwise flexible and resistant to single-particle average - is highly valuable and inspiring.

Weakness:

Though written with good clarity, the paper will benefit from some clarifications.

1) The angular distribution of particles for the 3D reconstructions should be provided (Figure 1 - Sup. 1 & Sup. 2).

The supplementary figures will be adapted to include particle distribution plots.

2) The B-factors for protein and ligand of the model, Map sharpening factor, and molprobity score should be provided (Table 1).

The map used to interpret the model was post-processed by density modification, therefore no sharpening factor was obtained. This information will be included in Table 1, together with B-factors and molprobity scores.

3) A supplemental Figure to Figure 2B, illustrating how a0-helix interacts with COR-A&LRR before and after GTP binding in atomic details, will be helpful for the readers to understand the critical role of a0-helix during CtRoco activation.

A supplemental figure will be prepared to illustrate this in the revised document.

4) For the following statement, "On the other hand, only relatively small changes are observed in the orientation of the Roc a3 helix. This helix, which was previously suggested to be an important element in the activation of LRRK2 (Kalogeropulou et al., 2022), is located at the interface of the Roc and CORB domains and harbors the residues H554 and Y558, orthologous to the LRRK2 PD mutation sites N1337 and R1441, respectively."

It is not surprising the a3-helix of the ROC domain only has small changes when the ROC domain is aligned (Figure 2E). However, in the study by Zhu et al (DOI: 10.1126/science.adi9926), it was shown that a3-helix has a "see-saw" motion when the COR-B domain is aligned. Is this motion conserved in CtRoco from inactive to active state?

We indeed describe the conformational changes from the perspective of the Roc domain. When using the COR-B domain for structural alignment, a rotational movement of Roc (including a “seesaw”-like movement of the α3-helix helix around His554) with respect to COR-B is correspondingly observed. We will include this in the revised document.

5) A supplemental figure showing the positions of and distances between NbRoco1 K91 and Roc K443, K583, and K611 would help the following statement. "Also multiple crosslinks between the Nbs and CtRoco, as well as between both nanobodies were found. ... NbRoco1-K69 also forms crosslinks with two lysines within the Roc domain (K583 and K611), and NbRoco1-K91 is crosslinked to K583".

A provisional figure displaying these crosslinks is already provided below, and we will also consider including this in the revised manuscript. However, in interpreting these crosslinks it should be taken into consideration that the additive length of the DSSO spacer and the lysine side chains leads to a theoretical upper limit of ∼26 Å for the distance between the α carbon atoms of cross-linked lysines (and even a cut-off distance of 35 Å when taking into account protein dynamics).

Author response image 1.

6) It would be informative to show the position of CtRoco-L487 in the NF and GTP-bound state and comment on why this mutation favors GTP hydrolysis.

We will create an additional figure showing the position of L487, and discuss possible mechanisms for the observed effect of a mutation on GTPase activity.

Reviewer #2 (Public Review):

Summary

The manuscript by Galicia et al describes the structure of the bacterial GTPyS-bound CtRoco protein in the presence of nanobodies. The major relevance of this study is in the fact that the CtRoco protein is a homolog of the human LRRK2 protein with mutations that are associated with Parkinson's disease. The structure and activation mechanisms of these proteins are very complex and not well understood. Especially lacking is a structure of the protein in the GTP-bound state. Previously the authors have shown that two conformational nanobodies can be used to bring/stabilize the protein in a monomer-GTPyS-bound state. In this manuscript, the authors use these nanobodies to obtain the GTPyS-bound structure and importantly discuss their results in the context of the mammalian LRRK2 activation mechanism and mutations leading to Parkinson's disease. The work is well performed and clearly described. In general, the conclusions on the structure are reasonable and well-discussed in the context of the LRRK2 activation mechanism.

Strengths:

The strong points are the innovative use of nanobodies to stabilize the otherwise flexible protein and the new GTPyS-bound structure that helps enormously in understanding the activation cycle of these proteins.

Weakness:

The strong point of the use of nanobodies is also a potential weak point; these nanobodies may have induced some conformational changes in a part of the protein that will not be present in a GTPyS-bound protein in the absence of nanobodies.

Two major points need further attention.

1) Several parts of the protein are very flexible during the monomer-dimer activity cycle. This flexibility is crucial for protein function, but obviously hampers structure resolution. Forced experiments to reduce flexibility may allow better structure resolution, but at the same time may impede the activation cycle. Therefore, careful experiments and interpretation are very critical for this type of work. This especially relates to the influence of the nanobodies on the structure that may not occur during the "normal" monomer-dimer activation cycle in the absence of the nanobodies (see also point 2). So what is the evidence that the nanobody-bound GTPyS-bound state is biochemically a reliable representative of the "normal" GTP-bound state in the absence of nanobodies, and therefore the obtained structure can be confidentially used to interpret the activation mechanism as done in the manuscript.

See below for an answer to remark 1 and 2.

2) The obtained structure with two nanobodies reveals that the nanobodies NbRoco1 and NbRoco2 bind to parts of the protein by which a dimer is impossible, respectively to a0-helix of the linker between Roc-COR and LRR, and to the cavity of the LRR that in the dimer binds to the dimerizing domain CORB. It is likely the open monomer GTP-bound structure is recognized by the nanobodies in the camelid, suggesting that overall the open monomer structure is a true GTP-bound state. However, it is also likely that the binding energy of the nanobody is used to stabilize the monomer structure. It is not automatically obvious that in the details the obtained nonobody-Roco-GTPyS structure will be identical to the "normal" Roco-GTPyS structure. What is the influence of nanobody-binding on the conformation of the domains where they bind; the binding energy may be used to stabilize a conformation that is not present in the absence of the nanobody. For instance, NbRoco1 binds to the a0 helix of the linker; what is here the "normal" active state of the Roco protein, and is e.g. the angle between RocCOR and LRR also rotated by 135 degrees? Furthermore, nanobody NbRoco2 in the LRR domain is expected to stabilize the LRR domain; it may allow a position of the LRR domain relative to the rest of the protein that is not present without nanobody in the LRR domain. I am convinced that the observed open structure is a correct representation of the active state, but many important details have to be supported by e,g, their CX-MS experiments, and in the end probably need confirmation by more structures of other active Roco proteins or confirmation by a more dynamic sampling of the active states by e.g. molecular dynamics or NMR.

Recently, nanobodies have increasingly been used successfully to obtain structural insights in protein conformational states (reviewed in Uchański et al, Curr. Opin. Struc. Biol. 2020). As reviewer # 2 points out, the concern is sometimes raised that antibodies could distort a protein into non-native conformations. Here, it is important to note that the nanobodies were raised by immunizing a llama with the fully native CtRoco protein bound to a non-hydrolysable GTP analogue, after which the nanobodies were selected by phage display using the same fully native and functional form of the protein. As clearly explained in Manglik et al. Annu Rev Pharmacol Toxicol. 2017, the probability of an in vivo matured nanobody inducing a non-native conformation of the antigen is low, although it is possible that it selects a high-energy, low-population conformation of a dynamic protein. Immature B cells require engagement of displayed antibodies with antigen to proliferate and differentiate during clonal selection. Antibodies that induce non-native conformations of the antigen pay a substantial energetic penalty in this process, and B cell clones displaying such antibodies will have a significantly lower probability of proliferation and differentiation into mature antibody-secreting B lymphocytes. Hence, many recent experiments and observation give credence to the notion that nanobodies bind antigens primarily by conformational selection and not induced fit (e.g. Smirnova et al. PNAS 2015).

Extrapolated to the case of CtRoco, which is clearly very flexible in its GTP-bound form, this means that the nanobodies are able to trap and stabilize one conformational state that is representative of the “active state” ensemble of the protein. In this respect, it is clear from our experiments (XL-MS, affinity and effect on GTPase activity) that the effects of NbRoco1 and NbRoco2 are additive (or even cooperative), meaning that both nanobodies recognize different features of the same CtRoco “active state”. Correspondingly, the monomeric, elongated “open” conformation is also observed in the structure of CtRoco bound to NbRoco1 only (Figure1 - supplement 2), albeit that this structure still displays more flexibility. The monomerization and conformational changes that we observe and describe in the current paper at high resolution are also in very good agreement with earlier observations for CtRoco in the GTP-bound form in absence of any nanobodies, including negative stain EM (Deyaert et al. Nature Commun, 2017), hydrogen-deuterium exchange experiments (Deyaert et al. Biochem. J. 2019) and native MS (Leemans et al. Biochem J. 2020).

In the revised document we will include some additional text to address and clarify these aspects.

Author response:

eLife Assessment

This study provides valuable insights into the behavioral, computational, and neural mechanisms of regime shift detection, by identifying distinct roles for the frontoparietal network and ventromedial prefrontal cortex in sensitivity to signal diagnosticity and transition probabilities, respectively. The findings are supported by solid evidence, including an innovative task design, robust behavioral modeling, and well-executed model-based fMRI analyses, though claims of neural selectivity would benefit from more rigorous statistical comparisons. Overall, this work advances our understanding of how humans adapt belief updating in dynamic environments and offers a framework for exploring biases in decision-making under uncertainty.

Thank you for reviewing our manuscript. We appreciate the editors’ assessment and the reviewers’ constructive comments. Below we address the reviewers’ comments. In particular, we addressed Reviewer 1’s comments on (1) neural selectivity by performing statistical comparisons and (2) parameter estimation by providing more details on how the system-neglect model was parameterized. We addressed Reviewer 2’s comments on (1) our neuroimaging results regarding frontoparietal network and (2) model comparisons.  

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study examines human biases in a regime-change task, in which participants have to report the probability of a regime change in the face of noisy data. The behavioral results indicate that humans display systematic biases, in particular, overreaction in stable but noisy environments and underreaction in volatile settings with more certain signals. fMRI results suggest that a frontoparietal brain network is selectively involved in representing subjective sensitivity to noise, while the vmPFC selectively represents sensitivity to the rate of change.

Strengths:

(1) The study relies on a task that measures regime-change detection primarily based on descriptive information about the noisiness and rate of change. This distinguishes the study from prior work using reversal-learning or change-point tasks in which participants are required to learn these parameters from experiences. The authors discuss these differences comprehensively.

Thank you for recognizing our contribution to the regime-change detection literature and our effort in discussing our findings in relation to the experience-based paradigms.

(2) The study uses a simple Bayes-optimal model combined with model fitting, which seems to describe the data well.

Thank you for recognizing the contribution of our Bayesian framework and system-neglect model.

(3) The authors apply model-based fMRI analyses that provide a close link to behavioral results, offering an elegant way to examine individual biases.

Thank you for recognizing our execution of model-based fMRI analyses and effort in using those analyses to link with behavioral biases.

Weaknesses:

My major concern is about the correlational analysis in the section "Under- and overreactions are associated with selectivity and sensitivity of neural responses to system parameters", shown in Figures 5c and d (and similarly in Figure 6). The authors argue that a frontoparietal network selectively represents sensitivity to signal diagnosticity, while the vmPFC selectively represents transition probabilities. This claim is based on separate correlational analyses for red and blue across different brain areas. The authors interpret the finding of a significant correlation in one case (blue) and an insignificant correlation (red) as evidence of a difference in correlations (between blue and red) but don't test this directly. This has been referred to as the "interaction fallacy" (Niewenhuis et al., 2011; Makin & Orban de Xivry 2019). Not directly testing the difference in correlations (but only the differences to zero for each case) can lead to wrong conclusions. For example, in Figure 5c, the correlation for red is r = 0.32 (not significantly different from zero) and r = 0.48 (different from zero). However, the difference between the two is 0.1, and it is likely that this difference itself is not significant. From a statistical perspective, this corresponds to an interaction effect that has to be tested directly. It is my understanding that analyses in Figure 6 follow the same approach.

Relevant literature on this point is:

Nieuwenhuis, S, Forstmann, B & Wagenmakers, EJ (2011). Erroneous analyses of interactions in neuroscience: a problem of significance. Nat Neurosci 14, 1105-1107. https://doi.org/10.1038/nn.2886

Makin TR, Orban de Xivry, JJ (2019). Science Forum: Ten common statistical mistakes to watch out for when writing or reviewing a manuscript. eLife 8:e48175. https://doi.org/10.7554/eLife.48175

There is also a blog post on simulation-based comparisons, which the authors could check out: https://garstats.wordpress.com/2017/03/01/comp2dcorr/

I recommend that the authors carefully consider what approach works best for their purposes. It is sometimes recommended to directly compare correlations based on Monte-Carlo simulations (cf Makin & Orban). It might also be appropriate to run a regression with the dependent variable brain activity (Y) and predictors brain area (X) and the model-based term of interest (Z). In this case, they could include an interaction term in the model:

Y = \beta_0 + \beta_1 \cdot X + \beta_2 \cdot Z + \beta_3 \cdot X \cdot Z

The interaction term reflects if the relationship between the model term Z and brain activity Y is conditional on the brain area of interest X.

Thank you for this great suggestion. We tested the difference in correlation both parametrically and nonparametrically. Their results were identical. In our parametric test, we used the Fisher z transformation to transform the difference in correlation coefficients to the z statistic (Fisher, 1921). That is, for two correlation coefficients, r_blue (the correlation between behavioral slope, and neural slope estimated at change-consistent signals; sample size n_blue) and  r_red, (the correlation between behavioral slope, and neural slope estimated at change-consistent signals; sample size n_red), the z statistic of the difference in correlation is given by

We found that among the five ROIs in the frontoparietal network, two of them, namely the left IFG and left IPS, the difference in correlation was significant (one-tailed z test; left IFG: z=1.8355, p=0.0332; left IPS: z=2.3782, p=0.0087). For the remaining three ROIs, the difference in correlation was not significant (dmPFC: z=0.7594, p=0.2238 ; right IFG: z=0.9068, p=0.1822; right IPS: z=1.3764, p=0.0843). We chose one-tailed test because we already know the correlation under the blue signals was significantly greater than 0. Hence the alternative hypothesis is that r_blue–r_red>0.

In our nonparametric test, we performed nonparametric bootstrapping to test for the difference in correlation. That is, we resampled with replacement the dataset (subject-wise) and used the resampled dataset to compute the difference in correlation. We then repeated the above for 100,000 times so as to obtain the distribution of the correlation difference. We then tested for significance and estimated p-value based on this distribution. Consistent with our parametric tests, here we also found that the difference in correlation was significant in left IFG and left IPS (left IFG: r_blue–r_red=0.46, p=0.0496; left IPS: r_blue–r_red=0.5306, p=0.0041), but was not significant in dmPFC, right IFG, and right IPS (dmPFC: r_blue–r_red=0.1634, p=0.1919; right IFG: r_blue–r_red=0.2123, p=0.1681; right IPS: r_blue–r_red=0.3434, p=0.0631).

We will update these results in the revised manuscript. In summary, we found that the left IFG and left IPS in the frontoparietal network differentially responded to signals consistent with change (blue signals) compared with signals inconsistent with change (red signals). First, the neural sensitivity to signal diagnosticity measured when signals consistent with change appeared (blue signals) significantly correlated with individual subjects’ behavioral sensitivity to signal diagnosticity (r_blue). By contrast, neural sensitivity to signal diagnosticity measured when signals inconsistent with change appeared did not significantly correlate with behavioral sensitivity (r_red). Second, the difference in correlation, r_blue–r_red, was statistically significant between correlation obtained at signals consistent with change and correlation obtained at signals inconsistent with change.

Another potential concern is that some important details about the parameter estimation for the system-neglect model are missing. In the respective section in the methods, the authors mention a nonlinear regression using Matlab's "fitnlm" function, but it remains unclear how the model was parameterized exactly. In particular, what are the properties of this nonlinear function, and what are the assumptions about the subject's motor noise? I could imagine that by using the inbuild function, the assumption was that residuals are Gaussian and homoscedastic, but it is possible that the assumption of homoscedasticity is violated, and residuals are systematically larger around p=0.5 compared to p=0 and p=1. Relatedly, in the parameter recovery analyses, the authors assume different levels of motor noise. Are these values representative of empirical values?

We thank the reviewer for this excellent point. The reviewer touched on model parameterization, assumption of noise, and parameter recovery analysis, which we answered below.

On our model was parameterized

We parameterized the model according to the system-neglect model in Eq. (2) and estimated the alpha parameter separately for each level of transition probability and the beta parameter separately for each level of signal diagnosticity. As a result, we had a total of 6 parameters (3 alpha and 3 beta parameters) in the model. The system-neglect model is then called by fitnlm so that these parameters can be estimated. The term ‘nonlinear’ regression in fitnlm refers to the fact that you can specify any model (in our case the system-neglect model) and estimate its parameters when calling this function. In our use of fitnlm, we assume that the noise is Gaussian and homoscedastic (the default option).

On the assumptions about subject’s motor noise

We wish to emphasize that we did not call the noise ‘motor’ because it can be estimation noise as well. Regardless, in the context of fitnlm, we assume that the noise is Gaussian and homoscedastic.

On the possibility that homoscedasticity is violated

In the revision, we plan to examine this possibility (residuals larger around p=0.5 compared with p=0 and p=1).

On whether the noise levels in parameter recovery analysis are representative of empirical values

To address the reviewer’s question, we conducted a new analysis using maximum likelihood estimation to estimate the noise level of each individual subject. We proceeded in the following steps. First, for each subject separately, we used the parameter estimates of the system-neglect model to compute the period-wise probability estimates of regime shift. As a reminder, we referred to a ‘period’ as the time when a new signal appeared during a trial (for a given transition probability and signal diagnosticity). Each trial consisted of 10 successive periods. Second, we computed the period-wise likelihood, the probability of observing the subject’s actual probability estimate given the probability estimate predicted by the system-neglect model and the noise level. Here we define noise as the standard deviation of a Gaussian distribution centered at the model-predicted probability estimate. We then summed over all periods the negative logarithm of likelihood and used MATLAB’s minimization algorithm (the ‘fmincon’ function) to obtain the noise estimate that minimized the sum of negative log likelihood (thus the noise estimate that maximized the sum of log likelihood). Across subjects, we found that the mean noise estimate was 0.1480 and ranged from 0.0816 to 0.3239. The noise estimate of each subject can be seen in the figure below.

Author response image 1.

Compared with our original parameter recovery analysis where the maximum noise level was set at 0.1, our data indicated that some subjects’ noise was larger than this value. Therefore, we expanded our parameter recovery analysis to include noise levels beyond 0.1 to up to 0.3. We found good parameter recovery across different levels of noise, with the Pearson correlation coefficient between the input parameter values used to simulate data and the estimated parameter values greater 0.95 (Supplementary Fig. S3). The results will be updated in Supplementary Fig. S3.

Author response image 2.

Parameter recovery. We simulated probability estimates according to the system-neglect model. We used each subject’s parameter estimates as our choice of parameter values used in the simulation. Using simulated data, we estimated the parameters (𝛼 and 𝛽) in the system-neglect model. To examine parameter recovery, we plotted the parameter values we used to simulate the data against the parameter estimates we obtained based on simulated data and computed their Pearson correlation. Further, we added different levels of Gaussian white noise with standard deviation 𝜎 = 0.01, 0.05, 0.1,0.2, 0.3 to the simulated data to examine parameter recovery and show the results respectively in Fig. A, B, C, D, and E. For each noise level, we show the parameter estimates in the left two graphs. In the right two graphs, we plot the parameter estimates based on simulated data against the parameter values used to simulate the data. A. Noise 𝜎 = 0.01. B. Noise 𝜎 = 0.05. C. Noise 𝜎 = 0.1. D. Noise 𝜎 = 0.2. E. Noise 𝜎 = 0.3.

We will update the parameter recovery section (p. 44) and Supplementary Figure S3 to incorporate these new results:

“We implemented 5 levels of noise with σ={0.01,0.05,0.1,0.2,0.3} and examined the impact of noise on parameter recovery for each level of noise. These noise levels covered the range of empirical noise levels we estimated from the subjects. To estimate each subject’s noise level, we carried out maximum likelihood estimation in the following steps. First, for each subject separately, we used the parameter estimates of the system-neglect model to compute the period-wise probability estimates of regime shift. As a reminder, we referred to a ‘period’ as the time when a new signal appeared during a trial (for a given transition probability and signal diagnosticity). Each trial consisted of 10 successive periods. Second, we computed the period-wise likelihood, the probability of observing the subject’s actual probability estimate given the probability estimate predicted by the system-neglect model and the noise level. Here we define noise as the standard deviation of a Gaussian distribution centered at the model-predicted probability estimate. We then summed over all periods the negative natural logarithm of likelihood and used MATLAB’s minimization algorithm (the ‘fmincon’ function) to obtain the noise estimate that minimized the sum of negative log likelihood (thus the noise estimate that maximized the sum of log likelihood). Across subjects, we found that the mean noise estimate was 0.1480 and ranged from 0.0816 to 0.3239 (Supplementary Figure S3).”

The main study is based on N=30 subjects, as are the two control studies. Since this work is about individual differences (in particular w.r.t. to neural representations of noise and transition probabilities in the frontoparietal network and the vmPFC), I'm wondering how robust the results are. Is it likely that the results would replicate with a larger number of subjects? Can the two control studies be leveraged to address this concern to some extent?

It would be challenging to use the control studies to address the robustness concern. The control studies were designed to address the motor confounds. They were less suitable, however, for addressing the individual difference issue raised by the reviewer. We discussed why this is the case below.

The two control studies did not allow us to examine individual differences – in particular with respect to neural selectivity of noise and transition probability – and therefore we think it is less likely to leverage the control studies. Having said that, it is possible to look at neural selectivity of noise (signal diagnosticity) in the first control experiment where subjects estimated the probability of blue regime in a task where there was no regime change (transition probability was 0). However, the fact that there were no regime shifts in the first control experiment changed the nature of the task. Instead of always starting at the Red regime in the main experiment, in the first control experiment we randomly picked the regime to draw the signals from. It also changed the meaning and the dynamics of the signals (red and blue) that would appear. In the main experiment the blue signal is a signal consistent with change, but in the control experiment this is no longer the case. In the main experiment, the frequency of blue signals is contingent upon both noise and transition probability where blue signals are less frequent than red signals because of the small transition probabilities. But in the first control experiment, the frequency of blue signals is not less frequent because the regime was blue in half of the trials. Due to these differences, we do not see how analyzing the control experiments could help in establishing robustness because we do not have a good prediction as to whether and how the neural selectivity would be impacted by these differences.

We can address the issue of robustness through looking at the effect size. In particular, with respect to individual differences in neural sensitivity of transition probability and signal diagnosticity, since the significant correlation coefficients between neural and behavioral sensitivity were between 0.4 and 0.58 for signal diagnosticity in frontoparietal network (Fig. 5C), and -0.38 and -0.37 for transition probability in vmPFC (Fig. 5D), the effect size of these correlation coefficients was considered medium to large (Cohen, 1992). Cohen, J. (1992). A power primer. Psychological Bulletin, 112(1), 155-159.

It seems that the authors have not counterbalanced the colors and that subjects always reported the probability of the blue regime. If so, I'm wondering why this was not counterbalanced.

We are aware of the reviewer’s concern. The first reason we did not do these (color counterbalancing and report blue/red regime balancing) was to not confuse the subjects in an already complicated task. Balancing these two variables also comes at the cost of sample size, which was the second reason we did not do it. Although we can elect to do these balancing at the between-subject level to not impact the task complexity, we could have introduced another confound that is the individual differences in how people respond to these variables. This is the third reason we were hesitant to do these counterbalancing.

Reviewer #2 (Public review):

Summary:

This paper focuses on understanding the behavioral and neural basis of regime shift detection, a common yet hard problem that people encounter in an uncertain world. Using a regime-shift task, the authors examined cognitive factors influencing belief updates by manipulating signal diagnosticity and environmental volatility. Behaviorally, they have found that people demonstrate both over and under-reaction to changes given different combinations of task parameters, which can be explained by a unified system-neglect account. Neurally, the authors have found that the vmPFC-striatum network represents current belief as well as belief revision unique to the regime detection task. Meanwhile, the frontoparietal network represents cognitive factors influencing regime detection i.e., the strength of the evidence in support of the regime shift and the intertemporal belief probability. The authors further link behavioral signatures of system neglect with neural signals and have found dissociable patterns, with the frontoparietal network representing sensitivity to signal diagnosticity when the observation is consistent with regime shift and vmPFC representing environmental volatility, respectively. Together, these results shed light on the neural basis of regime shift detection especially the neural correlates of bias in belief update that can be observed behaviorally.

Strengths:

(1) The regime-shift detection task offers a solid ground to examine regime-shift detection without the potential confounding impact of learning and reward. Relatedly, the system-neglect modeling framework provides a unified account for both over or under-reacting to environmental changes, allowing researchers to extract a single parameter reflecting people's sensitivity to changes in decision variables and making it desirable for neuroimaging analysis to locate corresponding neural signals.

Thank you for recognizing our task design and our system-neglect computational framework in understanding change detection.

(2) The analysis for locating brain regions related to belief revision is solid. Within the current task, the authors look for brain regions whose activation covary with both current belief and belief change. Furthermore, the authors have ruled out the possibility of representing mere current belief or motor signal by comparing the current study results with two other studies. This set of analyses is very convincing.

Thank you for recognizing our control studies in ruling out potential motor confounds in our neural findings on belief revision.

(3) The section on using neuroimaging findings (i.e., the frontoparietal network is sensitive to evidence that signals regime shift) to reveal nuances in behavioral data (i.e., belief revision is more sensitive to evidence consistent with change) is very intriguing. I like how the authors structure the flow of the results, offering this as an extra piece of behavioral findings instead of ad-hoc implanting that into the computational modeling.

Thank you for appreciating how we showed that neural insights can lead to new behavioral findings.

Weaknesses:

(1) The authors have presented two sets of neuroimaging results, and it is unclear to me how to reason between these two sets of results, especially for the frontoparietal network. On one hand, the frontoparietal network represents belief revision but not variables influencing belief revision (i.e., signal diagnosticity and environmental volatility). On the other hand, when it comes to understanding individual differences in regime detection, the frontoparietal network is associated with sensitivity to change and consistent evidence strength. I understand that belief revision correlates with sensitivity to signals, but it can probably benefit from formally discussing and connecting these two sets of results in discussion. Relatedly, the whole section on behavioral vs. neural slope results was not sufficiently discussed and connected to the existing literature in the discussion section. For example, the authors could provide more context to reason through the finding that striatum (but not vmPFC) is not sensitive to volatility.<br />

We thank the reviewer for the valuable suggestions.

With regard to the first comment, we wish to clarify that we did not find frontoparietal network to represent belief revision. It was the vmPFC and ventral striatum that we found to represent belief revision ( in Fig. 3). For the frontoparietal network, we identified its involvement in our task through finding that its activity correlated with strength of change evidence (Fig. 4) and individual subjects’ sensitivity to signal diagnosticity (Fig. 5). Conceptually, these two findings reflect how individuals interpret the signals (signals consistent or inconsistent with change) in light of signal diagnosticity. This is because (1) strength of change evidence is defined as signals (+1 for signal consistent with change, and -1 for signal inconsistent with change) multiplied by signal diagnosticity and (2) sensitivity to signal diagnosticity reflects how individuals subjectively evaluate signal diagnosticity. At the theoretical level, these two findings can be interpreted through our computational framework in that both the strength of change evidence and sensitivity to signal diagnosticity contribute to estimating the likelihood of change (Eqs. 1 and 2). We added a paragraph in Discussion to talk about this.

We will add on p. 35:

“For the frontoparietal network, we identified its involvement in our task through finding that its activity correlated with strength of change evidence (Fig. 4) and individual subjects’ sensitivity to signal diagnosticity (Fig. 5). Conceptually, these two findings reflect how individuals interpret the signals (signals consistent or inconsistent with change) in light of signal diagnosticity. This is because (1) strength of change evidence is defined as signals (+1 for signal consistent with change, and -1 for signal inconsistent with change) multiplied by signal diagnosticity and (2) sensitivity to signal diagnosticity reflects how individuals subjectively evaluate signal diagnosticity. At the theoretical level, these two findings can be interpreted through our computational framework in that both the strength of change evidence and sensitivity to signal diagnosticity contribute to estimating the likelihood of change (Eqs. 1 and 2).”

With regard to the second comment, we added discussion on the behavioral and neural slope comparison. We pointed out previous papers conducting similar analysis (Vilares et al., 2012; Ting et al., 2015; Yang & Wu, 2020), their findings and how they relate to our results. Vilares et al. found that sensitivity to prior information (uncertainty in prior distribution) in the orbitofrontal cortex (OFC) and putamen correlated with behavioral measure of sensitivity to prior. In the current study, transition probability acts as prior in the system-neglect framework (Eq. 2) and we found that ventromedial prefrontal cortex represents subjects’ sensitivity to transition probability. Together, these results suggest that OFC and vmPFC are involved in the subjective evaluation of prior information in both static (Vilares et al., 2012) and dynamic environments (current study). In addition, we added to the literature by showing that distinct from vmPFC in representing sensitivity to transition probability or prior, the frontoparietal network represents how sensitive individual decision makers are to the diagnosticity of signals in revealing the true state (regime) of the environment.

We will add on p. 36:

“In the current study, our psychometric-neurometric analysis focused on comparing behavioral sensitivity with neural sensitivity to the system parameters (transition probability and signal diagnosticity). We measured sensitivity by estimating the slope of behavioral data (behavioral slope) and neural data (neural slope) in response to the system parameters. Previous studies had adopted a similar approach (Vilares et al., 2012; Ting et al., 2015; Yang & Wu, 2020). For example, Vilares et al. (2012) found that sensitivity to prior information (uncertainty in prior distribution) in the orbitofrontal cortex (OFC) and putamen correlated with behavioral measure of sensitivity to the prior. In the current study, transition probability acts as prior in the system-neglect framework (Eq. 2) and we found that ventromedial prefrontal cortex represents subjects’ sensitivity to transition probability. Together, these results suggest that OFC and vmPFC are involved in the subjective evaluation of prior information in both static (Vilares et al., 2011) and dynamic environments (current study). In addition, we added to the literature by showing that distinct from vmPFC in representing sensitivity to transition probability or prior, the frontoparietal network represents how sensitive individual decision makers are to the diagnosticity of signals in revealing the true state (regime) of the environment.” 

(2) More details are needed for behavioral modeling under the system-neglect framework, particularly results on model comparison. I understand that this model has been validated in previous publications, but it is unclear to me whether it provides a superior model fit in the current dataset compared to other models (e.g., a model without \alpha or \beta). Relatedly, I wonder whether the final result section can be incorporated into modeling as well - i.e., the authors could test a variant of the model with two \betas depending on whether the observation is consistent with a regime shift and conduct model comparison.

Thank you for the great suggestion.

To address the reviewer’s question on model comparison, we tested 4 variants of the system-neglect model and incorporated them into the final result section. The original system-neglect model and its four models are:

– Original system-neglect model: 6 total parameters, 3 beta parameters (one for each level of signal diagnosticity) and 3 alpha parameters (one for each level of transition probability).  

– M1: System-neglect model with signal-dependent beta parameters (alpha parameters, and beta parameters separately estimated at change-consistent and change-inconsistent signals): 9 total parameters, 3 beta parameters for change-consistent signals, 3 beta parameters for change-inconsistent signals, and 3 alpha parameters.

– M2: System-neglect model with signal-dependent alpha parameters (alpha parameters separately estimated at change-consistent and change-inconsistent signals, and beta parameters): 9 total parameters, 3 alpha parameters for change-consistent signals, 3 alpha parameters for change-inconsistent signals, and 3 beta parameters.

– M3: System-neglect model without alpha parameters (only the beta parameters): 3 total parameters, all are beta parameters (one for each level of signal diagnosticity).

– M4: System-neglect model without beta parameters (only the alpha parameters): 3 total parameters, all are alpha parameters (one for each level of transition probability).

We compared these four models with the original system-neglect model. In the figure below, we plot  where  is the Akaike Information Criterion (AIC) of one of the new models minus the AIC of the original model. ∆AIC<0  indicates that the new model is better than the original model. By contrast, ∆AIC>0 suggests that the new model is worse than the original model.

Author response image 3.

When we separately estimated the beta parameter (M1) for change-consistent signals and change-inconsistent signals, we found that its AIC is significantly smaller than the original model (p<0.01). The same was found for the model where we separately estimated the alpha parameters for change-consistent and change-inconsistent signals (M2). When we took out either the alpha (M3) or the beta parameters (M4), we found that these models were worse than the original model (p<0.01). In summary, we found that models where we separately estimated the alpha/beta parameters for change-consistent and change-inconsistent signals were better than the original model. This is consistent with the insight the neural data provided.

To show these results, we will add a new figure (Figure 7) in the revised manuscript.

Author response:

We are grateful for the thorough and constructive feedback provided on our manuscript.

Regarding the main concern about power law behavior and scale invariance, we would like to clarify that our study does not aim to establish criticality. Instead, we focus on describing and understanding a specific scale-invariant property: the collapsed eigenspectra in neural activity under random sampling. Indeed, we tested Morrell et al.’s latent-variable model (eLife 12, RP89337, 2024, [1]), where a slowly varying latent factor drives population activity. Although it produces a seemingly power-law-like spectrum, random sampling does not replicate the strict spectral collapse observed in our data (second row in Author response image 1). This highlights that simply adding latent factors does not fully recapitulate the scale invariance we measure, suggesting richer or more intricate processes may be involved in real neural recordings.

Author response image 1.

Morrell et al.’s latent variable model [1, 2]. A-D: Functional sampled (RSap) eigenspectral of the Morrell et al. model. E-H: Random sampled (RSap) eigenspectra of the same model. Briefly, in Morrell et al.’s latent variable model [1, 2], neural activity is driven by Nf latent fields and a place fields. The latent fields are modeled as Ornstein-Uhlenbeck processes with a time constant τ . The parameters ϵ and η control the mean and variance of individual neurons’ firing rates, respectively. The following are the parameter values used. A,E: Using the same parameters as in [1]: N_f = 10, ϵ = −2.67, η = 6, τ = 0.1. Half of the cells are also coupled to the place field. B,C,D,F,G,H: Using parameters from [2]: N_f = 5, ϵ = −3, η = 4. There is no place field. The time constant τ = 0.1, 1, 10 for B,F, C,G, and D,H, respectively.

We decided to make 5 key revisions.

• As mentioned, we have evaluated the latent variable model proposed by Morrell et al. and found that they fail to reproduce the scale-invariant eigenspectra observed in our data; these results will be presented in the Discussion section and supported by a new Supplementary Figure.

• We will include a discussion on the findings of Manley et al. (2024, [2]) regarding the issue of saturating dimensionality in the Discussion section, highlighting the methodological differences and their implications.

• We will add a new mathematical derivation in the Methods section, elucidating the bounded dimensionality using the spectral properties of our model.

• We will elaborate in the Discussion section to further emphasize the robustness of our findings by demonstrating their consistency across diverse datasets and experimental techniques.

• We will incorporate a brief discussion on the implications for neural coding. In particular, Fisher information can become unbounded when the slope of the power-law rank plot is less than one, as highlighted in the recent work by Moosavi et al. (bioRxiv 2024.08.23.608710, Aug, 2024 [3]) in the Discussion section.

We believe these revisions will address the concerns raised by you and collectively strengthen our manuscript to provide a more comprehensive and robust understanding of the geometry and dimensionality of brain-wide activity.

References

(1) M. C. Morrell, A. J. Sederberg, I. Nemenman, Latent dynamical variables produce signatures of spatiotemporal criticality in large biological systems. Physical Review Letters 126, 118302 (2021).

(2) M. C. Morrell, I. Nemenman, A. Sederberg, Neural criticality from effective latent variables. eLife 12, RP89337 (2024).

Author rsponse:

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this paper, the authors have performed an antigenic assay for human seasonal N1 neuraminidase using antigens and mouse sera from 2009-2020 (with one avian N1 antigen). This shows two distinct antigen groups. There is poorer reactivity with sera from 2009-2012 against antigens from 2015-2019, and poorer reactivity with sera from 2015-2020 against antigens from 2009-2013. There is a long branch separating these two groups. However, 321 and 423 are the only two positions that are consistently different between the two groups. Therefore these are the most likely cause of these antigenic differences.

Strengths:

(1) A sensible rationale was given for the choice of sera, in terms of the genetic diversity.

(2) There were two independent batches of one of the antigens used for generating sera, which demonstrated the level of heterogeneity in the experimental process.

(3) Replicate of the Wisconsin/588/2019 antigen (as H1 and H6) is another useful measure of heterogeneity.

(4) The presentation of the data, e.g. Figure 2, clearly shows two main antigenic groups.

(5) The most modern sera are more recent than other related papers, which demonstrates that has been no major antigenic change.

Weaknesses:

(1) Issues with experimental methods

As I am not an experimentalist, I cannot comment fully on the experimental methods. However, I note that BALB/c mice sera were used, whereas outbred ferret sera are typically used in influenza antigenic characterisation, so the antigenic difference observed may not be relevant in humans. Similarly, the mice were immunised with an artificial NA immunogen where the typical approach would be to infect the ferret with live virus intra-nasally.

Indeed, ferrets are the gold standard model for the study of influenza. The main reason for this is the susceptibility of ferrets to infection with primary human influenza virus isolates and their ability to transmit human influenza A and B viruses. Although mouse models often require the use of mouse-adapted influenza virus strains, it is still the most used model to study new developments on influenza vaccine.

In our previous publication we performed a parallel analysis of sera of ferrets that were primed by infection and boosted by recombinant protein, as well as mice that, like in this study that focuses on N1 NA, were prime-boosted with purified recombinant NA proteins in the presence of an adjuvant. Our data indicate that the NAI responses in immune sera from infected ferrets after infection and after boost enables similar antigenic classification and correlated strongly with those induced in mice that had been prime-boosted with adjuvanted recombinant NA (Catani et al., eLife 2024). To a large extend, the immunogenicity of an antigen relies on epitope accessibility, which may dictate a universal rule of immunogenicity and antigenicity (Altman et al., 2015).

(2) Five mice sera were generated per immunogen and then pooled, but data was not presented that demonstrated these sera were sufficiently homogenous that this approach is valid.

Although individual sera was not tested here. Based on previous studies from our group we are confident that a prime-boost schedule with 1 µg of adjuvanted soluble tetrameric NA, induces a highly homogeneous response in mice (Catani et al., 2022).

(3) There were no homologous antigens for most of the sera. This makes the responses difficult to interpret as the homologous titre is often used to assess the overall reactivity of a serum. The sequence of the antigens used is not described, which again makes it difficult to interpret the results.

The absence of homologous antigens may indeed make interpretation more difficult. However, we have observed that homologous sera do not always coincide with the highest reactivity, although highest reactivity is always found within an antigenic cluster. A sequence comparison would be appropriate to improve interpretability of the data. Therefore, a sequence alignment and a pairwise comparison will be provided in the revised manuscript as supplement. 

(4) To be able to untangle the effects of the individual substitutions at 321, 386, and 432, it would have been useful to have included the naturally occurring variants at these positions, or to have generated mutants at these positions. Gao et al clearly show an antigenic difference with ferret sera correlated separately with N386K and I321V/K432E.

The prevalence of single amino acid substitutions in N1 NA of clinical H1N1 virus strains isolated between 2009 and 2024 is minimal, which may indicate reduced fitness (see Author response image 1) in strains with these substitutions in NA. Nevertheless, we agree that the rescue of single mutants would provide important evidence to untangle those individual impacts on antigenicity. We plan to generate mutants with substitution at these positions in NA of A/Wisconsin/588/2019 H1N1 and determine the NAI against our panel of sera.

Author response image 1.

Prevalence of the indicated N1 NA substitutions in all clinical human H1N1 isolates with unique sequences deposited in the GISAID data bank since 2009.

(5) The challenge experiments in Gao et al showed that NI titre was not a good correlate of protection, so that limits the interpretation of these results.

On the contrary, challenges experiments confirmed that drift occurred in NA from H1N1 viruses isolated between 2009 (CA/09) and 2015 (MI/15). The dilution of transferred sera to equal inhibitory titers indicate that the homologous ferret sera (shown in figure 5e-f)(Gao et al., 2019) is still effective in protecting against infection while heterologous sera are not. This result emphasises that the nature of the homologous NAI response is well-suited for protection against a homologous challenge, although mechanistic data was not provided.

Issues with the computational methods

(6) The NAI titres were normalised using the ELISA results, and the motivation for this is not explained. It would be nice to see the raw values.

Mice were immunized with different batches of recombinant protein. Each of those batches may have distinct intrinsic immunogenicity, as observed in Figure 1d. For that reason, NAI values were normalized using homologous ELISA titers induced by each respective NA antigen. A table with the raw values will be included in the revised manuscript.

(7) It is not clear what value the random forest analysis adds here, given that positions 321 and 432 are the only two that consistently differ between the two groups.

The substitutions at position 321 and 432 are indeed the only 2 consistently differing amino acids among the tested N1s. Although their correlation with antigenic clustering may be obvious after analysis, a random forest analysis would enable to reveal less obvious substitutions that contribute to the antigenic diversity. In the future, we intend to expand this methodology to strains that are not currently included in the panel. A random forest model is a relatively simple and performant method to deal with a new dataset.

(8) As with the previous N2 paper, the metric for antigenic distance (the root mean square of the difference between the titres for two sera) is not one that would be consistent when different sera are included. More usual metrics of distance are Archetti-Horsfall, fold down from homologous, or fold down from maximum.

The antigenic distances calculated prior to our random forest does use fold-difference as metrics as log2(max(EC50) / EC50). After having obtained the fold-difference values, a pairwise dissimilarity matrix was calculated to obtain the average antigenic distance between pairs of sera. A more detailed description of the methodology will be included in the methods session, including the R-code.

(9) Antigenic cartography of these data is fraught. I wonder whether 2 dimensions are required for what seems like a 1-dimensional antigenic difference - certainly, the antigens, excluding the H5N1, are in a line. The map may be skewed by the high reactivity Brisbane/18 antigen. It is not clear if the column bases (normalisation factors for calculating antigenic distance) have been adjusted to account for the lack of homologous antigens. It is typical to present antigenic maps with a 1:1 x:y ratio.

Antigenic cartography will be repeated excluding H5N1 and/or Brisbane/18 antigen. Data will be provided in the final rebuttal letter.

Issues with interpretation

(10) Figure 2 shows the NAI titres split into two groups for the antigens, however, A/Brisbane is an outlier in the second antigenic group with high reactivity.

Indeed, A/Brisbane/02/2018 has overall higher IC50 values. However, it still falls into the same cluster that we called AG2. Highlighting A/Brisbane/02/2018 may lead to the misinterpretation of a non-existent antigenic group. 

(11) Following Gao et al, I think you can claim that it is more likely that the antigenic change is due to K432E than I321V, based on a comparison of the amino acid change.

Indeed, we would expect that substitution of the basic arginine to an acidic glutamate is more likely to impact antigenicity than the isoleucine-to-valine apolar substitution. Testing of mutant reassortants with single mutations may provide the definitive answer for that question.

Appraisal:

Taking into account the limitations of the experimental techniques (which I appreciate are due to resource constraints), this paper meets its aim of measuring the antigenic relationships between 2009-2020 seasonal N1s, showing that there were two main groups. The authors discovered that the difference between the two antigenic groups was likely attributable to positions 321 and 432, as these were the only two positions that were consistently different between the two groups. They came to this finding by using a random forest model, but other simpler methods could have been used.

Impact:

This paper contributes to the growing literature on the potential benefit of NA in the influenza vaccine.

Reviewer #2 (Public review):

Summary:

In this study, Catani et al. have immunized mice with 17 recombinant N1 neuraminidases (NAs) from human isolates circulating between 2009-2020 to investigate antigenic diversity. NA inhibition (NAI) titers revealed two groups that were antigenically and phylogenetically distinct. Machine learning was used to estimate the antigenic distances between the N1 NAs and mutations at residues K432E and I321V were identified as key determinants of N1 NA antigenicity.

Strengths:

Observation of mutations associated with N1 antigenic drift.

Weaknesses:

Validation that K432E and I321V are responsible for antigenic drift was not determined in a background strain with native K432 and I321 or the restitution of antibody binding by reversion to K432 and I321 in strains that evaded sera.

Reassortant A/Wisconsin/588/2019 with E432K, V321I and also K386N single mutations will be rescued and tested against the panel of sera.

Author Response

We would like to thank the Editors and Reviewers for their comprehensive review of the manuscript. We appreciate your feedback, and we will carefully consider all your comments in the revision of the manuscript. Below are our provisional responses to your comments.

eLife assessment

This manuscript reveals important insights into the role of ipsilateral descending pathways in locomotion, especially following unilateral spinal cord injury. The study provides solid evidence that this method improves the injured side's ability to support weight, and as such the findings may lead to new treatments for stroke, spinal cord injuries, or unilateral cerebral injuries. However, the methods and results need to be better detailed, and some of the statistical analysis enhanced.

Thank you for your assessment. We will incorporate various textual enhancements in the final version of the manuscript to address the weaknesses you have pointed out. The specific improvements are outlined below.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This manuscript provides potentially important new information about ipsilateral cortical impact on locomotion. A number of issues need to be addressed.

Strengths:

The primary appeal and contribution of this manuscript are that it provides a range of different measures of ipsilateral cortical impact on locomotion in the setting of impaired contralateral control. While the pathways and mechanisms underlying these various measures are not fully defined and their functional impacts remain uncertain, they comprise a rich body of results that can inform and guide future efforts to understand cortical control of locomotion and to develop more effective rehabilitation protocols.

Weaknesses:

1. The authors state that they used a cortical stimulation location that produced the largest ankle flexion response (lines 102-104). Did other stimulation locations always produce similar, but smaller responses (aside from the two rats that showed ipsilateral neuromodulation)? Was there any site-specific difference in response to stimulation location?

We derived motor maps in each rat, akin to the representation depicted in Fig 6. In each rat, alternative cortical sites did, indeed, produce distal or proximal contralateral leg flexion responses. Distal responses were more likely to be evoked in the rostral portion of the array, similarly to proximal responses early after injury. This distribution in responses across different cortical sites is reported in this study (Fig. 6) and is consistent with our prior work. The Results section will be revised to provide additional clarification and context for the data presented in Figure 6.

1. Figure 2: There does not appear to be a strong relationship between the percentage of spared tissue and the ladder score. For example, the animal with the mild injury (based on its ladder score) in the lower left corner of Figure 2A has less than 50% spared tissue, which is less spared tissue than in any animal other than the two severe injuries with the most tissue loss. Is it possible that the ladder test does not capture the deficits produced by this spinal cord injury? Have the authors looked for a region of the spinal cord that correlates better with the deficits that the ladder test produces? The extent of damage to the region at the base of the dorsal column containing the corticospinal tract would be an appropriate target area to quantify and compare with functional measures.

In Fig. S6 of our 2021 publication "Bonizzato and Martinez, Science Translational Medicine", we investigated the predictive value of tissue sparing in specific sub-regions of the spinal cord for ladder performance. Specifically, we examined the correlation between the accuracy of left leg ladder performance in the acute state and the preservation of the corticospinal tract (CST). Our results indicated that dorsal CST sparing serves as a mild predictor for ladder deficits, confirming the results obtain in this study.

1. Lines 219-221: The authors state that "phase-coherent stimulation reinstated the function of this muscle, leading to increased burst duration (90{plus minus}18% of the deficit, p=0.004, t-test, Fig. 4B) and total activation (56{plus minus}13% of the deficit, p=0.014, t-test, Fig. 3B). This way of expressing the data is unclear. For example, the previous sentence states that after SCI, burst duration decreased by 72%. Does this mean that the burst duration after stimulation was 90% higher than the -72% level seen with SCI alone, i.e., 90% + -72% = +18%? Or does it mean that the stimulation recovered 90% of the portion of the burst duration that had been lost after SCI, i.e., -72% * (100%-90%)= -7%? The data in Figure 4 suggests the latter. It would be clearer to express both these SCI alone and SCI plus stimulation results in the text as a percent of the pre-SCI results, as done in Figure 4.

Your assessment is correct; we intended to report that the stimulation recovered 90% of the portion of the burst duration that had been lost after SCI. This point will be addressed in the revision of the manuscript.

1. Lines 227-229: The authors claim that the phase-dependent stimulation effects in SCI rats are immediate, but they don't say how long it takes for these effects to be expressed. Are these effects evident in the response to the first stimulus train, or does it take seconds or minutes for the effects to be expressed? After the initial expression of these effects, are there any gradual changes in the responses over time, e.g., habituation or potentiation?

The effects are immediately expressed at the very first occurrence of stimulation. We never tested a rat completely naïve to stimuli, as each treadmill session involves prior cortical mapping to identify a suitable active site for involvement in locomotor experiments. Yet, as demonstrated in Supplementary Video 1 accompanying our 2021 publication on contralateral effects of cortical stimulation, "Bonizzato and Martinez, Science Translational Medicine," the impact of phase-dependent cortical stimulation on movement modulation is instantaneous and ceases promptly upon discontinuation of the stimulation. We did not quantify potential gradual changes in responsiveness over time, but we cannot exclude that for long stimulation sessions (e.g., 30 min or more), stimulus amplitude may need to be slightly increased over time to compensate habituation.

1. Awake motor maps (lines 250-277): The analysis of the motor maps appears to be based on measurements of the percentage of channels in which a response can be detected. This analytic approach seems incomplete in that it only assesses the spatial aspect of the cortical drive to the musculature. One channel could have a just-above-threshold response, while another could have a large response; in either case, the two channels would be treated as the same positive result. An additional analysis that takes response intensity into account would add further insight into the data, and might even correlate with the measures of functional recovery. Also, a single stimulation intensity was used; the results may have been different at different stimulus intensities.

We confirm that maps of cortical stimulation responsiveness may vary at different stimulus amplitudes. To establish an objective metric of excitability, we identified 100µA as a reliable stimulation amplitude across rats and used this value to build the ipsilateral motor representation results in Figure 6. This choice allows direct comparison with Figure 6 of our 2021 article, related to contralateral motor representation. The comparison reveals a lack of correlation with functional recovery metrics in the ipsilateral case, in contrast to the successful correlation achieved in the contralateral case.

Regarding the incorporation of stimulation amplitudes into the analysis, as detailed in the Method section (lines 770-771), we systematically tested various stimulation amplitudes to determine the minimal threshold required for eliciting a muscle twitch, identified as the threshold value. This process was conducted for each electrode site. Upon reviewing these data, we considered the possibility of presenting an additional assessment of ipsilateral cortical motor representation based on stimulation thresholds. However, the representation depicted in the figure did not differ significantly from the data presented in Figure 6A. Furthermore, this representation introduced an additional weakness, as it was unclear how to represent the absence of a response in the threshold scale. We chose to arbitrarily designate it as zero on the inverse logarithmic scale, where, for reference, 100 µA is positioned at 0.2 and 50 µA at 0.5.

In conclusion, we believe that the conclusions drawn from this analysis align substantially with those in the text. The addition of the threshold analysis, in our assessment, would not contribute significantly to improving the manuscript.

Author response image 1.

Threshold analysis

Author response image 2.

Original occurrence probability analysis, for comparison.

1. Lines 858-860: The authors state that "All tests were one-sided because all hypotheses were strictly defined in the direction of motor improvement." By using the one-sided test, the authors are using a lower standard for assessing statistical significance that the overwhelming majority of studies in this field use. More importantly, ipsilateral stimulation of particular kinds or particular sites might conceivably impair function, and that is ignored if the analysis is confined to detecting improvement. Thus, a two-sided analysis or comparable method should be used. This appropriate change would not greatly modify the authors' current conclusions about improvements.

Our original hypothesis, drawn from previous studies involving cortical stimulation in rats and cats, as well as other neurostimulation research for movement restoration, posited a favorable impact of neurostimulation on movement. Consistent with this hypothesis, we designed our experiments with a focus on enhancing movement, emphasizing a strict direction of improvement.

It's important to note that a one-sided test is the appropriate match for a one-sided hypothesis, and it is not a lower standard in statistics. Each experiment we conducted was constructed around a strictly one-sided hypothesis: the inclusion of an extensor-inducing stimulus would enhance extension, and the inclusion of a flexion-inducing stimulus would enhance flexion. This rationale guided our choice of the appropriate statistical test.

We acknowledge your concern regarding the potential for ipsilateral stimulation to have negative effects on locomotion, which might not be captured when designing experiments based on one-sided hypotheses. This concern is valid, and we will explicitly mention it in the statistics section. Nonetheless, even if such observations were made, they could serve as the basis for triggering an ad-hoc follow-up study.

Reviewer #2 (Public Review):

Summary:

The authors' long-term goals are to understand the utility of precisely phased cortex stimulation regimes on recovery of function after spinal cord injury (SCI). In prior work, the authors explored the effects of contralesion cortex stimulation. Here, they explore ipsilesion cortex stimulation in which the corticospinal fibers that cross at the pyramidal decussation are spared. The authors explore the effects of such stimulation in intact rats and rats with a hemisection lesion at the thoracic level ipsilateral to the stimulated cortex. The appropriately phased microstimulation enhances contralateral flexion and ipsilateral extension, presumably through lumbar spinal cord crossed-extension interneuron systems. This microstimulation improves weight bearing in the ipsilesion hindlimb soon after injury, before any normal recovery of function would be seen. The contralateral homologous cortex can be lesioned in intact rats without impacting the microstimulation effect on flexion and extension during gait. In two rats ipsilateral flexion responses are noted, but these are not clearly demonstrated to be independent of the contralateral homologous cortex remaining intact.

Strengths:

This paper adds to prior data on cortical microstimulation by the laboratory in interesting ways. First, the strong effects of the spared crossed fibers from the ipsi-lesional cortex in parts of the ipsi-lesion leg's step cycle and weight support function are solidly demonstrated. This raises the interesting possibility that stimulating the contra-lesion cortex as reported previously may execute some of its effects through callosal coordination with the ipsi-lesion cortex tested here. This is not fully discussed by the authors but may represent a significant aspect of these data. The authors demonstrate solidly that ablation of the contra-lesional cortex does not impede the effects reported here. I believe this has not been shown for the contra-lesional cortex microstimulation effects reported earlier, but I may be wrong. Effects and neuroprosthetic control of these effects are explored well in the ipsi-lesion cortex tests here.

In the revised version of the manuscript, we will incorporate various text improvements to address the points you have highlighted below. Additionally, we will integrate the suggested discussion topic on callosal coordination related to contralateral cortical stimulation.

Weaknesses:

Some data is based on very few rats. For example (N=2) for ipsilateral flexion effects of microstimulation. N=3 for homologous cortex ablation, and only ipsi extension is tested it seems. There is no explicit demonstration that the ipsilateral flexion effects in only 2 rats reported can survive the contra-lateral cortex ablation. We agree with this assessment. The ipsilateral flexion representation is here reported as a rare but consistent phenomenon, which we believe to have robustly described with Figure 7 experiments. We will underline in the text that the ablation experiment did not conclude on the unilateral-cortical nature of ipsilateral flexion effects.

Some improvements in clarity and precision of descriptions are needed, as well as fuller definitions of terms and algorithms.

Likely Impacts: This data adds in significant ways to prior work by the authors, and an understanding of how phased stimulation in cortical neuroprosthetics may aid in recovery of function after SCI, especially if a few ambiguities in writing and interpretation are fully resolved.

The manuscript text will be revised in its final version, and we seek to eliminate any ambiguity in writing, data interpretation and algorithms.

Reviewer #3 (Public Review):

Summary:

This article aims to investigate the impact of neuroprosthesis (intracortical microstimulation) implanted unilaterally on the lesion side in the context of locomotor recovery following unilateral thoracic spinal cord injury.

Strength:

The study reveals that stimulating the left motor cortex, on the same side as the lesion, not only activates the expected right (contralateral) muscle activity but also influences unexpected muscle activity on the left (ipsilateral) side. These muscle activities resulted in a substantial enhancement in lift during the swing phase of the contralateral limb and improved trunk-limb support for the ipsilateral limb. They used different experimental and stimulation conditions to show the ipsilateral limb control evoked by the stimulation. This outcome holds significance, shedding light on the engagement of the "contralateral projecting" corticospinal tract in activating not only the contralateral but also the ipsilateral spinal network.

The experimental design and findings align with the investigation of the stimulation effect of contralateral projecting corticospinal tracts. They carefully examined the recovery of ipsilateral limb control with motor maps. They also tested the effective sites of cortical stimulation. The study successfully demonstrates the impact of electrical stimulation on the contralateral projecting neurons on ipsilateral limb control during locomotion, as well as identifying important stimulation spots for such an effect. These results contribute to our understanding of how these neurons influence bilateral spinal circuitry. The study's findings contribute valuable insights to the broader neuroscience and rehabilitation communities.

Thank you for your assessment of this manuscript. The final version of the manuscript will incorporate your suggestions for improving term clarity and will also enhance the discussion on the mechanism of spinal network engagement, as outlined below.

Weakness:

The term "ipsilateral" lacks a clear definition in the title, abstract, introduction, and discussion, potentially causing confusion for the reader. In the next revision of the manuscript, we will provide a clear definition of the term "ipsilateral."

The unexpected ipsilateral (left) muscle activity is most likely due to the left corticospinal neurons recruiting not only the right spinal network but also the left spinal network. This is probably due to the joint efforts of the neuroprosthesis and activation of spinal motor networks which work bilaterally at the spinal level. However, in my opinion, readers can easily link the ipsilateral cortical network to the ipsilateral-projecting corticospinal tract, which is less likely to play a role in ipsilateral limb control in this study since this tract is disrupted by the thoracic spinal injury.

We agree with your assessment. The discussion section paragraph presenting putative mechanisms of cortico-spinal transmission in the effects presented in the results will be enhanced to reflect these suggestions.

Author response:

Reviewer #1:

(1) After Figure 1, a single saturated (palmitic acid; PA) and a single unsaturated (linoleic acid; LA) fatty acid are used for the remaining studies, bringing into question whether effects are in fact the result of a difference in saturation vs. other potential differences.

PA, SA, OA and LA are the most common FA species in humans (Figure 1A in manuscript). Among them, PA predominantly represents saturated FAs while LA is the main unsaturated FAs, respectively. Of note, although both SA and OA were included in our studies, their effects were comparable to those of PA and LA, respectively. Due to space constraints, the data of SA and OA are not presented in the figures.  

(2) While primary macrophages are used in several mechanistic studies, tumor-associated macrophages (TAMs) are not used. Rather, correlative evidence is provided to connect mechanistic studies in macrophage cell lines and primary macrophages to TAMs.

The roe of FABP4 in TAMs has been demonstrated in our previous studies using in vivo animal models1. Therefore, we did not include TAM-specific data in the current study.

(3) CEBPA and FABP4 clearly regulate LA-induced changes in gene expression. However, whether these two key proteins act in parallel or as a pathway is not resolved by presented data.

Multiple lines of evidence in our studies suggest that FABP4 and CEBPA act as a pathway in LA-induced changes: 1) FABP4-negative macrophages exhibit reduced expression of CEBPA in single cell sequencing data; 2) FABP4 KO macrophages exhibited reduced CEBPA expression; 3) LA-induced CEBPA expression in macrophages was compromised when FABP4 was absent.

(4) It is very interesting that FABP4 regulates both lipid droplet formation and lipolysis, yet is unclear if the regulation of lipolysis is direct or if the accumulation of lipid droplets - likely plus some other signal(s) - induces upregulation of lipolysis genes.

Yes, it is likely that tumor cells induce lipolysis signals. Multiple studies have shown that various tumor types stimulate lipolysis to support their growth and progression2-4.  In this process, lipid-loaded macrophages have emerged as a promising therapeutic target in cancer5, 6. Consistent with findings that lipolysis is essential for tumor-promoting M2 alternative macrophage activation7, our data using FABP4 WT and KO macrophages demonstrate that FABP4 plays a critical role in LA-induced lipid accumulation and lipolysis for tumor metastasis. 

(5) In several places increased expression of genes coding for enzymes with known functions in lipid biology is conflated with an increase in the lipid biology process the enzymes mediate. Additional evidence would be needed to show these processes are in fact increased in a manner dependent on increased enzyme expression.

We fully agree with the reviewer that increased gene expression does not necessarily equate to increased activity. The key finding of this study is that FABP4 plays a pivotal role in linoleic acid (LA)-mediated lipid accumulation and lipolysis in macrophages that promote tumor metastasis. Numerous lipid metabolism-related genes, including FABP4, CEBPA, GPATs, DGATs, and HSL, are involved in this process. While it was not feasible to verify the activity of all these genes, we confirmed the functional roles of key genes like FABP4 and CEBPA through various functional assays, such as gene silencing, knockout cell lines, lipid droplet formation, and tumor migration assays. Supported by established lipid metabolism pathways, our data provide compelling evidence that FABP4 functions as a crucial lipid messenger, facilitating unsaturated fatty acid-driven lipid accumulation and lipolysis in tumor-associated macrophages (TAMs), thus promoting breast cancer metastasis.   

Reviewer #2:

Overall, there is solid evidence for the importance of FABP4 expression in TAMs on metastatic breast cancer as well as lipid accumulation by LA in the ER of macrophages. A stronger rationale for the exclusive contribution of unsaturated fatty acids to the utilization of TAMs in breast cancer and a more detailed description and statistical analysis of data will strengthen the findings and resulting claims.

We greatly appreciated the positive comments from Reviewer #2. In our study, we evaluated the effects of both saturated and unsaturated fatty acids (FA) on lipid metabolism in macrophages.  Our results showed that unsaturated FAs exhibited a preference for lipid accumulation in macrophages compared to saturated FAs. Further analysis revealed that unsaturated LA, but not saturated PA, induced FABP4 nuclear translocation and CEBPA activation, driving the TAG synthesis pathway. For in vitro experiments, statistical analyses were performed using a two-tailed, unpaired student t-test, two-way ANOVA followed by Bonferroni’s multiple comparison test, with GraphPad Prism 9. For experiments analyzing associations of FABP4, TAMs and other factors in breast cancer patients, the Kruskal-Wallis test was applied to compare differences across levels of categorical predictor variable. Additionally, multiple linear regression models were used to examine the association between the predictor variables and outcomes, with log transformation and Box Cox transformation applied to meet the normality assumptions of the model. It is worth noting that in some experiments, only significant differences were observed in groups treated with unsaturated fatty acids. Non-significant results from groups treated with saturated fatty acids were not included in the figures.

Reviewer #3

(1) While the authors speculate that UFA-activated FABP4 translocates to the nucleus to activate PPARgamma, which is known to induce C/EBPalpha expression, they do not directly test involvement of PPARgamma in this axis.

Yes, LA induced FABP4 nuclear translocation and activation of PPARgamma in macrophages (see Figure below). Since these findings have been reported in multiple other studies 8, 9, we did not include the data in the current manuscript.

Author response image 1.

LA induced PPARg expression in macrophages. Bone-marrow derived macrophages were treated with 400μM saturated FA (SFA), unsaturated FA (UFA) or BSA control for 6 hours. PPARg expression was measured by qPCR (***p<0.001).

(2) While there is clear in vitro evidence that co-cultured murine macrophages genetically deficient in FABP4 (or their conditioned media) do not enhance breast cancer cell motility and invasion, these macrophages are not bonafide TAM - which may have different biology. Use of actual TAM in these experiments would be more compelling. Perhaps more importantly, there is no in vivo data in tumor bearing mice that macrophage-deficiency of FABP4 affects tumor growth or metastasis.

In our previous studies, we have shown that macrophage-deficiency of FABP4 reduced tumor growth and metastasis in vivo in mouse models1.

(3) Related to this, the authors find FABP4 in the media and propose that macrophage secreted FABP4 is mediating the tumor migration - but don't do antibody neutralizing experiments to directly demonstrate this.

Yes, we have recently published a paper of developing anti-FABP4 antibody for treatment of breast cancer in moue models10.

(4) No data is presented that the mechanisms/biology that are elegantly demonstrated in the murine macrophages also occurs in human macrophages - which would be foundational to translating these findings into human breast cancer.

Thanks for the excellent suggestions. Since this manuscript primarily focuses on mechanistic studies using mouse models, we plan to apply these findings in our future human studies. 

(5) While the data from the human breast cancer specimens is very intriguing, it is difficult to ascertain how accurate IHC is in determining that the CD163+ cells (TAM) are in fact the same cells expressing FABP4 - which is central premise of these studies. Demonstration that IHC has the resolution to do this would be important. Additionally, the in vitro characterization of FABP4 expression in human macrophages would also add strength to these findings.

The expression of FABP4 in CD163+ TAM observed through IHC is consistent with our previous findings, where we confirmed FABP4 expression in CD163+ TAMs using confocal microscopy. Emerging evidence further supports the pro-tumor role of FABP4 expression in human macrophages across various types of obesity-associated cancers11-13. 

References

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Author response:

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This study sought to reveal the potential roles of m6A RNA methylation in gene dosage regulatory mechanisms, particularly in the context of aneuploid genomes in Drosophila. Specifically, this work looked at the relationships between the expression of m6A regulatory factors, RNA methylation status, classical and inverse dosage effects, and dosage compensation. Using RNA sequencing and m6A mapping experiments, an in-depth analysis was performed to reveal changes in m6A status and expression changes across multiple aneuploid Drosophila models. The authors propose that m6A methylation regulates MOF and, in turn, deposition of H4K16Ac, critical regulators of gene dosage in the context of genomic imbalance.

Strengths:

This study seeks to address an interesting question with respect to gene dosage regulation and the possible roles of m6A in that process. Previous work has linked m6A to X-inactivation in humans through the Xist lncRNA, and to the regulation of the Sxl in flies. This study seeks to broaden that understanding beyond these specific contexts to more broadly understand how m6A impacts imbalanced genomes in other contexts.

Weaknesses:

The methods being used particularly for analysis of m6A at both the bulk and transcript-specific level are not sufficiently specific or quantitative to be able to confidently draw the conclusions the authors seek to make. MeRIP m6A mapping experiments can be very valuable, but differential methylation is difficult to assess when changes are small (as they often are, in this study but also m6A studies more broadly). For instance, based on the data presented and the methods described, it is not clear that the statement that "expression levels at m6A sites in aneuploidies are significantly higher than that in wildtype" is supported. MeRIP experiments are not quantitative, and since there are far fewer peaks in aneuploidies, it stands to reason that more antibody binding sites may be available to enrich those fewer peaks to a larger extent. But based on the data as presented (figure 2D) this conclusion was drawn from RPKM in IP samples, which may not fully account for changing transcript abundances in absolute (expression level changes) and relative (proportion of transcripts in input RNA sample) terms.

Methylated RNA immunoprecipitation followed by sequencing (MeRIP-seq) is a commonly used strategy of genome-wide mapping of m6A modification. This method uses anti-m6A antibody to immunoprecipitate RNA fragments, which results in selective enrichment of methylated RNA. Then the RNA fragments were subjected to deep sequencing, and the regions enriched in the immunoprecipitate relative to input samples are identified as m6A peaks using the peak calling algorithm. We identified m6A peaks in different samples by the exomePeak2 program and determined common m6A peaks for each genotype based on the intersection of biological replicates. Figure 2D shows the RPM values of m6A peaks in MeRIP samples for each genotype, indicating that the levels of reads in the m6A peak regions were significantly higher in the aneuploid IP samples than in wildtypes. When the enrichment of IP samples relative to Input samples (RPM.IP/RPM.Input) was taken into account, the statistics for all three aneuploidies were still significantly higher than those of the wildtypes (Mann Whitney U test p-values < 0.001). This analysis is not about changes in the abundance of transcripts, but from the MeRIP perspective, showing that there are relatively more m6A-modified reads mapped to the m6A peaks in aneuploidies than that in wildtypes. In addition, we have added the results of IP/Input in the main text, and revised the description in the manuscript to make it more precise to reduce possible misunderstandings.

The bulk-level m6A measurements as performed here also cannot effectively support these conclusions, as they are measured in total RNA. The focus of the work is mRNA m6A regulators, but m6A levels measured from total RNA samples will not reflect mRNA m6A levels as there are other abundance RNAs that contain m6A (including rRNA). As a result, conclusions about mRNA m6A levels from these measurements are not supported.

According to some published articles, m6A levels of purified mRNA or total RNA can be detected by different methods (such as mass spectrometry, 2D thin-layer chromatography, etc.) in Drosophila cells or tissues [1-3].

Here, we used the EpiQuik m6A RNA Methylation Quantification Kit (Colorimetric) (Epigentek, NY, USA, Cat # P-9005), which is suitable for detecting m6A methylation status directly using total RNA isolated from any species such as mammals, plants, fungi, bacteria, and viruses. This kit has previously been used by researchers to detect the m6A/A ratio in total RNA [4, 5] or purified mRNA [6] from different species.

In order to compare the m6A levels between the total RNA and mRNA, it was shown that the enrichment of mRNA from total RNA using Dynabeads™mRNA Purification Kit (Invitrogen Cat # 61006) did not show any significantly differences comparing with the results of total RNA (Figure 1). That’s the reason why most of the results of m6A levels in the manuscript were detected in total RNA.

Author response image 1.

The m6A levels of total RNA and mRNA

As suggested, we will try to extract and purify mRNA from different genotypes to verify our conclusion based on the m6A levels of total RNA if necessary. In addition, m6A modification in other types of RNA other than mRNA (e.g., lncRNA, rRNA) is not necessarily meaningless. We will also add discussions of this issue in the manuscript.

(1) Lence T, et al. (2016) m6A modulates neuronal functions and sex determination in Drosophila. Nature 540(7632):242-247.

(2) Haussmann IU, et al. (2016) m(6)A potentiates Sxl alternative pre-mRNA splicing for robust Drosophila sex determination. Nature 540(7632):301-304.

(3) Kan L, et al. (2017) The m(6)A pathway facilitates sex determination in Drosophila. Nat Commun 8:15737.

(4) Zhu C, et al. (2023) RNA Methylome Reveals the m(6)A-mediated Regulation of Flavor Metabolites in Tea Leaves under Solar-withering. Genomics Proteomics Bioinformatics 21(4):769-787.

(5) Song H, et al. (2021) METTL3-mediated m(6)A RNA methylation promotes the anti-tumour immunity of natural killer cells. Nat Commun 12(1):5522.

(6) Yin H, et al. (2021) RNA m6A methylation orchestrates cancer growth and metastasis via macrophage reprogramming. Nat Commun 12(1):1394.

Reviewer #2 (Public Review):

Summary:

The authors have tested the effects of partial- or whole-chromosome aneuploidy on the m6A RNA modification in Drosophila. The data reveal that overall m6A levels trend up but that the number of sites found by meRIP-seq trend down, which seems to suggest that aneuploidy causes a subset of sites to become hyper-methylated. Subsequent bioinformatic analysis of other published datasets establish correlations between the activity of the H4K16 acetyltransferase dosage compensation complex (DCC) and the expression of m6A components and m6A abundance, suggesting that DCC and m6A can act in a feedback loop on each other. Overall, this paper uses bioinformatic trends to generate a candidate model of feedback between DCC and m6A. It would be improved by functional studies that validate the effect in vivo.

Strengths:

• Thorough bioinformatic analysis of their data.

• Incorporation of other published datasets that enhance scope and rigor.

• Finds trends that suggest that a chromosome counting mechanism can control m6A, as fits with pub data that the Sxl mRNA is m6A modified in XX females and not XY males.

• Suggests this counting mechanism may be due to the effect of chromatin-dependent effects on the expression of m6A components.

Weaknesses:

• The linkage between H4K16 machinery and m6A is indirect and based on bioinformatic trends with little follow-up to test the mechanistic bases of these trends.

We found a set of ChIP-seq data (GSE109901) of H4K16ac in female and male Drosophila larvae from the public database, and analyzed whether H4K16ac is directly associated with m6A regulator genes. ChIP-seq is a standard method to study transcription factor binding and histone modification by using efficient and specific antibodies for immunoprecipitation. The results showed that there were H4K16ac peaks at the 5' region in gene of m6A reader Ythdc1 in both males and females. In addition, most of the genome sites where the other m6A regulator genes located are acetylated at H4K16 in both sexes, except that Ime4 shows sexual dimorphism and only contains H4K16ac peak in females. These results indicate that the m6A regulator gene itself is acetylated at H4K16, so there is a direct relationship between H4K16ac and m6A regulators. We have added these contents to the text.

Besides the above conclusion from the seq data, we are also going to do some experiments to test the linkage between H4K16 and m6A in the next, such as how about the m6A levels when MOF is over expressed with the increased levels of H4K16Ac, the H4K16 levels when YT521B is knocked down or over expressed and the relative expression levels of important regulatory genes in there.

• The paper lacks sufficient in vivo validation of the effects of DCC alleles on m6A and vice versa. For example, Is the Ythdc1 genomic locus a direct target of the DCC component Msl-2 ? (see Figure 7).

In order to study whether Ythdc1 genomic locus is a direct target of DCC component, we first analyzed a published MSL2 ChIP-seq data of Drosophila (GSE58768). Since MSL2 is only expressed in males under normal conditions, this set of data is from male Drosophila. According to the results, the majority (99.1%) of MSL2 peaks are located on the X chromosome, while the MSL2 peaks on other chromosomes are few. This is consistent with the fact that MSL2 is enriched on the X chromosome in male Drosophila [1, 2]. Ythdc1 gene is located on chromosome 3L, and there is no MSL2 peak near it. Similarly, other m6A regulator genes are not X-linked, and there is no MSL2 peak. Then we analyzed the MOF ChIP-seq data (GSE58768) of male Drosophila. It was found that 61.6% of MOF peaks were located on the X chromosome, which was also expected [3, 4]. Although there are more MOF peaks on autosomes than MSL2 peaks, MOF peaks are absent on m6A regulator genes on autosomes. Therefore, at present, there is no evidence that the gene locus of m6A regulators are the direct targets of DCC component MSL2 and MOF, which may be due to the fact that most MSL2 and MOF are tethered to the X chromosome by MSL complex under physiological conditions. Whether there are other direct or indirect interactions between Ythdc1 and MSL2 is an issue worthy of further study in the future.

(1) Bashaw GJ & Baker BS (1995) The msl-2 dosage compensation gene of Drosophila encodes a putative DNA-binding protein whose expression is sex specifically regulated by Sex-lethal. Development 121(10):3245-3258.

(2) Kelley RL, et al. (1995) Expression of msl-2 causes assembly of dosage compensation regulators on the X chromosomes and female lethality in Drosophila. Cell 81(6):867-877.

(3) Kind J, et al. (2008) Genome-wide analysis reveals MOF as a key regulator of dosage compensation and gene expression in Drosophila. Cell 133(5):813-828.

(4) Conrad T, et al. (2012) The MOF chromobarrel domain controls genome-wide H4K16 acetylation and spreading of the MSL complex. Dev Cell 22(3):610-624.

Quite a bit of technical detail is omitted from the main text, making it difficult for the reader to interpret outcomes.

(1) Please add the tissues to the labels in Figure 1D.

Figure 1D shows the subcellular localization of FISH probe signals in Drosophila embryos. Arrowheads indicate the foci of probe signals. The corresponding tissue types are (1) blastoderm nuclei; (2) yolk plasm and pole cells; (3) brain and midgut; (4) salivary gland and midgut; (5) blastoderm nuclei and yolk cortex; (6) blastoderm nuclei and pole cells; (7) blastoderm nuclei and yolk cortex; (8) germ band. We have added these to the manuscript.

(2) In the main text, please provide detail on the source tissues used for meRIP; was it whole larvae? adult heads? Most published datasets are from S2 cells or adult heads and comparing m6A across tissues and developmental stages could introduce quite a bit of variability, even in wt samples. This issue seems to be what the authors discuss in lines 197-199.

In this article, the material used to perform MeRIP-seq was the whole third instar larvae. Because trisomy 2L and metafemale Drosophila died before developing into adults, it was not possible to use the heads of adults for MeRIP-seq detection of aneuploidy. For other experiments described here, the m6A abundance was measured using whole larvae or adult heads; material used for RT-qPCR analysis was whole larvae, larval brains, or adult heads; Drosophila embryos at different developmental stages were used for fluorescence in situ hybridization (FISH) experiments. We provide a detailed description of the experimental material for each assay in the manuscript.

(3) In the main text, please identify the technique used to measure "total m6A/A" in Fig 2A. I assume it is mass spec.

We used the EpiQuik m6A RNA Methylation Quantification Kit (Colorimetric) (Epigentek, NY, USA, Cat # P-9005) to measure the m6A/A ratio in RNA samples. This kit is commercially available for quantification of m6A RNA methylation, which used colorimetric assay with easy-to-follow steps for convenience and speed, and is suitable for detecting m6A methylation status directly using total RNA isolated from any species such as mammals, plants, fungi, bacteria, and viruses.

(4) Line 190-191: the text describes annotating m6A sites by "nearest gene" which is confusing. The sites are mapped in RNAs, so the authors must unambiguously know the identity of the gene/transcript, right?

When the m6A peaks were annotated using the R package ChIPseeker, it will include two items: "genomic annotation" and "nearest gene annotation". "Genomic annotation" tells us which genomic features the peak is annotated to, such as 5’UTR, 3’UTR, exon, etc. "Nearest gene annotation" indicates which specific gene/transcript the peak is matched to. We modified the description in the main text to make it easier to understand.

Author response:

eLife Assessment

This valuable study presents a theoretical model of how punctuated mutations influence multistep adaptation, supported by empirical evidence from some TCGA cancer cohorts. This solid model is noteworthy for cancer researchers as it points to the case for possible punctuated evolution rather than gradual genomic change. However, the parametrization and systematic evaluation of the theoretical framework in the context of tumor evolution remain incomplete, and alternative explanations for the empirical observations are still plausible.

We thank the editor and the reviewers for their thorough engagement with our work. The reviewers’ comments have drawn our attention to several important points that we have addressed in the updated version. We believe that these modifications have substantially improved our paper.

There were two major themes in the reviewers’ suggestions for improvement. The first was that we should demonstrate more concretely how the results in the theoretical/stylized modelling parts of our paper quantitatively relate to dynamics in cancer.

To this end, we have now included a comprehensive quantification of the effect sizes of our results across large and biologically-relevant parameter ranges. Specifically, following reviewer 1’s suggestion to give more prominence to the branching process, we have added two figures (Fig S3-S4) quantifying the likelihood of multi-step adaptation in a branching process for a large range of mutation rates and birth-death ratios. Formulating our results in terms of birth-death ratios also allowed us to provide better intuition regarding how our results manifest in models with constant population size vs models of growing populations. In particular, the added figure (Fig S3) highlights that the effect size of temporal clustering on the probability of successful 2-step adaptation is very sensitive to the probability that the lineage of the first mutant would go extinct if it did not acquire a second mutation. As a result, the phenomenon we describe is biologically likely to be most effective in those phases during tumor evolution in which tumor growth is constrained. This important pattern had not been described sufficiently clearly in the initial version of our manuscript, and we thank both reviewers for their suggestions to make these improvements.

The second major theme in the reviewers’ suggestions was focused on how we relate our theoretical findings to readouts in genomic data, with both reviewers pointing to potential alternative explanations for the empirical patterns we describe.

We have now extended our empirical analyses following some of the reviewers’ suggestions. Specifically, we have included analyses investigating how the contribution of reactive oxygen species (ROS)-related mutation signatures correlates with our proxies for multi-step adaptation; and we have included robustness checks in which we use Spearman instead of Pearson correlations. Moreover, we have included more discussion on potential confounds and the assumptions going into our empirical analyses as well as the challenges in empirically identifying the phenomena we describe.

Below, we respond in detail to the individual comments made by each reviewer.

Public Reviews:

Reviewer #1 (Public review):

Summary:

Grasper et al. present a combined analysis of the role of temporal mutagenesis in cancer, which includes both theoretical investigation and empirical analysis of point mutations in TCGA cancer patient cohorts. They find that temporally elevated mutation rates contribute to cancer fitness by allowing fast adaptation when the fitness drops (due to previous deleterious mutations). This may be relevant in the case of tumor suppressor genes (TSG), which follow the 2-hit hypothesis (i.e., biallelic 2 mutations are necessary to deactivate TS), and in cases where temporal mutagenesis occurs (e.g., high APOBEC, ROS). They provide evidence that this scenario is likely to occur in patients with some cancer types. This is an interesting and potentially important result that merits the attention of the target audience. Nonetheless, I have some questions (detailed below) regarding the design of the study, the tools and parametrization of the theoretical analysis, and the empirical analysis, which I think, if addressed, would make the paper more solid and the conclusion more substantiated.

Strengths:

Combined theoretical investigation with empirical analysis of cancer patients.

Weaknesses:

Parametrization and systematic investigation of theoretical tools and their relevance to tumor evolution.

We sincerely thank Reviewer 1 for their comments. As communicated in more detail in the point-by-point replies to the “Recommendations for the authors”, we have revised the paper to address these comments in various ways. To summarize, Reviewer 1 asked for (1) more comprehensive analyses of the parameter space, especially in ranges of small fitness effects and low mutation rates; (2) additional clarifications on details of mechanisms described in the manuscript; and (3) suggested further robustness checks to our empirical analyses. We have addressed these points as follows: we have added detailed analyses of dynamics and effect sizes for branching processes (see Sections SI2 and SI3 in the Supplementary Information, as well as Figures S3 and S4). As suggested, these additions provide characterizations of effect sizes in biologically relevant parameter ranges (low mutation rates and smaller fitness effect sizes), and extend our descriptions to processes with dynamically changing population sizes. Moreover, we have added further clarifications at suggested points in the manuscript, e.g. to elaborate on the non-monotonicities in Fig 3. Lastly, we have undertaken robustness checks using Spearman rather than Pearson correlation coefficients to quantify relations between TSG deactivation and APOBEC signature contribution, and have performed analyses investigating dynamics of reactive oxygen species-associated mutagenesis instead of APOBEC.

Reviewer #2 (Public review):

This work presents theoretical results concerning the effect of punctuated mutation on multistep adaptation and empirical evidence for that effect in cancer. The empirical results seem to agree with the theoretical predictions. However, it is not clear how strong the effect should be on theoretical grounds, and there are other plausible explanations for the empirical observations.

Thank you very much for these comments. We have now substantially expanded our investigations of the parameter space as outlined in the response to the “eLife Assessment” above and in the detailed comments below (A(1)-A(3)) to convey more quantitative intuition for the magnitude of the effects we describe for different phases of tumor evolution. We agree that there could be potential additional confounders to our empirical investigations besides the challenges regarding quantification that we already described in our initial version of the manuscript. We have thus included further discussion of these in our manuscript (see replies to B(1)-B(3)), and we have expanded our empirical analyses as outlined in the response to the “eLife Assessment”.

For various reasons, the effect of punctuated mutation may be weaker than suggested by the theoretical and empirical analyses:

(A1) The effect of punctuated mutation is much stronger when the first mutation of a two-step adaptation is deleterious (Figure 2). For double inactivation of a TSG, the first mutation--inactivation of one copy--would be expected to be neutral or slightly advantageous. The simulations depicted in Figure 4, which are supposed to demonstrate the expected effect for TSGs, assume that the first mutation is quite deleterious. This assumption seems inappropriate for TSGs, and perhaps the other synergistic pairs considered, and exaggerates the expected effects.

Thank you for highlighting this discrepancy between Figure 2 and Figure 4. For computational efficiency and for illustration purposes, we had opted for high mutation rates and large fitness effects in Figure 2; however, our results are valid even in the setting of lower mutation rates and fitness effects. To improve the connection to Figure 4, and to address other related comments regarding parameter dependencies, we have now added more detailed quantification of the effects we describe (Figures SF3 and SF4) to the revised manuscript. These additions show that the effects illustrated in Figure 2 retain large effect sizes when going to much lower mutation rates and much smaller fitness effects. Indeed, while under high mutation rates we only see the large relative effects if the first mutation is highly deleterious, these large effects become more universal when going to low mutation rates.

In general, it is correct that the selective disadvantage (or advantage) conveyed by the first mutation affects the likelihood of successful 2-step adaptations. It is also correct that the magnitude of the ‘relative effect’ of temporal clustering on valley-crossing is highest if the lineage with only the first of the two mutations is vanishingly unlikely to produce a second mutant before going extinct. If the first mutation is strongly deleterious, the lineage of such a first mutant is likely to quickly go extinct – and therefore also more likely to do so before producing a second mutant.

However, this likelihood of producing the second mutant is also low if the mutation rate is low. As our added figure (Figure SF3) illustrates, at low mutation rates appropriate for cancer cells, is insensitive to the magnitude of the fitness disadvantage for large parts of the parameter space. Especially in populations of constant size (approximated by a birth/death ratio of 1), the relative effects for first mutations that reduce the birth rate by 0.5 or by 0.05 are indistinguishable (Figure SF3f).

Moreover, the absolute effect (f_k - f₁), as we discuss in the paper (Figures SF2 and SF3) is largest in regions of the parameter space in which the first mutant is not infinitesimally unlikely to produce a second mutant (and f_k  and f₁ would be infinitesimally small), but rather in parameter regions in which this first mutant has a non-negligible chance to produce a second mutant. The absolute effect (f_k - f₁) therefore peaks around fitness-neutral first mutations. While the next comment (below) says that our empirical investigations more closely resemble comparisons of relative effects and not absolute effects, we would expect that the observations in our data come preferentially from multi-step adaptations with large absolute effect since the absolute effect is maximal when both f_k and f₁ are relatively high.

In summary, we believe Figure 2, while having exaggerated parameters for very defendable reasons, is not a misleading illustration of the general phenomenon or of its applicability in biological settings, as effect sizes remain large when moving to biologically realistic parameter ranges. To clarify this issue, we have largely rewritten the relevant paragraphs in the results section and have added two additional figures (Figures SF3 and SF4) as well as a section in the SI with detailed discussion (SI2).

(A2) More generally, parameter values affect the magnitude of the effect. The authors note, for example, that the relative effect decreases with mutation rate. They suggest that the absolute effect, which increases, is more important, but the relative effect seems more relevant and is what is assessed empirically.

Thank you for this comment. As noted in the replies to the above comments, we have now included extensive investigations of how sensitive effect sizes are to different parameter choices. We also apologize for insufficiently clearly communicating how the quantities in Figure 4 relate to the findings of our theoretical models.

The challenge in relating our results to single-timepoint sequencing data is that we only observe the mutations that a tumor has acquired, but we do not directly observe the mutation rate histories that brought about these mutations. As an alternative readout, we therefore consider (through rough proxies: TSGs and APOBEC signatures) the amount of 2-step adaptations per acquired/retained mutation. While we unfortunately cannot control for the average mutation rate in a sample, we motivate using this “TSG-deactivation score” by the hypothesis that for any given mutation rate, we expect a positive relationship between the amount of temporal clustering and the amount of 2-step adaptations per acquired/retained mutation. This hypothesis follows directly from our theoretical model where it formally translates to the statement that for a fixed μ, f_k is increasing in k.

However, while both quantities f_k/f₁ or f_k - f₁ from our theoretical model relate to this hypothesis – both are increasing in k –, neither of them maps directly onto the formulation of our empirical hypothesis.

We have now rewritten the relevant passages of the manuscript to more clearly convey our motivation for constructing our TSG deactivation score in this form (P. 4-6).

(A3) Routes to inactivation of both copies of a TSG that are not accelerated by punctuation will dilute any effects of punctuation. An example is a single somatic mutation followed by loss of heterozygosity. Such mechanisms are not included in the theoretical analysis nor assessed empirically. If, for example, 90% of double inactivations were the result of such mechanisms with a constant mutation rate, a factor of two effect of punctuated mutagenesis would increase the overall rate by only 10%. Consideration of the rate of apparent inactivation of just one TSG copy and of deletion of both copies would shed some light on the importance of this consideration.

This is a very good point, thank you. In our empirical analyses, the main motivation was to investigate whether we would observe patterns that are qualitatively consistent with our theoretical predictions, i.e. whether we would find positive associations between valley-crossing and temporal clustering. Our aim in the empirical analyses was not to provide a quantitative estimate of how strongly temporally clustered mutation processes affect mutation accumulation in human cancers. We hence restricted attention to only one mutation process which is well characterized to be temporally clustered (APOBEC mutagenesis) and to only one category of (epi)genomic changes (SNPs, in which APOBEC signatures are well characterized). Of course, such an analysis ignores that other mutation processes (e.g. LOH, copy number changes, methylation in promoter regions, etc.) may interact with the mechanisms that we consider in deactivating Tumor suppressor genes.

We have now updated the text to include further discussion of this limitation and further elaboration to convey that our empirical analyses are not intended as a complete quantification of the effect of temporal clustering on mutagenesis in-vivo (P. 10,11).

Several factors besides the effects of punctuated mutation might explain or contribute to the empirical observations:

(B1) High APOBEC3 activity can select for inactivation of TSGs (references in Butler and Banday 2023, PMID 36978147). This selective force is another plausible explanation for the empirical observations.

Thank you for making this point. We agree that increased APOBEC3 activity, or any other similar perturbation, can change the fitness effect that any further changes/perturbations to the cell would bring about. Our empirical analyses therefore rely on the assumption that there are no major confounding structural differences in selection pressures between tumors with different levels of APOBEC signature contributions. We have expanded our discussion section to elaborate on this potential limitation (P. 10-11).

While the hypothesis that APOBEC3 activity selects for inactivation of TSGSs has been suggested, there remain other explanations. Either way, the ways in which selective pressures have been suggested to change would not interfere relevantly with the effects we describe. The paper cited in the comment argues that “high APOBEC3 activity may generate a selective pressure favoring” TSG mutations as “APOBEC creates a high [mutation] burden, so cells with impaired DNA damage response (DDR) due to tumor suppressor mutations are more likely to avert apoptosis and continue proliferating”. To motivate this reasoning, in the same passage, the authors cite a high prevalence of TP53 mutations across several cancer types with “high burden of APOBEC3-induced mutations”, but also note that “this trend could arise from higher APOBEC3 expression in p53-mutated tumors since p53 may suppress APOBEC3B transcription via p21 and DREAM proteins”.

Translated to our theoretical framework, this reasoning builds on the idea that APOBEC3 activity increases the selective advantage of mutants with inactivation of both copies of a TSG. In contrast, the mechanism we describe acts by altering the chances of mutants with only one TSG allele inactivated to inactivate the second allele before going extinct. If homozygous inactivation of TSGs generally conveys relatively strong fitness advantages, lineages with homozygous inactivation would already be unlikely to go extinct. Further increasing the fitness advantage of such lineages would thus manifest mostly in a quicker spread of these lineages, rather than in changes in the chance that these lineages survive. In turn, such a change would have limited effect on the “rate” at which such 2-step adaptations occur, but would mostly affect the speed at which they fixate. It would be interesting to investigate these effects empirically by quantifying the speed of proliferation and chance of going extinct for lineages that newly acquired inactivating mutations in TSGs.

Beyond this explicit mention of selection pressures, the cited paper also discusses high occurrences of mutations in TSGs in relation to APOBEC. These enrichments, however, are not uniquely explained by an APOBEC-driven change in selection pressures. Indeed, our analyses would also predict such enrichments.

(B2) Without punctuation, the rate of multistep adaptation is expected to rise more than linearly with mutation rate. Thus, if APOBEC signatures are correlated with a high mutation rate due to the action of APOBEC, this alone could explain the correlation with TSG inactivation.

Thank you for making this point. Indeed, an identifying assumption that we make is that average mutation rates are balanced between samples with a higher vs lower APOBEC signature contribution. We cannot cleanly test this assumption, as we only observe aggregate mutation counts but not mutation rates. However, the fact that we observe an enrichment for APOBEC-associated mutations among the set of TSG-inactivating mutations (see Figure 4F) would be consistent with APOBEC-mutations driving the correlations in Fig 4D, rather than just average mutation rates. We have now added a paragraph to our manuscript to discuss these points (P. 10-11).

(B3) The nature of mutations caused by APOBEC might explain the results. Notably, one of the two APOBEC mutation signatures, SBS13, is particularly likely to produce nonsense mutations. The authors count both nonsense and missense mutations, but nonsense mutations are more likely to inactivate the gene, and hence to be selected.

Thank you for making this point.  We have included it in our discussion of potential confounders/limitations in the revised manuscript (P. 10-11).

Author response:

Reviewer 1:

Summary:

This paper describes molecular dynamics simulations (MDS) of the dynamics of two T-cell receptors (TCRs) bound to the same major histocompatibility complex molecule loaded with the same peptide (pMHC). The two TCRs (A6 and B7) bind to the pMHC with similar affinity and kinetics, but employ different residue contacts. The main purpose of the study is to quantify via MDS the differences in the inter- and intra-molecular motions of these complexes, with a specific focus on what the authors describe as catch-bond behavior between the TCRs and pMHC, which could explain how T-cells can discriminate between different peptides in the presence of weak separating force.

Strengths:

The authors present extensive simulation data that indicates that, in both complexes, the number of high-occupancy interdomain contacts initially increases with applied load, which is generally consistent with the authors’ conclusion that both complexes exhibit catch-bond behavior, although to different extents. In this way, the paper somewhat expands our understanding of peptide discrimination by T-cells.

The reviewer makes thoughtful assessments of our manuscript. While our manuscript is meant to be a “short” contribution, our significant new finding is that even for TCRs targeting the same pMHC, having similar structures, and leading to similar functional outcomes in conventional assays, their response to applied load can be different. This supports out recent experimental work where TCRs targeting the same pMHC differed in their catch bond characteristics, and importantly, in their response to limiting copy numbers of pMHCs on the antigen-presenting cell (Akitsu et al., Sci. Adv., 2024; cited in our manuscript). Our present manuscript provides the physical basis where two similar TCRs respond to applied load differently. In the revised manuscript, we will make this point clearer.

Weaknesses:

While generally well supported by data, the conclusions would nevertheless benefit from a more concise presentation of information in the figures, as well as from suggesting experimentally testable predictions.

Following the reviewers’ suggestions, we will update figures and use Figure Supplements to make the main figures more concise and to simplify the overall presentation.

Regarding testable predictions, one prediction would be that B7 TCR will exhibit weaker catch bond behavior than A6. This is an important prediction because the two TCRs targeting the same pMHC have similar structures and are functionally similar in conventional assays. This prediction can be tested by single-molecule optical tweezers experiments. We also predict the A6 TCR may perform better when the number of pMHC molecules presented are limited, analogous to our recent experiments on different TCRs, Akitsu et al., Sci. Adv. (2024).

Another testable prediction for the conservation of the basic allostery mechanism is to test the Cβ FG-loop deletion mutant located at the hinge region of the β chain, yet its deletion severely impairs the catch bond formation. These predictions will be mentioned and discussed in the updated manuscript.

Reviewer 2:

In this work, Chang-Gonzalez and coworkers follow up on an earlier study on the force-dependence of peptide recognition by a T-cell receptor using all-atom molecular dynamics simulations. In this study, they compare the results of pulling on a TCR-pMHC complex between two different TCRs with the same peptide. A goal of the paper is to determine whether the newly studied B7 TCR has the same load-dependent behavior mechanism shown in the earlier study for A6 TCR. The primary result is that while the unloaded interaction strength is similar, A6 exhibits more force stabilization.

This is a detailed study, and establishing the difference between these two systems with and without applied force may establish them as a good reference setup for others who want to study mechanobiological processes if the data were made available, and could give additional molecular details for T-Cell-specialists. As written, the paper contains an overwhelming amount of details and it is difficult (for me) to ascertain which parts to focus on and which results point to the overall take-away messages they wish to convey.

As mentioned above and as the reviewer correctly pointed out, the condensed appearance of this manuscript arose largely because we intended it to be a Research Advances article as a short follow up study of our previous paper on A6 TCR published in eLife. Most of the analysis scripts for the A6 TCR study are already available on Github. We will additionally deposit sample structures and simulation scripts for the B7 TCR. Trajectory will be provided upon request given their large size.

Regarding the focus issue, it is in part due to the complex nature of the problem, which required simulations under different conditions and multi-faceted analyses. Concisely presenting the complex analyses also has been a challenge in our previous papers on TCR simulations (Hwang et al., PNAS 2020; Chang-Gonzalez et al., eLife, 2024 – both are cited in our manuscript). With updated figures and texts, we expect that the presentation will be a lot clearer. But even in the present form, the reviewer points out the main take-away message well: “The primary result is that while the unloaded interaction strength is similar, A6 exhibits more force stabilization.

Detailed comments:

(1) In Table 1 - are the values of the extension column the deviation from the average length at zero force (that is what I would term extension) or is it the distance between anchor points (which is what I would assume based on the large values. If the latter, I suggest changing the heading, and then also reporting the average extension with an asterisk indicating no extensional restraints were applied for B7-0, or just listing 0 load in the load column. Standard deviation in this value can also be reported. If it is an extension as I would define it, then I think B7-0 should indicate extension = 0+/- something.

The distance between anchor points could also be labeled in Figure 1A.

“Extension” is the distance between anchor points (blue spheres at the ends of the added strands in Fig. 1A). While its meaning should be clear in the section “Laddered extensions” in MD simulation protocol, at first glance it may lead to confusion. In a strict sense, use of “extension” for the distance is a misnomer, but we have used it in our previous two papers (Hwang et al., PNAS 2020; Chang-Gonzalez et al., eLife, 2024), so we prefer to keep it for consistency. Instead, in the caption of Table 1, we will explain its meaning, and also explicitly label it in Fig. 1A, as the reviewer suggested.

Please also note that the no-load case B7⁰ does not have a particular extension that yields zero load on average. It would in fact be very difficult to find such an extension (distance between two anchor points). To simulate the system without load, we separately built a TCR-pMHC complex without added linkers, and held the distal part of pMHC with weak harmonic restraints (explained in sections “Structure preparation” and “Systems without load”). In this way, no external force is applied to TCR as it moves relative to pMHC. We will clarify this when introducing B7⁰ in the Results section.

(2) As in the previous paper, the authors apply ”constant force” by scanning to find a particular bond distance at which a desired force is selected, rather than simply applying a constant force. I find this approach less desirable unless there is experimental evidence suggesting the pMHC and TCR were forced to be a particular distance apart when forces are applied. It is relatively trivial to apply constant forces, so in general, I would suggest this would have been a reasonable comparison. Line 243-245 speculates that there is a difference in catch bonding behavior that could be inferred because lower force occurs at larger extensions, but I do not believe this hypothesis can be fully justified and could be due to other differences in the complex.

There is indeed experimental evidence that the TCR-pMHC complex operates under constant separation. The spacing between a T-cell and an antigen-presenting cell is maintained by adhesion molecules such as the CD2CD58 pair, as explained in our paper on the A6 TCR, (Chang-Gonzalez et al., eLife, 2024; please see the bottom paragraph on page 4 of the paper). In in vitro single-molecule experiments, pulling to a fixed separation and holding is also commonly done. Detailed comparison between constant extension vs. constant force simulations is definitely a subject of our future study. We will clarify these points when explaining about the constant extension (or separation).

Regarding line 243–245, we agree with the reviewer that without further tests, lower forces at larger extensions per se cannot be an indicator that B7 forms a weaker catch bond. But with additional insight, it does have an indirect relevance. In addition to fewer TCR-pMHC contacts (Fig. 1C of our manuscript), the intra-TCR contacts are also reduced compared to those of A6 (Fig. 1D vs. Chang-Gonzalez et al., eLife, 2024, Fig. 8A,B, first column; reproduced in the figure in our response to reviewer 3 below). This shows that the B7 TCR forms a looser complex with pMHC compared to A6. With its higher compliance, the B7 TCR-pMHC complex needs to be under a greater extension than A6 to apply comparable levels of force, and it would be more difficult to achieve load-induced stabilization of the TCR-pMHC interface, hence a weaker catch bond. We will add this point when explaining the weaker catch bond behavior of B7.

(3) On a related note, the authors do not refer to or consider other works using MD to study force-stabilized interactions (e.g. for catch bonding systems), e.g. these cases where constant force is applied and enhanced sampling techniques are used to assess the impact of that applied force: https://www.cell.com/biophysj/fulltext/S0006-3495(23)00341-7, https://www.biorxiv.org/content/10.1101/2024.10.10.617580v1. I was also surprised not to see this paper on catch bonding in pMHC-TCR referred to, which also includes some MD simulations: https://www.nature.com/articles/s41467-023-38267-1

We thank the reviewer for bringing the three papers to our attention, which are:

(1) Languin-Cattoën, Sterpone, and Stirnemann, Biophys. J. 122:2744 (2023): About bacterial adhesion protein FimH.

(2) Peña Ccoa, et al., bioRxiv (2024): About actin binding protein vinculin.

(3) Choi et al., Nat. Comm. 14:2616 (2023): About a mathematical model of the TCR catch bond.

Catch bond mechanisms of FimH and vinculin are different from that of TCR in that FimH and vinculin have relatively well-defined weak- and strong-binding states where there are corresponding crystal structures. Availability of the end-state structures enable using simulation approaches such as enhanced sampling of individual states and studying the transition between the two states. In contrast, TCR does not have any structurally well-defined weakor strong-binding states, which requires a different approach. As demonstrated in our current manuscript as well as in our previous two papers (Hwang et al., PNAS 2020; Chang-Gonzalez et al., eLife, 2024), our microsecond-long simulations of the complex under realistic pN-level loads and a combination of analysis methods are effective for elucidating the catch bond mechanism of TCR. In the revised manuscript, we will cite the two papers, to compare the TCR catch bond mechanism with those of FimH and vinculin, which will offer a broader perspective.

The third paper (Choi, 2023) proposes a mathematical model to analyze extensive sets of data, and also perform new experiments and additional simulations. Of note, their model assumptions are based mainly on the steered MD (SMD) simulation in their previous paper (Wu, et al., Mol. Cell. 73:1015, 2019). In their model, formation of a catch bond (called catch-slip bond in Choi’s paper) requires partial unfolding of MHC and tilting of the TCR-pMHC interface. While further studies are needed to find whether those changes are indeed required, even so, the question remains regarding how the complex in the fully folded state can bear load and enter such a state in the first place. Our current and previous simulation studies suggest a mechanism by which ligand- and load-dependent responses occur as the first obligatory step of catch bond formation, after which partial unfolding and/or extensive conformational transitions may occur, as described in our recent paper (Akitsu et al., Sci. Adv., 2024). In the revised manuscript, we will cite Wu’s paper and briefly explain the above.

(4) The authors should make at least the input files for their system available in a public place (github, zenodo) so that the systems are a more useful reference system as mentioned above. The authors do not have a data availability statement, which I believe is required.

As mentioned above, we will make sample input files and coordinates available on Github. Data availability statement will be added.

Reviewer 3:

Summary:

The paper by Chang-Gonzalez et al. is a molecular dynamics (MD) simulation study of the dynamic recognition (load-induced catch bond) by the T cell receptor (TCR) of the complex of peptide antigen (p) and the major histocompatibility complex (pMHC) protein. The methods and simulation protocols are essentially identical to those employed in a previous study by the same group (Chang-Gonzalez et al., eLife 2024). In the current manuscript, the authors compare the binding of the same pMHC to two different TCRs, B7 and A6 which was investigated in the previous paper. While the binding is more stable for both TCRs under load (of about 10-15 pN) than in the absence of load, the main difference is that, with the current MD sampling, B7 shows a smaller amount of stable contacts with the pMHC than A6.

Strengths:

The topic is interesting because of the (potential) relevance of mechanosensing in biological processes including cellular immunology.

Weaknesses:

The study is incomplete because the claims are based on a single 1000-ns simulation at each value of the load and thus some of the results might be marred by insufficient sampling, i.e., statistical error. After the first 600 ns, the higher load of B7high than B7low is due mainly to the simulation segment from about 900 ns to 1000 ns (Figure 1D). Thus, the difference in the average value of the load is within their standard deviation (9 +/- 4 pN for B7low and 14.5 +/- 7.2 for B7high, Table 1). Even more strikingly, Figure 3E shows a lack of convergence in the time series of the distance between the V-module and pMHC, particularly for B70 (left panel, yellow) and B7low (right panel, orange). More and longer simulations are required to obtain a statistically relevant sampling of the relative position and orientation of the V-module and pMHC.

The reviewer uses data points during the last 100 ns to raise an issue with sampling. But since we are using realistic pN range forces, force fluctuates more slowly. In fact, in our simulation of B7^high, while the force peaks near 35 pN at 500 ns (Fig. 1D of our manuscript; reproduced as panels C and D below), the contact heat map shows no noticeable changes around 500 ns (Fig. 2C of our manuscript). Thus, a wider time window must be considered rather than focusing on instantaneous force.

We believe the reviewer’s concern about sampling arose also due to a lack of clear explanation. Author response image 1 below contains panels from our earlier eLife paper on the A6 TCR. Panels A and B are from Fig. 8 of the A6 paper, and panels C and D are from Fig. 1D of our present manuscript. The high-load simulations in both cases (outlined circles) fluctuate widely in force so that one might argue that sampling was insufficient. However, unless one is interested in finding the precise value of force for a given extension, sampling in our simulations was reasonable enough to distinguish between high- and low-force behaviors. To support this, we show panel E below, which is from Appendix 3–Fig. 1 of our A6 paper. Added to this panel are the average forces and standard deviations of B7^low and B7^high from Table 1 of our manuscript (red squares). Please note that all of the data were measured after 500 ns. Except for Y8A^low and dFG^low of A6 (explained below), all of the data points lie on nearly a straight line.

Author response image 1.

Thermodynamically, the force and position of the restraint (blue spheres in Fig. 1A of our manuscript) form a pair of generalized force and the corresponding spatial variable in equilibrium at temperature 300 K, which is akin to the pressure P and volume V of an ideal gas. If V is fixed, P fluctuates. Denoting the average and std of pressure as ⟨P⟩ and ∆P, respectively, Burgess showed that ∆P/⟨P⟩ is a constant (Eq. 5 of Burgess, Phys. Lett. A, 44:37; 1973). In the case of the TCRαβ-pMHC system, although individual atoms are not ideal gases, since their motion leads to the fluctuation in force on the restraints, the situation is analogous to the case where pressure arises from individual ideal gas molecules hitting the confining wall as the restraint. Thus, the near-linear behavior in panel E above is a consequence of the system being many-bodied and at constant temperature. The linearity is also an indirect indicator that sampling of force was reasonable. The fact that A6 and B7 data show a common linear profile further demonstrates the consistency in our force measurement. That said, the B7 data points (red in panel E) are elevated slightly above nearby A6 data points. This is consistent with B7 forming an overall weaker complex, both at the TCR-pMHC interface (panels A vs. C) and within intra-TCR interfaces (panels B vs. D), which can be seen by the wider ranges of color bars in panels A and B for A6 compared to panels C and D for B7.

About the two outliers of A6, Y8A^low is for an antagonist peptide and dFG^low is the Cβ FG-loop deletion mutant. Interestingly, both cases had reduced numbers of contacts with pMHC, which likely caused a wider conformational motion, hence greater fluctuation in force.

A similar argument applies to Fig. 3E of our manuscript. If precise values of the V-module to pMHC distance were needed, longer or duplicate simulations would be necessary, however, Fig. 3E as it currently stands clearly shows that B7^high maintains more stable interface compared to B7^low, which is consistent with all other measures we used, such as Fig. 3B (Hamming distance), Fig. 3C (buried surface area), and Fig. 4A–E (Vα-Vβ motion and CDR3 distance). They are also consistent with our simulations of A6.

Thus, rather than relying on peculiarities of individual trajectories, we analyze data in multiple ways and draw conclusions based on features that are consistent across different simulations. Please also note that reviewer 1 mentioned that our conclusions are “generally well supported by data.”

We will update our manuscript to concisely explain the above and also will add Panel E above as a supplement of Fig. 1.

It is not clear why ”a 10 A distance restraint between alphaT218 and betaA259 was applied” (section MD simulation protocol, page 9).

αT218 and βA259 are the residues attached to a leucine-zipper handle in in vitro optical trap experiments (Das, et al., PNAS 2015). In T cells, those residues also connect to transmembrane helices. Author response image 2 is a model of N15 TCR used in experiments in Das’ paper, constructed based on PDB 1NFD. Blue spheres represent Cα atoms corresponding to αT218 and βA259 of B7 TCR. Their distance is 6.7 ˚A. The 10-˚A distance restraint in simulation was applied to mimic the presence of the leucine zipper that prevents excessive separation of the added strands. The distance restraint is a flat-bottom harmonic potential which is activated only when the distance between the two atoms exceeds 10 ˚A, which we did not clarify in our original manuscript. The same restraint was used in our previous studies on JM22 and A6 TCRs.

We will add the figure as a supplement of Fig. 1, cite Das’ paper, and also update description of the distance restraint in the MD simulation protocol section.

Author response image 2.

Author response:

Public Reviews:

We thank the reviewers for their overall positive assessments and constructive feedback

Reviewer #1 (Public Review):

Summary:

The study explored the biomechanics of kangaroo hopping across both speed and animal size to try and explain the unique and remarkable energetics of kangaroo locomotion.

Strengths:

The study brings kangaroo locomotion biomechanics into the 21st century. It is a remarkably difficult project to accomplish. There is excellent attention to detail, supported by clear writing and figures.

Weaknesses:

The authors oversell their findings, but the mystery still persists.

The manuscript lacks a big-picture summary with pointers to how one might resolve the big question.

General Comments

This is a very impressive tour de force by an all-star collaborative team of researchers. The study represents a tremendous leap forward (pun intended) in terms of our understanding of kangaroo locomotion. Some might wonder why such an unusual species is of much interest. But, in my opinion, the classic study by Dawson and Taylor in 1973 of kangaroos launched the modern era of running biomechanics/energetics and applies to varying degrees to all animals that use bouncing gaits (running, trotting, galloping and of course hopping). The puzzling metabolic energetics findings of Dawson & Taylor (little if any increase in metabolic power despite increasing forward speed) remain a giant unsolved problem in comparative locomotor biomechanics and energetics. It is our "dark matter problem".

Thank you for the kind words

This study is certainly a hop towards solving the problem. But, the title of the paper overpromises and the authors present little attempt to provide an overview of the remaining big issues.

We will modify the title to reflect this comment.  

The study clearly shows that the ankle and to a lesser extent the mtp joint are where the action is. They clearly show in great detail by how much and by what means the ankle joint tendons experience increased stress at faster forward speeds.

Since these were zoo animals, direct measures were not feasible, but the conclusion that the tendons are storing and returning more elastic energy per hop at faster speeds is solid.

The conclusion that net muscle work per hop changes little from slow to fast forward speeds is also solid.

Doing less muscle work can only be good if one is trying to minimize metabolic energy consumption. However, to achieve greater tendon stresses, there must be greater muscle forces. Unless one is willing to reject the premise of the cost of generating force hypothesis, that is an important issue to confront.

Further, the present data support the Kram & Dawson finding of decreased contact times at faster forward speeds. Kram & Taylor and subsequent applications of (and challenges to) their approach supports the idea that shorter contact times (tc) require recruiting more expensive muscle fibers and hence greater metabolic costs. Therefore, I think that it is incumbent on the present authors to clarify that this study has still not tied up the metabolic energetics across speed problems and placed a bow atop the package.

Fortunately, I am confident that the impressive collective brain power that comprises this author list can craft a paragraph or two that summarizes these ideas and points out how the group is now uniquely and enviably poised to explore the problem more using a dynamic SIMM model that incorporates muscle energetics (perhaps ala' Umberger et al.). Or perhaps they have other ideas about how they can really solve the problem.

You have raised important points, thank you for this feedback. We will add a paragraph discussing the limitations of our study and ensure the revised manuscript makes it clear which mysteries remain. We intend to address muscle forces, contact time, and energetics in future work when we have implemented all hindlimb muscles within the musculoskeletal model.  

I have a few issues with the other half of this study (i.e. animal size effects). I would enjoy reading a new paragraph by these authors in the Discussion that considers the evolutionary origins and implications of such small safety factors. Surely, it would need to be speculative, but that's OK.

We will integrate this into the discussion.

Reviewer #2 (Public Review):

Summary

This is a fascinating topic that has intrigued scientists for decades. I applaud the authors for trying to tackle this enigma. In this manuscript, the authors primarily measured hopping biomechanics data from kangaroos and performed inverse dynamics.

While these biomechanical analyses were thorough and impressively incorporated collected anatomical data and an Opensim model, I'm afraid that they did not satisfactorily address how kangaroos can hop faster and not consume more metabolic energy, unique from other animals.

Noticeably, the authors did not collect metabolic data nor did they model metabolic rates using their modelling framework. Instead, they performed a somewhat traditional inverse dynamics analysis from multiple animals hopping at a self-selected speed.

We aimed to provide a joint-level explanation, but we will address the limitations of not modelling the energy consumers themselves (the skeletal muscles) in the revised manuscript. We plan to expand upon muscle level energetics in the future with a more detailed MSK model.

Within these analyses, the authors largely focused on ankle EMA, discussing its potential importance (because it affects tendon stress, which affects tendon strain energy, which affects muscle mechanics) on the metabolic cost of hopping. However, EMA was roughly estimated (CoP was fixed to the foot, not measured)…

As noted in our methods, EMA was not calculated from a fixed centre of pressure (CoP). We did fix the medial-lateral position, owing to the fact that both feet contacted the force plate together, but the anteroposterior movement of the CoP was recorded by the force plate and thus allowed to move. We report the movement (or lack of movement) in our results. The anterior-posterior axis is the most relevant to lengthening or shortening the distance of the ‘out-lever’ R, and thereby EMA.

It is necessary to assume fixed medial-lateral position because a single force trace and CoP is recorded when two feet land on the force plate. The medial-lateral forces on each foot cancel out so there is no overall medial-lateral movement if the forces are symmetrical (e.g. if the kangaroo is hopping in a straight path and one foot is not in front of the other). We only used symmetrical trials so that the anterior-posterior movement of the CoP would be reliable.

and did not detectibly associate with hopping speed (see results).

Yet, the authors interpret their EMA findings as though it systematically related with speed to explain their theory on how metabolic cost is unique in kangaroos vs. other animals.

Indeed, the relationship between R and speed (and therefore EMA and speed) was not significant. However, the significant change in ankle height with speed, combined with no systematic change in COP at midstance, demonstrates that R would get longer at faster speeds. If we consider the nonsignificant relationship between R and speed to indicate that there is no change in R, then these two results conflict. We could not find a flaw in our methods, so instead concluded that the nonsignificant relationship between R and speed may be due to a small change in R being undetectable in our data. Taking both results into account, we think it is more likely that there is a non-detectable change in R, rather than no change in R with speed, but we presented both results for transparency.

These speed vs. biomechanics relationships were limited by comparisons across different animals hopping at different speeds and could have been strengthened using repeated measures design.

There is significant variation in speed within individuals, not just between individuals. The preferred speed of kangaroos is 2-4.5 m/s, but most individuals show a wide range within this. Eight of our 16 kangaroos had a maximum speed that was between 1-2m/s faster than their slowest trial. Repeated measures of these eight individuals comprises 78 out of the 100 trials.

It would be ideal to collect data across the full range of speeds for all individuals, but it is not feasible in this type of experimental setting. Interference such as chasing is dangerous to kangaroos as they are prone to strong adverse reactions to stress.

There are also multiple inconsistencies between the authors' theory on how mechanics affect energetics and the cited literature, which leaves me somewhat confused and wanting more clarification and information on how mechanics and energetics relate.

We will ensure that this is clearer in the revised manuscript.

My apologies for the less-than-favorable review, I think that this is a neat biomechanics study - but am unsure if it adds much to the literature on the topic of kangaroo hopping energetics in its current form.

Reviewer #3 (Public Review):

Summary:

The goal of this study is to understand how, unlike other mammals, kangaroos are able to increase hopping speed without a concomitant increase in metabolic cost. They use a biomechancial analysis of kangaroo hopping data across a range of speeds to investigate how posture, effective mechanical advantage, and tendon stress vary with speed and mass. The main finding is that a change in posture leads to increasing effective mechanical advantage with speed, which ultimately increases tendon elastic energy storage and returns via greater tendon strain. Thus kangaroos may be able to conserve energy with increasing speed by flexing more, which increases tendon strain.

Strengths:

The approach and effort invested into collecting this valuable dataset of kangaroo locomotion is impressive. The dataset alone is a valuable contribution.

Thank you!

Weaknesses:

Despite these strengths, I have concerns regarding the strength of the results and the overall clarity of the paper and methods used (which likely influences how convincingly the main results come across).

(1) The paper seems to hinge on the finding that EMA decreases with increasing speed and that this contributes significantly to greater tendon strain estimated with increasing speed. It is very difficult to be convinced by this result for a number of reasons:

• It appears that kangaroos hopped at their preferred speed. Thus the variability observed is across individuals not within. Is this large enough of a range (either within or across subjects) to make conclusions about the effect of speed, without results being susceptible to differences between subjects?

Apologies, this was not clear in the manuscript. Kangaroos hopping at their preferred speed means we did not chase or startle them into high speeds to comply with ethics and enclosure limitations. Thus we did not record a wide range of speed within the bounds of what kangaroos are capable of (up to 12 m/s), but for the range we did measure (~2-4.5 m/s), there is variation hopping speed within each individual kangaroo. Out of 16 individuals, eight individuals had a difference of 1-2m/s between their slowest and fastest trials, and these kangaroos accounted for 78 out of 100 trials. Of the remainder, six individuals had three for fewer trials each, and two individual had highly repeatable speeds (3 out of 4, and 6 out of 7 trials were within 0.5 m/s). We will ensure this is clear in the revised manuscript.

In the literature cited, what was the range of speeds measured, and was it within or between subjects?

For other literature, to our knowledge the highest speed measured is ~9.5m/s (see supplementary Fig1b) and there were multiple measures for several individuals (see methods Kram & Dawson 1998).

• Assuming that there is a compelling relationship between EMA and velocity, how reasonable is it to extrapolate to the conclusion that this increases tendon strain and ultimately saves metabolic cost?

They correlate EMA with tendon strain, but this would still not suggest a causal relationship (incidentally the p-value for the correlation is not reported).

We will add supporting literature on the relationship between metabolic cost and tendon stress (or strain), to elaborate on why the correlation between EMA and stress is important.

Tendon strain could be increasing with ground reaction force, independent of EMA.

Even if there is a correlation between strain and EMA, is it not a mathematical necessity in their model that all else being equal, tendon stress will increase as ema decreases? I may be missing something, but nonetheless, it would be helpful for the authors to clarify the strength of the evidence supporting their conclusions.

Yes, GRF also contributes to the increase in tendon stress in the mechanism we propose. We have illustrated this in Fig 6, however we will make this clearer in the revised discussion.

• The statistical approach is not well-described. It is not clear what the form of the statistical model used was and whether the analysis treated each trial individually or grouped trials by the kangaroo. There is also no mention of how many trials per kangaroo, or the range of speeds (or masses) tested.

The methods include the statistical model with the variables that we used, as well as the kangaroo masses (13.7 to 26.6 kg, mean: 20.9 ± 3.4 kg). We will move the range of speeds from the supplementary material to the results or figure captions. We will add information on the number of trials per kangaroo to the methods.

We did not group the data e.g. by using an average speed per individual for all their trials, or by comparing fast to slow groups (this was for display purposes in our figures, which we will make clearer in the methods).

Related to this, there is no mention of how different speeds were obtained. It seems that kangaroos hopped at a self-selected pace, thus it appears that not much variation was observed. I appreciate the difficulty of conducting these experiments in a controlled manner, but this doesn't exempt the authors from providing the details of their approach.

• Some figures (Figure 2 for example) present means for one of three speeds, yet the speeds are not reported (except in the legend) nor how these bins were determined, nor how many trials or kangaroos fit in each bin. A similar comment applies to the mass categories. It would be more convincing if the authors plotted the main metrics vs. speed to illustrate the significant trends they are reporting.

Thank you for this comment. The bins are used only for display purposes and not within the analysis. In the revised manuscript, we will ensure this is clear.

(2) The significance of the effects of mass is not clear. The introduction and abstract suggest that the paper is focused on the effect of speed, yet the effects of mass are reported throughout as well, without a clear understanding of the significance. This weakness is further exaggerated by the fact that the details of the subject masses are not reported.

Indeed, the primary aim of our study was to explore the influence of speed, given the uncoupling of energy from hopping speed in kangaroos. We included mass to ensure that the effects of speed were not driven by body mass (i.e.: that larger kangaroos hopped faster).  

(3) The paper needs to be significantly re-written to better incorporate the methods into the results section. Since the results come before the methods, some of the methods must necessarily be described such that the study can be understood at some level without turning to the dedicated methods section. As written, it is very difficult to understand the basis of the approach, analysis, and metrics without turning to the methods.

We agree, and in the revised manuscript will incorporate some of the methodological details within the results.

Author response image 1.

Author response:

Reviewer 1:

Summary:

Identifying drugs that target specific disease phenotypes remains a persistent challenge. Many current methods are only applicable to well-characterized small molecules, such as those with known structures. In contrast, methods based on transcriptional responses offer broader applicability because they do not require prior information about small molecules. Additionally, they can be rapidly applied to new small molecules. One of the most promising strategies involves the use of “drug response signatures”-specific sets of genes whose differential expression can serve as markers for the response to a small molecule. By comparing drug response signatures with expression profiles characteristic of a disease, it is possible to identify drugs that modulate the disease profile, indicating a potential therapeutic connection.

This study aims to prioritize potential drug candidates and to forecast novel drug combinations that may be effective in treating triple-negative breast cancer (TNBC). Large consortia, such as the LINCS-L1000 project, offer transcriptional signatures across various time points after exposing numerous cell lines to hundreds of compounds at different concentrations. While this data is highly valuable, its direct applicability to pathophysiological contexts is constrained by the challenges in extracting consistent drug response profiles from these extensive datasets. The authors use their method to create drug response profiles for three different TNBC cell lines from LINCS.

To create a more precise, cancer-specific disease profile, the authors highlight the use of single-cell RNA sequencing (scRNA-seq) data. They focus on TNBC epithelial cells collected from 26 diseased individuals compared to epithelial cells collected from 10 healthy volunteers. The authors are further leveraging drug response data to develop inhibitor combinations.

Strengths:

The authors of this study contribute to an ongoing effort to develop automated, robust approaches that leverage gene expression similarities across various cell lines and different treatment regimens, aiming to predict drug response signatures more accurately. The authors are trying to address the gap that remains in computational methods for inferring drug responses at the cell subpopulation level.

Weaknesses:

One weakness is that the authors do not compare their method to previous studies. The authors develop a drug response profile by summarizing the time points, concentrations, and cell lines. The computational challenge of creating a single gene list that represents the transcriptional response to a drug across different cell lines and treatment protocols has been previously addressed. The Prototype Ranked List (PRL) procedure, developed by Iorio and co-authors (PNAS, 2010, doi:10.1073/pnas.1000138107), uses a hierarchical majority-voting scheme to rank genes. This method generates a list of genes that are consistently overexpressed or downregulated across individual conditions, which then hold top positions in the PRL. The PRL methodology was used by Aissa and co-authors (Nature Comm 2021, doi:10.1038/s41467-021-21884-z) to analyze drug effects on selective cell populations using scRNA-seq datasets. They combined PRL with Gene Set Enrichment Analysis (GSEA), a method that compares a ranked list of genes like PRL against a specific set of genes of interest. GSEA calculates a Normalized Enrichment Score (NES), which indicates how well the genes of interest are represented among the top genes in the PRL. Compared to the method described in the current manuscript, the PRL method allows for the identification of both upregulated and downregulated transcriptional signatures relevant to the drug’s effects. It also gives equal weight to each cell line’s contribution to the drug’s overall response signature.

The authors performed experimental validation of the top two identified drugs; however, the effect was modest. In addition, the effect on TNBC cell lines was cell-line specific as the identified drugs were effective against BT20, whose transcriptional signatures from LINCS were used for drug identification, but not against the other two cell lines analyzed. An incorrect choice of genes for the signature may result in capturing similarities tied to experimental conditions (e.g., the same cell line) rather than the drug’s actual effects. This reflects the challenges faced by drug response signature methods in both selecting the appropriate subset of genes that make up the signature and managing the multiple expression profiles generated by treating different cell lines with the same drug.

We appreciate the reviewer’s thoughtful feedback and their suggestion to refer to the Prototype Ranked List (PRL) manuscript. Unfortunately, since this methodology for the PRL isn’t implemented in an open-source package, direct comparison with our approach is challenging. Nonetheless, we investigated whether using ranks would yield similar results for the most likely active drug pairs identified by retriever. To do this, we calculated and compared the rankings of the average effect sizes provided by retriever. Although the Spearman (ρ \= 0.98) correlation coefficient was high, we observed that key genes are disadvantaged when using ranks compared to effect sizes. This difference is particularly evident in the gene set enrichment analysis, where using average ranks identified only one pathway as statistically significantly enriched. The code to replicate these analyses is available at https://github.com/dosorio/L1000-TNBC/blob/main/Code/.

Author response image 1.

Given the similarity in purpose between retriever and the PRL approach, we have added the following statement to the introduction: “Previously, this goal was approached using a majority-voting scheme to rank genes across various cell types, concentrations, and time points. This approach generates a prototype ranked list (PRL) that represents the consistent ranks of genes across several cell lines in response to a specific drug.”

Regarding the experimental validation, we believe there is a misunderstanding about the evidence we provided. We would like to claridy that we used three different TNBC cell lines: CAL120, BT20, and DU4475. It’s important to note that CAL120 and DU4475 were not included in the signature generation process. Despite this, we observed effects that exceeded the additive effects expectations, particularly in the CAL120 cell line (Figure 5, Panel F).

Reviewer 2:

Summary:

In their study, Osorio and colleagues present ‘retriever,’ an innovative computational tool designed to extract disease-specific transcriptional drug response profiles from the LINCS-L1000 project. This tool has been effectively applied to TNBC, leveraging single-cell RNA sequencing data to predict drug combinations that may effectively target the disease. The public review highlights the significant integration of extensive pharmacological data with high-resolution transcriptomic information, which enhances the potential for personalized therapeutic applications.

Strengths:

A key finding of the study is the prediction and validation of the drug combination QL-XII-47 and GSK-690693 for the treatment of TNBC. The methodology employed is robust, with a clear pathway from data analysis to experimental confirmation.

Weaknesses:

However, several issues need to be addressed. The predictive accuracy of ’retriever’ is contingent upon the quality and comprehensiveness of the LINCS-L1000 and single-cell datasets utilized, which is an important caveat as these datasets may not fully capture the heterogeneity of patient responses to treatment. While the in vitro validation of the drug combinations is promising, further in vivo studies and clinical trials are necessary to establish their efficacy and safety. The applicability of these findings to other cancer types also warrants additional investigation. Expanding the application of ’retriever’ to a broader range of cancer types and integrating it with clinical data will be crucial for realizing its potential in personalized medicine. Furthermore, as the study primarily focuses on kinase inhibitors, it remains to be seen how well these findings translate to other drug classes.

We thank the reviewer for their thoughtful and constructive feedback. We appreciate your insights and agree that several important considerations need to be addressed.

We recognize that the predictive accuracy of retriever depends on the LINCS-L1000 and single-cell datasets. These resources may not fully represent the complete range of transcriptional responses to disease and treatment across different patients. As you mentioned, this is an important limitation. However, we believe that by extrapolating the evaluation of the most likely active compound to each individual patient, we can help address this issue. This approach will provide valuable insights into which patients in the study are most likely to respond positively to treatment.

On the in-vitro validation of drug combinations, we agree that while promising, these results are not sufficient on their own to establish clinical efficacy. Additional in-vivo studies will be essential in assessing the therapeutic potential and safety of these combinations, and clinical trials will be an important next step to validate the translational impact of our findings.

Lastly, we appreciate the reviewer’s comment about the focus of our study on kinase inhibitors. This result was unexpected, as we tested the full set of compounds from the LINCS-L1000 project. We agree that exploring other top candidates, including different drug classes, will be important for assessing how broadly retriever approach can be applied.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

Pradhan et al investigated the potential gustatory mechanisms that allow flies to detect cholesterol. They found that flies are indifferent to low cholesterol and avoid high cholesterol. They further showed that the ionotropic receptors Ir7g, Ir51b, and Ir56d are important for the cholesterol sensitivity in bitter neurons. The figures are clear and the behavior result is interesting. However, I have several major comments, especially on the discrepancy of the expression of these Irs with other lab published results, and the confusing finding that the same receptors (Ir7g, Ir51b) have been implicated in the detection of various seemingly unrelated compounds.

Strengths:

The results are very well presented, the figures are clear and well-made, text is easy to follow.

Weaknesses:

(1) Regarding the expression of Ir56d. The reported Ir56d expression pattern contradicts multiple previous studies (Brown et al., 2021 eLife, Figure 6a-c; Sanchez-Alcaniz et al., 2017 Nature Communications, Figure 4e-h; Koh et al., 2014 Neuron, Figure 3b). These studies, using three different driver lines, consistently showed Ir56d expression in sweet-sensing neurons and taste peg neurons. Importantly, Sanchez-Alcaniz et al. demonstrated that Ir56d is not expressed in Gr66a-expressing (bitter) neurons. This discrepancy is critical since Ir56d is identified as the key subunit for cholesterol detection in bitter neurons, and misexpression of Ir7g and Ir51b together is insufficient to confer cholesterol sensitivity (Fig.4b,d). Which Ir56d-GAL4 (and Gr66a-I-GFP) line was used in this study? Is there additional evidence (scRNA sequencing, in-situ hybridization, or immunostaining) supporting Ir56d expression in bitter neurons?

We agree that the expression pattern of Ir56d diverges from two prior reports . The studies by Brown et al. and Koh et al. employed the same Ir56d-GAL4 driver line, which exhibited expression in sweet-sensing gustatory receptor neurons (GRNs) and taste peg neurons, but not bitter GRNs (the Sanchez-Alcaniz et al. paper did not use an Ir56d-Gal4).

In our study, we used a Ir56d-GAL4 driver line (KDRC:2307) and the Gr66a-I-GFP reporter line (Weiss et al., 2011 Neuron). This is a crucial distinction, as differences in the regulatory regions used to generate different driver lines are well known to underlie differences in expression patterns. Our double-labeling experiments revealed co-expression of Ir56d with Gr66a-positive bitter GRNs specifically within the S6 and S7 sensilla—types previously shown to exhibit strong electrophysiological responses to cholesterol (Figure 2—figure supplement 1F).

We believe this observation is biologically significant and consistent with our functional data. Specifically, targeted expression of Ir56d in bitter neurons using the Gr33a-GAL4 was sufficient to rescue cholesterol avoidance behavior in Ir56d¹ mutants (Figure 3G). These results demonstrate that Ir56d plays a functional role in bitter GRNs for cholesterol detection. The convergence of genetic, behavioral, and electrophysiological data presented in our study provides compelling support for this previously unappreciated expression pattern and function of Ir56d.

(2) Ir51b has previously been implicated in detecting nitrogenous waste (Dhakal 2021), lactic acid (Pradhan 2024), and amino acids (Aryal 2022), all by the same lab. Additionally, both Ir7g and Ir51b have been implicated in detecting cantharidin, an insect-secreted compound that flies may or may not encounter in the wild, by the same lab. Is Ir51b proposed to be a specific receptor for these chemically distinct compounds or a general multimodal receptor for aversive stimuli? Unlike other multimodal bitter receptors, the expression level of Ir51b is rather low and it's unclear which subset of GRNs express this receptor. The chemical diversity among nitrogenous waste, amino acids, lactic acid, cantharidin, and cholesterol raises questions about the specificity of these receptors and warrants further investigation and at a minimum discussion in this paper. Given the wide and seemingly unrelated sensitivity of Ir51b and Ir7g to these compounds I'm leaning towards the hypothesis that at least some of these is non-specific and ecologically irrelevant without further supporting evidence from the authors.

While it is true that IR51b and IR7g are responsive to a range of compounds, they share chemical features such as nitrogen-containing groups, hydrophobicity, or amphipathic structures suggesting that recognition of these chemicals may be mediated by the same or overlapping domains within the receptor complexes. These features could facilitate binding to a structurally diverse yet chemically related groups of aversive ligands.

In the case of cholesterol, while its sterol ring system is distinct from the other compounds, it shares hydrophobic and amphipathic properties that may enable interaction with these receptors via similar structural motifs. Importantly, our data demonstrates that Ir51b and Ir7g are necessary but not sufficient on their own to confer cholesterol sensitivity, indicating that additional co-factors or receptor subunits are required for full functionality (Figure 4B, D). Furthermore, our dose-response analysis (Figure 3F) shows that Ir7g is particularly important at higher cholesterol concentrations, supporting the idea of graded sensitivity rather than indiscriminate activation. This suggests that these receptors may have evolved to recognize cholesterol and its analogs (e.g., phytosterols such as stigmasterol, yet to be tested), which are naturally found in the fly’s diet (e.g., yeast and plant-derived matter), as ecologically relevant cues signaling microbial contamination, lipid imbalance, or dietary overconsumption.

We acknowledge the reviewer’s concern regarding the relatively low expression levels of Ir51b and Ir7g. However, we note that low transcript abundance does not necessarily equate to diminished physiological relevance. Finally, we agree that the chemical diversity of ligands associated with Ir51b and Ir7g warrants deeper investigation, particularly through structure-function studies aimed at identifying ligand-binding domains and receptor-ligand interactions at atomic resolution.

(3) The Benton lab Ir7g-GAL4 reporter shows no expression in adults. Additionally, two independent labellar RNA sequencing studies (Dweck, 2021 eLife; Bontonou et al., 2024 Nature Communications) failed to detect Ir7g expression in the labellum. This contradicts the authors' previous RT-PCR results (Pradhan 2024 Fig. S4, Journal of Hazardous Materials) showing Ir7g expression in the labellum. Additionally the Benton and Carlson lab Ir51b-GAL4 reporters show no expression in adults as well. Please address these inconsistencies.

With respect to Ir7g, we acknowledge that the Ir7g-GAL4 reporter line from the Benton lab does not exhibit detectable expression in adult labella. Furthermore, two independent transcriptomic studies—Dweck et al., 2021 (eLife) and Bontonou et al., 2024 (Nature Communications) also did not detect Ir7g transcripts in bulk RNA-seq datasets derived from adult labella. However, our previously published RT-PCR data (Pradhan et al., 2024, Journal of Hazardous Materials, Fig. S4) revealed Ir7g expression in labellar tissue, albeit at low levels. Our RT-PCR includes an internal control (tubulin) with the same reaction tube with control and the Ir7g mutant as a negative control. Therefore, we stand behind the findings that Ir7g is expressed in the labellum.

We would like to point out that RT-PCR is more sensitive and better-suited to detect low-abundance transcripts than bulk RNA-seq, which may fail to capture transcripts due to limitations in depth of coverage. Moreover, immunohistochemistry can have limitations in detecting very low expression levels. Costa et al. 2013 (Translational lung cancer research) states that “RNA-Seq technique will not likely replace current RT-PCR methods, but will be complementary depending on the needs and the resources as the results of the RNA-Seq will identify those genes that need to then be examined using RT-PCR methods”.

Similarly, regarding Ir51b, while the GAL4 reporter lines from the Benton and Carlson labs do not show robust adult expression, our RT-PCR and functional data strongly support a role for Ir51b in labellar bitter GRNs. Specifically, Ir51b¹ mutants display electrophysiological deficits in response to cholesterol (Figure 2A–B), and these defects are rescued by expressing Ir51b in Gr33a-positive bitter neurons (Figure 3G), providing functional validation of the RT-PCR expression.

(4) The premise that high cholesterol intake is harmful to flies, which makes sensory mechanisms for cholesterol avoidance necessary, is interesting but underdeveloped. Animal sensory systems typically evolve to detect ecologically relevant stimuli with dynamic ranges matching environmental conditions. Given that Drosophila primarily consume fruits and plant matter (which contain minimal cholesterol) rather than animal-derived foods (which contain higher cholesterol), the ecological relevance of cholesterol detection requires more thorough discussion. Furthermore, at high concentrations, chemicals often activate multiple receptors beyond those specifically evolved for their detection. If the cholesterol concentrations used in this study substantially exceed those encountered in the fly's natural diet, the observed responses may represent an epiphenomenon rather than an ecologically and ethologically relevant sensory mechanism. What is the cholesterol content in flies' diet and how does that compare to the concentrations used in this paper?

Drosophila melanogaster cannot synthesize sterols de novo, and must acquire them from its diet. In natural environments, flies acquire sterols from fermenting fruit, decaying plant matter, and yeast, which contain trace amounts of phytosterols (e.g., stigmasterol, β-sitosterol) and ergosterol. While the exact sterol concentrations in these sources remain uncharacterized, our behavioral assays used concentrations (0.001–0.01% by weight) that align with the low levels expected in such nutrient-limited ecological niches.

In our study, the cholesterol concentrations tested ranged from 0.001% to 0.1%, thereby spanning both the physiologically relevant and slightly elevated range. Importantly, avoidance behaviors and receptor activation were most prominent at 0.1% cholesterol. While it is true that high chemical concentrations may elicit off-target effects via broad receptor activation, our genetic and electrophysiological data indicate that the observed responses are mediated by specific ionotropic receptors (Ir51b, Ir7g, Ir56d) and not merely generalized chemical stress.

Ecologically, elevated sterol levels may also signal conditions unsuitable for egg-laying or larval development. For example, high levels of cholesterol or other sterols may occur in substrates colonized by pathogenic microbes, decaying animal tissue, or in cases of abnormal microbial fermentation, which could represent a nutritional or microbial hazard. The avoidance of cholesterol may help signal the flies to avoid consuming decaying animal tissue. In this context, sensory detection of excessive cholesterol might serve as a protective function.

Reviewer #2 (Public review):

Summary:

In Cholesterol Taste Avoidance in Drosophila melanogaster, Pradhan et al. used behavioral and electrophysiological assays to demonstrate that flies can: (1) detect cholesterol through a subset of bitter-sensing gustatory receptor neurons (GRNs) and (2) avoid consuming food with high cholesterol levels. Mechanistically, they identified five members of the IR family as necessary for cholesterol detection in GRNs and for the corresponding avoidance behavior. Ectopic expression experiments further suggested that Ir7g + Ir56d or Ir51b + Ir56d may function as tuning receptors for cholesterol detection, together with the Ir25a and Ir76b co-receptors.

Strengths:

The experimental design of this study was logical and straightforward. Leveraging their expertise in the Drosophila taste system, the research team identified the molecular and cellular basis of a previously unrecognized taste category, expanding our understanding of gustation. A key strength of the study was its combination of electrophysiological recordings with behavioral genetic experiments.

Weaknesses:

My primary concern with this study is the lack of a systematic survey of the IRs of interest in the labellum GRNs. Consequently, there is no direct evidence linking the expression of putative cholesterol IRs to the B GRNs in the S6 and S7 sensilla.

Specifically, the authors need to demonstrate that the IR expression pattern explains cholesterol sensitivity in the B GRNs of S6 and S7 sensilla, but not in other sensilla. Instead of providing direct IR expression data for all candidate IRs (as shown for Ir56d in Figure 2-figure supplement 1F), the authors rely on citations from several studies (Lee, Poudel et al. 2018; Dhakal, Sang et al. 2021; Pradhan, Shrestha et al. 2024) to support their claim that Ir7g, Ir25a, Ir51b, and Ir76b are expressed in B GRNs (Lines 192-194). However, none of these studies provide GAL4 expression or in situ hybridization data to substantiate this claim.

Without a comprehensive IR expression profile for GRNs across all taste sensilla, it is difficult to interpret the ectopic expression results observed in the B GRN of the I9 sensillum or the A GRN of the L-sensillum (Figure 4). It remains equally plausible that other tuning IRs-beyond the co-receptor Ir25a and Ir76b-could interact with the ectopically expressed IRs to confer cholesterol sensitivity, rather than the proposed Ir7g + Ir56d or Ir51b + Ir56d combinations.

We provide electrophysiological data demonstrating that the S6 and S7 sensilla respond to cholesterol (Figure 1D). This finding is consistent with the hypothesis that these sensilla harbor the complete receptor complexes necessary for cholesterol detection. In our electrophysiological recordings, only those bitter GRNs that co-express Ir56d along with either Ir7g or Ir51b generate action potentials in response to cholesterol. Other S-type sensilla lacking one or more of these subunits remain unresponsive, reinforcing the idea that these components are necessary for receptor function and sensory coding of cholesterol. Moreover, in the cholesterol-insensitive I9 sensillum (based on our mapping results using electrophysiology), co-expression of either Ir7g + Ir56d or Ir51b + Ir56d conferred de novo cholesterol sensitivity (Figure 4B). Importantly, no cholesterol response was observed when any of these IRs was expressed alone or when Ir7g + Ir51b were co-expressed without Ir56d. These findings strongly argue against the possibility that endogenous tuning IRs in I9 sensilla (e.g., Ir25a, Ir76b) are sufficient to generate cholesterol responsiveness.

Furthermore, based on the literature, Ir25a and Ir76b are endogenously expressed in I- and L-type sensilla. Thus, their presence alone is insufficient for cholesterol responsiveness. These data support the model that cholesterol sensitivity depends on a specific, multi-subunit receptor complex (e.g., Ir7g + Ir25a + Ir56d + Ir76b or Ir51b + Ir25a + Ir56d + Ir76b).

In conclusion, while we acknowledge that our data do not provide a full anatomical map of IR expression across all sensilla, our results strongly support the idea that cholesterol sensitivity in S6 and S7 sensilla arises from specific combinations of IRs expressed in the B GRNs.

Reviewer #3 (Public review):

Summary:

Whether and how animals can taste cholesterol is not well understood. The study provides evidence that 1) cholesterol activates a subset of bitter-sensing gustatory receptor neurons (GRNs) in the fly labellum, but not other types of GRNs, 2) flies show aversion to high concentrations of cholesterol, and this is mediated by bitter GRNs, and 3) cholesterol avoidance depends on a specific set of ionotropic receptor (IR) subunits acting in bitter GRNs. The claims of the study are supported by electrophysiological recordings, genetic manipulations, and behavioral readouts.

Strengths:

Cholesterol taste has not been well studied, and the paper provides new insight into this question. The authors took a comprehensive and rigorous approach in several different parts of the paper, including screening the responses of all 31 labellar sensilla, screening a large panel of receptor mutants, and performing misexpression experiments with nearly every combination of the 5 IRs identified. The effects of the genetic manipulations are very clear and the results of electrophysiological and behavioral studies match nicely, for the most part. The appropriate controls are performed for all genetic manipulations.

Weaknesses:

The weaknesses of the study, described below, are relatively minor and do not detract from the main conclusions of the paper.

(1) The paper does not state what concentrations of cholesterol are present in Drosophila's natural food sources. Are the authors testing concentrations that are ethologically Drosophila melanogaster primarily feeds on fermenting fruits and associated microbial communities, especially yeast, which serve as major sources of dietary sterols. These natural food sources are known to contain phytosterols such as stigmasterol and β-sitosterol. One study quantified phytosterols (e.g., stigmasterol, sitosterol) in fruits, reporting concentrations between 1.6–32.6 mg/100 g edible portion (~0.0016–0.0326% wet weight) (Han et al 2008). The range we tested falls within this range. Additionally, ergosterol, the principal sterol in yeast and a structural analog of cholesterol, is present at levels of about 0.005% to 0.02% in yeast-rich environments.

To ensure physiological relevance, we designed our behavioral assays to include a broad concentration range of cholesterol, from 10^-5% to 10^-1%. This spans both physiological levels (0.001–0.01%), which are comparable to those found in the natural diet, and supra-physiological levels (e.g., 0.1%), which exceed natural exposure but help define the threshold for aversive behavior.

Our results demonstrate that flies begin to avoid cholesterol at concentrations ≥10^-3% more (Figure 3A), which falls within the upper physiological range and may reflect the threshold beyond which cholesterol or related sterols become deleterious. At these higher concentrations, excess sterols may disrupt membrane fluidity, interfere with hormone signaling, or promote microbial overgrowth—all of which could compromise fly health.

(2) The paper does not state or show whether the expression of IR7g, IR51b, and IR56d is confined to bitter GRNs. Bitter-specific expression of at least some of these receptors would be necessary to explain why bitter GRNs but not sugar GRNs (or other GRN types) normally show cholesterol responses.

We show the Ir56d-Gal4 is co-expressed with Gr66a-GFP in S6/S7 sensilla, indicating that it is expressed in bitter GRNs (Figure 2—figure supplement 1F). In the case of Ir7g and Ir51b, there are no reporters or antibodies to address expression. However, previously they have been shown to be expressed in bitter GRNs using RT-PCR (Dhakal et al. 2021, Communications Biology; Pradhan et al. 2024, Journal of Hazardous Materials). In addition, we provide functional evidence that bitter GRNs are required for the cholesterol response since silencing bitter GRNs abolishes cholesterol-induced action potentials (Figure 1E–F). Moreover, we showed that we could rescue the Ir7g¹, Ir51b¹ and Ir56d¹ mutant phenotypes only when we expressed the cognate transgenes in bitter GRNs using the Gr33a-GAL4 (Figure 3G). Thus, while Ir7g/Ir51b are not exclusive to bitter GRNs, their functional role in cholesterol detection is bitter-GRN-specific.

(3) The authors only investigated the responses of GRNs in the labellum, but GRN responses in the leg may also contribute to the avoidance of cholesterol feeding. Alternatively, leg GRNs might contribute to cholesterol attraction that is unmasked when bitter GRNs are silenced. In support of this possibility, Ahn et al. (2017) showed that Ir56d functions in sugar GRNs of the leg to promote appetitive responses to fatty acids.

This is an interesting idea. Indeed, when bitter GRNs are hyperpolarized, the flies exhibit a strong attraction to cholesterol. Nevertheless, the cellular basis for cholesterol attraction and whether it is mediated by GRNs in the legs will require a future investigation.

(4) The authors might consider using proboscis extension as an additional readout of taste attraction or aversion, which would help them more directly link the labellar GRN responses to a behavioral readout. Using food ingestion as a readout can conflate the contribution of taste with post-ingestive effects, and the regulation of food ingestion also may involve contributions from GRNs on multiple organs, whereas organ-specific contributions can be dissociated using proboscis extension. For example, does presenting cholesterol on the proboscis lead to aversive responses in the proboscis extension assay (e.g., suppression of responses to sugar)? Does this aversion switch to attraction when bitter GRNs are silenced, as with the feeding assay?

We thank the reviewer for the suggestion regarding the use of the proboscis extension reflex (PER) assay to strengthen the link between labellar GRN activity and behavioral responses to cholesterol.

Author response image 1.

Our PER assay results shown above indicate that cholesterol presentation on the labellum or forelegs leads to an aversive response, as evidenced by a significant reduction in proboscis extension when compared to control stimuli (Author response image 1A. 2% sucrose or 2% sucrose with 10^-1% cholesterol was applied to labellum or forelegs and the percent PER was recorded. n=6. Data were compared using single-factor ANOVA coupled with Scheffe’s post-hoc test. Statistical significance was compared with the control. Means ± SEMs. **p<0.01). This finding supports the idea that cholesterol is detected by labellar and leg GRNs and elicits behavioral avoidance. In contrast, sucrose stimulation robustly induces proboscis extension, as expected for an appetitive stimulus. We confirmed the defects of due to each Ir mutant by presenting the stimuli to the labellum (Author response image 1B). Together, these PER results provide a more direct behavioral correlate of labellar and leg GRN activation and reinforce our conclusion that cholesterol is sensed as an aversive tastant through the labellar bitter GRNs.

(5) The authors claim that the cholesterol receptor is composed of IR25a, IR76b, IR56d, and either IR7g or IR51b. While the authors have shown that IR25a and IR76b are each required for cholesterol sensing, they did not show that both are required components of the same receptor complex. If the authors are relying on previous studies to make this assumption, they should state this more clearly. Otherwise, I think further misexpression experiments may be needed where only IR25a or IR76b, but not both, are expressed in GRNs.

In our study, we relied on prior work demonstrating that Ir25a and Ir76b function as broadly required co-receptors in most IR-dependent chemosensory pathways (Ganguly et al., 2017; Lee et al., 2018). These studies showed that Ir25a and Ir76b are co-expressed in many GRNs across multiple taste modalities. Functional IR complexes often fail to form or signal properly in the absence of these co-receptors. Thus, it is widely accepted in the field that Ir25a and Ir76b function together as a core heteromeric scaffold for diverse IR complexes, akin to co-receptors in other ionotropic glutamate receptor families. We state that while Ir25a and Ir76b are presumed co-receptors in the cholesterol receptor complex based on their conserved roles, their direct physical interaction with Ir7g, Ir51b, and Ir56d remains to be demonstrated.

In support of this model, we note that in our ectopic expression experiments using I9 sensilla, which endogenously express Ir25a and Ir76b, introduction of either Ir7g + Ir56d or Ir51b + Ir56d was sufficient to confer cholesterol sensitivity (Figure 4B). We obtained a similar result in L6 sensilla (Figure 4D), which also endogenously express Ir25a and Ir76b. These findings imply that both co-receptors are already present in these sensilla and are likely part of the functional complex. However, we agree that we have not directly tested the requirement for both co-receptors in a minimal reconstitution context, such as expressing only Ir25a or Ir76b alongside tuning IRs in an otherwise null background. Such an experiment would indeed provide more direct evidence of their joint requirement in the receptor complex. Future studies, including heterologous expression experiments, will be necessary to define the cholesterol-receptor complexes.

Author Response

Reviewer #1 (Public Review):

The authors introduce a computational model that simulates the dendrites of developing neurons in a 2D plane, subject to constraints inspired by known biological mechanisms such as diffusing trophic factors, trafficked resources, and an activity-dependent pruning rule. The resulting arbors are analyzed in terms of their structure, dynamics, and responses to certain manipulations. The authors conclude that 1) their model recapitulates a stereotyped timecourse of neuronal development: outgrowth, overshoot, and pruning 2) Neurons achieve near-optimal wiring lengths, and Such models can be useful to test proposed biological mechanisms- for example, to ask whether a given set of growth rules can explain a given observed phenomenon - as developmental neuroscientists are working to understand the factors that give rise to the intricate structures and functions of the many cell types of our nervous system.

Overall, my reaction to this work is that this is just one instantiation of many models that the author could have built, given their stated goals. Would other models behave similarly? This question is not well explored, and as a result, claims about interpreting these models and using them to make experimental predictions should be taken warily. I give more detailed and specific comments below.

We thank the reviewer for the summary of the work. We find the criticism “that this is one instantiation of many models [we] could have built” can apply to any model. To quote George Box, “all models are wrong, but some models are useful” was the moto that drove our modeling approach. In principle, there are infinitely many possible models. We chose one of the most minimalistic models which implements known biological mechanisms including activity-independent and -dependent phases of dendritic growth, and constrained parameters based on experimental data. We compare the proposed model to other alternatives in the Discussion section, especially to the models of Hermann Cuntz which propose very different strategies for growth.

However, the reviewer is right that within the type of model we chose, we could have more extensively explored the sensitivity to parameters. In the revised manuscript we will investigate the sensitivity of model output to variations of specific parameters, as explained below.

Point 1.1. Line 109. After reading the rest of the manuscript, I worry about the conclusion voiced here, which implies that the model will extrapolate well to manipulations of all the model components. How were the values of model parameters selected? The text implies that these were selected to be biologically plausible, but many seem far off. The density of potential synapses, for example, seems very low in the simulations compared to the density of axons/boutons in the cortex; what constitutes a potential synapse? The perfect correlations between synapses in the activity groups is flawed, even for synapses belonging to the same presynaptic cell. The density of postsynaptic cells is also orders of magnitude of, etc. Ideally, every claim made about the model's output should be supported by a parameter sensitivity study. The authors performed few explorations of parameter sensitivity and many of the choices made seem ad hoc.

It is indeed important to clarify how the model parameters were selected. Here we provide a short justification for some of these parameters, which will be included in the revised manuscript.

1) Potential synapse density: We modelled 1,500 potential synapses in a cortical sheet of size 185x185 microns squared. We used 1 pixel per μm to capture approximately 1 μm thick dendrites. Therefore, we started with initial density of 0.044 potential synapses per μm^2. From Author Response Image 1 we can see that at the end of our simulation time ~1,000 potential synapses remain. So in fact, the density of potential synapses is totally sufficient, since not many potential synapses end up connected. The rapid slowing down of growth in our model is not due to a depletion of potential synaptic partners as the number of potential synapses remains high. Nonetheless, we will explore this in the revised manuscript. (this figure will be included in the revised submission):

2) Stabilized synapse density: Since ~1,000 of the potential synapses in the modeled cortical sheet remain available, ~500 become connected to the dendrites of the 9 somas in the modeled cortical sheet. This means that the density of stable connected synapses is approximately 0.015 synapses per μm^2. This is also the number that is shown in Figure 3b, which is about 60 synapses stabilized per cell. This density is much easier to compare to experimental data, and below we provide some numbers from literature we already cited in the manuscript as well as a recent preprint.

In the developing cortex:

• Leighton, Cheyne and Lohmann 2023 https://doi.org/10.1101/2023.03.02.530772 find up to 0.4 synapses per μm in pyramidal neurons in vivo in the developing mouse visual cortex at P8 to P13. This is almost identical to our value of 0.4 synapses per μm.

• Ultanir et al., 2007 https://doi.org/10.1073/pnas.0704031104 find 0.7 to 1.7 spines per μm in pyramidal neurons in vivo in L2/3 of the developing mouse cortex, at P10 to P20.

• Glynn et al., 2011 https://doi.org/10.1038/nn.2764 find 0.1 to 0.7 spines per μm^2 in pyramidal neurons in vivo and in vitro in L2/3 of the developing mouse cortex, at P8 to P60.

In the developing hippocampus:

• Yang et al., 2014 https://doi.org/10.1016/j.celrep.2014.03.040 find 0.75 to 1 spines per μm in pyramidal neurons in vivo in CA1 of the developing mouse hippocampus, at one month of age.

• Koshimizu et al., 2009 https://doi.org/10.1186/1756-6606-2-27 find 0.1 to 0.4 spines per μm in pyramidal neurons in slice in the developing rat hippocampus, at (Embryonic Day) ED18 to ED20.

• Tyler and Pozzo-Miller, 2001 https://doi.org/10.1523/JNEUROSCI.21-12-04249.2001 find 0.28 to 0.1 spines per μm in slice in the developing mouse hippocampus, at P7 (14 DIV, days in vitro).

Although these values vary somewhat across experiments, in most cases they are in agreement with our chosen values, especially when taking into account that we are modeling development (rather than adulthood).

3) Soma/neuron density: Indeed, we did not exactly mention this number anywhere in the paper. But from the figures we can infer 9 somas growing dendrites on an area of ~34,000 μm^2. Thus, neuron density would be 300 neurons per mm^2. This number seems a bit low after a short search through the literature. For e.g. Keller et al., 2018 https://www.frontiersin.org/articles/10.3389/fnana.2018.00083/full reports about 90,000 neurons per mm^3, albeit in adulthood.

We are also performing a sensitivity analysis where some of these parameters are varied and will include this in the revised manuscript. In particular:

(1) We will vary the nature of the input correlations. In the current model, the synapses in each correlated group receive spike trains with a perfect correlation and there are no correlations across the groups. We will reduce the correlations within group and add non-zero correlations across the groups.

(2) We will vary the density of the neuronal somas. We expect that higher densities of somas will either yield smaller dendritic areas because the different neurons compete more or result in a state where nearby neurons have to complement each other regarding their activity preferences.

(3) We will introduce dynamics in the potential synapses to model the dynamics of axons. We plan to explore several scenarios. We could introduce a gradual increase in the density of potential synapses and implement a cap on the number of synapses that can be alive at the same time, and vary that cap. We could also introduce a lifetime of each synapse (following for example a lognormal distribution). A potential synapse can disappear if it does not form a stable synapse in its lifetime, in which case it could move to a different location.

Point 1.2. Many potentially important phenomena seem to be excluded. I realize that no model can be complete, but the choice of which phenomena to include or exclude from this model could bias studies that make use of it and is worth serious discussion. The development of axons is concurrent with dendrite outgrowth, is highly dynamic, and perhaps better understood mechanistically. In this model, the inputs are essentially static. Growing dendrites acquire and lose growth cones that are associated with rapid extension, but these do not seem to be modeled. Postsynaptic firing does not appear to be modeled, which may be critical to activity-dependent plasticity. For example, changes in firing are a potential explanation for the global changes in dendritic pruning that occur following the outgrowth phase.

As the reviewer concludes, no model can be complete. In agreement with this, here we would like to quote a paragraph from a very nice paper by Larry Abbott (“Theoretical Neuroscience Rising, Neuron 2008 https://www.sciencedirect.com/science/article/pii/S0896627308008921) which although published more than 10 years ago, still applies today:

“Identifying the minimum set of features needed to account for a particular phenomenon and describing these accurately enough to do the job is a key component of model building. Anything more than this minimum set makes the model harder to understand and more difficult to evaluate. The term ‘‘realistic’’ model is a sociological rather than a scientific term. The truly realistic model is as impossible and useless a concept as Borges’ ‘‘map of the empire that was of the same scale as the empire and that coincided with it point for point’’ (Borges, 1975). […] The art of modeling lies in deciding what this subset should be and how it should be described.”

We have clearly stated in the Introduction (e.g. lines 37-75) which phenomena we include in the model and why. The Discussion also compares our model to others (lines 315-373), pointing out that most models either focus on activity-independent or activity-dependent phases. We include both, combining literature on molecular gradients and growth factors, with activity-dependent connectivity refinements instructed by spontaneous activity. We could not think of a more tractable, more minimalist model that would include both activity-independent or activity-dependent aspects. Therefore, we feel that the current manuscript provides sufficient motivation but also a discussion of limitations of the current model.

Regarding including the concurrent development of axons, we agree this is very interesting and currently not addressed in the model. As noted at the bottom of our reply to point 1.1, bullet (3) we are now revising the manuscript to include a simplified form of axonal dynamics by allowing changes in the lifetime and location of potential synapses, which come from axons of presynaptic partners.

Regarding postsynaptic firing, this is indeed super relevant and an important point to consider. In one of our recent publications (Kirchner and Gjorgjieva, 2021 https://www.nature.com/articles/s41467-021-23557-3), we studied only an activity-dependent model for the organization of synaptic inputs on non-growing dendrites which have a fixed length. There, we considered the effect of postsynaptic firing and demonstrated that it plays an important role in establishing a global organization of synapses on the entire dendritic tree of the neuron, and not just local dendritic branches. For example, we showed that could that it could lead to the emergence of retinotopic maps which have been found experimentally (Iacaruso et al., 2017 https://www.nature.com/articles/nature23019). Since we use the same activity-dependent plasticity model in this paper, we expect that the somatic firing will have the same effect on establishing synaptic distributions on the entire dendritic tree. We will make a note of this in the Discussion in the revised paper.

Point 1.3. Line 167. There are many ways to include activity -independent and -dependent components into a model and not every such model shows stability. A key feature seems to be that larger arbors result in reduced growth and/or increased retraction, but this could be achieved in many ways (whether activity dependent or not). It's not clear that this result is due to the combination of activity-dependent and independent components in the model, or conceptually why that should be the case.

We never argued for model uniqueness. There are always going to be many different models (at different spatial and temporal scales, at different levels of abstraction). We can never study all of them and like any modeling study in systems neuroscience we have chosen one model approach and investigated this approach. We do compare the current model to others in the Discussion. If the reviewers have a specific implementation that we should compare our model to as an alternative, we could try, but not if this means doing a completely separate project.

Point 1.4. Line 183. The explanation of overshoot in terms of the different timescales of synaptic additions versus activity-dependent retractions was not something I had previously encountered and is an interesting proposal. Have these timescales been measured experimentally? To what extent is this a result of fine-tuning of simulation parameters?

We found that varying the amount of BDNF controls the timescale of the activity-dependent plasticity (see our Figure 5c). Hence, changing the balance between synaptic additions vs. retractions is already explored in Figure 5e and f. Here we show that the overshoot and retraction does not have to be fine-tuned but may be abolished if there is too much activity-dependent plasticity.

Regarding the relative timescales of synaptic additions vs. retractions: since the first is mainly due to activity-independent factors, and the second due to activity-dependent plasticity, the questions is really about the timescales of the latter two. As we write in the Introduction (lines 60-62), manipulating activity-dependent synaptic transmission has been found to not affect morphology but rather the density and specificity of synaptic connections (Ultanir et al. 2007 https://doi.org/10.1073/pnas.0704031104), supporting the sequential model we have (although we do not impose the sequence, as both activity-independent and activity-dependent mechanisms are always “on”; but note that activity-dependent plasticity can only operate on synapses that have already formed).

Point 1.5. Line 203. This result seems at odds with results that show only a very weak bias in the tuning distribution of inputs to strongly tuned cortical neurons (e.g. work by Arthur Konnerth's group). This discrepancy should be discussed.

First, we note that the correlated activity experienced by our modeled synapses (and resulting synaptic organization) does not necessarily correspond to visual orientation, or any stimulus feature, for that matter.

Nonetheless, this is a very interesting question and there is some variability in what the experimental data show. Many studies have shown that synapses on dendrites are organized into functional synaptic clusters: across brain regions, developmental ages and diverse species from rodent to primate (Kleindienst et al. 2011; Takahashi et al. 2012; Winnubst et al. 2015; Gökçe et al., 2016; Wilson et al. 2016; Iacaruso et al., 2017; Scholl et al., 2017; Niculescu et al. 2018; Kerlin et al. 2019; Ju et al. 2020). Interestingly, some in vivo studies have reported lack of fine-scale synaptic organization (Varga et al. 2011; X. Chen et al. 2011; T.-W. Chen et al. 2013; Jia et al. 2010; Jia et al. 2014), while others reported clustering for different stimulus features in different species. For example, dendritic branches in the ferret visual cortex exhibit local clustering of orientation selectivity but do not exhibit global organization of inputs according to spatial location and receptive field properties (Wilson et al. 2016; Scholl et al., 2017). In contrast, synaptic inputs in mouse visual cortex do not cluster locally by orientation, but only by receptive field overlap, and exhibit a global retinotopic organization along the proximal-distal axis (Iacaruso et al., 2017). We proposed a theoretical framework to reconcile these data: combining activity-dependent plasticity similar to the BDNF-proBDNF model that we used in the current work, and a receptive field model for the different species (Kirchner and Gjorgjieva, 2021 https://www.nature.com/articles/s41467-021-23557-3). We can mention this aspect in the revised manuscript.

Point 1.6. Line 268. How does the large variability in the size of the simulated arbors relate to the relatively consistent size of arbors of cortical cells of a given cell type? This variability suggests to me that these simulations could be sensitive to small changes in parameters (e.g. to the density or layout of presynapses).

As noted at the bottom of our reply to point 1.1, bullet (3) we are now revising the manuscript to include changes in the lifetime and location of potential synapses.

Point 1.7. The modeling of dendrites as two-dimensional will likely limit the usefulness of this model. Many phenomena- such as diffusion, random walks, topological properties, etc - fundamentally differ between two and three dimensions.

The reviewer is right about there being differences between two and three dimensions. But a simpler model does not mean a useless model even if not completely realistic. We have ongoing work that extends the current model to 3D but is beyond the scope of the current paper. In systems neuroscience, people have found very interesting results making such simplified geometric assumptions about networks, for instance the one-dimensional ring model has been used to uncover fundamental insights about computations even though highly simplified and abstracted.

Point 1.8. The description of wiring lengths as 'approximately optimal' in this text is problematic. The plotted data show that the wiring lengths are several deviations away from optimal, and the random model is not a valid instantiation of the 2D non-overlapping constraints the authors imposed. A more appropriate null should be considered.

We did not use the term “optimal” in line with previous literature. We wrongly referred to the minimal wiring length as the optimal wiring length, but neurons can optimize their wiring not only by minimizing their dendritic length (e.g. work of Hermann Cuntz). In the revised manuscript, we will replace the term “optimal wiring” with “minimal wiring”. Then we will compare the wiring length in the model with the theoretically minimal wiring length, the random wiring length and the actual data.

Point 1.9. It's not clear to me what the authors are trying to convey by repeatedly labeling this model as 'mechanistic'. The mechanisms implemented in the model are inspired by biological phenomena, but the implementations have little resemblance to the underlying biophysical mechanisms. Overall my impression is that this is a phenomenological model intended to show under what conditions particular patterns are possible. Line 363, describing another model as computational but not mechanistic, was especially unclear to me in this context.

What we mean by mechanistic is that we implement equations that model specific mechanisms i.e. we have a set of equations that implement the activity-independent attraction to potential synapses (with parameters such as the density of synapses, their spatial influence, etc) and the activity-dependent refinement of synapses (with parameters such as the ratio of BDNF and proBDNF to induce potentiation vs depression, the activity-dependent conversion of one factor to the other, etc). This is a bottom-up approach where we combine multiple elements together to get to neuronal growth and synaptic organization. This approach is in stark contrast to the so-called top-down or normative approaches where the method would involve defining an objective function (e.g. minimal dendritic length) which depends on a set of parameters and then applying a gradient descent or other mathematical optimization technique to get at the parameters that optimize the objective function. This latter approach we would not call mechanistic because it involves an abstract objective function (who could say what a neuron or a circuit should be trying to optimize) and a mathematical technique for how to optimize the function (we don’t know of neurons can compute gradients of abstract objective functions).

Hence our model is mechanistic, but it does operate at a particular level of abstraction/simplification. We don’t model individual ion channels, or biophysics of synaptic plasticity (opening and closing of NMDA channels, accumulation of proteins at synapses, protein synthesis). We do, however, provide a biophysical implementation of the plasticity mechanism though the BDNF/proBDNF model which is more than most models of plasticity achieve, because they typically model a phenomenological STDP or Hebbian rule that just uses activity patterns to potential or depress synaptic weights, disregarding how it could be implemented.

Reviewer #2 (Public Review):

This work combines a model of two-dimensional dendritic growth with attraction and stabilisation by synaptic activity. The authors find that constraining growth models with competition for synaptic inputs produces artificial dendrites that match some key features of real neurons both over development and in terms of final structure. In particular, incorporating distance-dependent competition between synapses of the same dendrite naturally produces distinct phases of dendritic growth (overshoot, pruning, and stabilisation) that are observed biologically and leads to local synaptic organisation with functional relevance. The approach is elegant and well-explained, but makes some significant modelling assumptions that might impact the biological relevance of the results.

Strengths:

The main strength of the work is the general concept of combining morphological models of growth with synaptic plasticity and stabilisation. This is an interesting way to bridge two distinct areas of neuroscience in a manner that leads to findings that could be significant for both. The modelling of both dendritic growth and distance-dependent synaptic competition is carefully done, constrained by reasonable biological mechanisms, and well-described in the text. The paper also links its findings, for example in terms of phases of dendritic growth or final morphological structure, to known data well.

Weaknesses:

The major weaknesses of the paper are the simplifying modelling assumptions that are likely to have an impact on the results. These assumptions are not discussed in enough detail in the current version of the paper.

1) Axonal dynamics.

A major, and lightly acknowledged, assumption of this paper is that potential synapses, which must come from axons, are fixed in space. This is not realistic for many neural systems, as multiple undifferentiated neurites typically grow from the soma before an axon is specified (Polleux & Snider, 2010). Further, axons are also dynamic structures in early development and, at least in some systems, undergo activity-dependent morphological changes too (O'Leary, 1987; Hall 2000). This paper does not consider the implications of joint pre- and post-synaptic growth and stabilisation.

We thank the reviewer for the summary of the strengths and weaknesses of the work. While we feel that including a full model of axonal dynamics is beyond the scope of the current manuscript, some aspects of axonal dynamics can be included. In a revised model, we will introduce a gradual increase in the density of potential synapses and implement a cap on the number of synapses that can be alive at the same time, and vary that cap. We plan to also introduce a lifetime of each synapse (following for example a lognormal distribution). A potential synapse can disappear if it does not form a stable synapse in its lifetime, in which case it could move to a different location. See also our reply to reviewer comment 1.1, bullet (3).

2) Activity correlations

On a related note, the synapses in the manuscript display correlated activity, but there is no relationship between the distance between synapses and their correlation. In reality, nearby synapses are far more likely to share the same axon and so display correlated activity. If the input activity is spatially correlated and synaptic plasticity displays distance-dependent competition in the dendrites, there is likely to be a non-trivial interaction between these two features with a major impact on the organisation of synaptic contacts onto each neuron.

We are exploring the amount of correlation (between and within correlated groups) to include in the revised manuscript (see also our reply to reviewer comment 1.1, bullet (1)).

However, previous experimental work, (Kleindienst et al., 2011 https://doi.org/10.1016/j.neuron.2011.10.015) has provided anatomical and functional analyses that it is unlikely that the functional synaptic clustering on dendritic branches is the result of individual axons making more than one synapse (see pg. 1019).

3) BDNF dynamics

The models are quite sensitive to the ratio of BDNF to proBDNF (eg Figure 5c). This ratio is also activity-dependent as synaptic activation converts proBDNF into BDNF. The models assume a fixed ratio that is not affected by synaptic activity. There should at least be more justification for this assumption, as there is likely to be a positive feedback relationship between levels of BDNF and synaptic activation.

The reviewer is correct. We used the BDNF-proBDNF model for synaptic plasticity based on our previous work: Kirchner and Gjorgjieva, 2021 https://www.nature.com/articles/s41467-021-23557-3.

There, we explored only the emergence of functionally clustered synapses on static dendrites which do not grow. In the Methods section (Parameters and data fitting) we justify the choice of the ratio of BDNF to proBDNF from published experimental work. We also performed sensitivity analysis (Supplementary Fig. 1) and perturbation simulations (Supplementary Fig. 3), which showed that the ratio is crucial in regulating the overall amount of potentiation and depression of synaptic efficacy, and therefore has a strong impact on the emergence and maintenance of synaptic organization. Since we already performed all this analysis, we do not expect there will be any differences in the current model which includes dendritic growth, as the activity-dependent mechanism has such a different timescale.

A further weakness is in the discussion of how the final morphologies conform to principles of optimal wiring, which is quite imprecise. 'Optimal wiring' in the sense of dendrites and axons (Cajal, 1895; Chklovskii, 2004; Cuntz et al, 2007, Budd et al, 2010) is not usually synonymous with 'shortest wiring' as implied here. Instead, there is assumed to be a balance between minimising total dendritic length and minimising the tree distance (ie Figure 4c here) between synapses and the site of input integration, typically the soma. The level of this balance gives the deviation from the theoretical minimum length as direct paths to synapses typically require longer dendrites. In the model this is generated by the guidance of dendritic growth directly towards the synaptic targets. The interpretation of the deviation in this results section discussing optimal wiring, with hampered diffusion of signalling molecules, does not seem to be correct.

We agree with this comment. We had wrongly used the term “optimal wiring” as neurons can optimize their wiring not only by minimizing their dendritic length but other factors as noted by the reviewer. In the revised manuscript will replace the term “optimal wiring” with “minimal wiring” and discuss these differences to previous work.

Reviewer #3 (Public Review):

The authors propose a mechanistic model of how the interplay between activity-independent growth and an activity-dependent synaptic strengthening/weaken model influences the dendrite shape, complexity and distribution of synapses. The authors focus on a model for stellate cells, which have multiple dendrites emerging from a soma. The activity independent component is provided by a random pool of presynaptic sites that represent potential synapses and that release a diffusible signal that promotes dendritic growth. Then a spontaneous activity pattern with some correlation structure is imposed at those presynaptic sites. The strength of these synapses follow a learning rule previously proposed by the lab: synapses strengthen when there is correlated firing across multiple sites, and synapses weaken if there is uncorrelated firing with the relative strength of these processes controlled by available levels of BDNF/proBDNF. Once a synapse is weakened below a threshold, the dendrite branch at that site retracts and loses its sensitivity to the growth signal

The authors run the simulation and map out how dendrites and synapses evolve and stabilize. They show that dendritic trees growing rapidly and then stabilize by balancing growth and retraction (Figure 2). They also that there is an initial bout of synaptogenesis followed by loss of synapses, reflecting the longer amount of time it takes to weaken a synapse (Figure 3). They analyze how this evolution of dendrites and synapses depends on the correlated firing of synapses (i.e. defined as being in the same "activity group"). They show that in the stabilized phase, synapses that remain connected to a given dendritic branch are likely to be from same activity group (Figure 4). The authors systemically alter the learning rule by changing the available concentration of BDNF, which alters the relative amount of synaptic strengthening, which in turn affects stabilization, density of synapses and interestingly how selective for an activity group one dendrite is (Figure 5). In addition the authors look at how altering the activity-independent factors influences outgrowth (Figure 6). Finally, one of the interesting outcomes is that the resulting dendritic trees represent "optimal wiring" solutions in the sense that dendrites use the shortest distance given the distribution of synapses. They compare this distribute to one published data to see how the model compared to what has been observed experimentally.

There are many strengths to this study. The consequence of adding the activity-dependent contribution to models of synapto- and dendritogenesis is novel. There is some exploration of parameters space with the motivation of keeping the parameters as well as the generated outcomes close to anatomical data of real dendrites. The paper is also scholarly in its comparison of this approach to previous generative models. This work represented an important advance to our understanding of how learning rules can contribute to dendrite morphogenesis

We thank the reviewer for the positive evaluation of the work and the suggestions below.

Author response:

Reviewer #1 (Evidence, reproducibility and clarity):

Authors has provided a mechanism by which how presence of truncated P53 can inactivate function of full length P53 protein. Authors proposed this happens by sequestration of full length P53 by truncated P53.

In the study, performed experiments are well described.

My area of expertise is molecular biology/gene expression, and I have tried to provide suggestions on my area of expertise. The study has been done mainly with overexpression system and I have included few comments which I can think can be helpful to understand effect of truncated P53 on endogenous wild type full length protein. Performing experiments on these lines will add value to the observation according to this reviewer.

Major comments:

(1) What happens to endogenous wild type full length P53 in the context of mutant/truncated isoforms, that is not clear. Using a P53 antibody which can detect endogenous wild type P53, can authors check if endogenous full length P53 protein is also aggregated as well? It is hard to differentiate if aggregation of full length P53 happens only in overexpression scenario, where lot more both of such proteins are expressed. In normal physiological condition P53 expression is usually low, tightly controlled and its expression get induced in altered cellular condition such as during DNA damage. So, it is important to understand the physiological relevance of such aggregation, which could be possible if authors could investigate effect on endogenous full length P53 following overexpression of mutant isoforms.

Thank you very much for your insightful comments.

(1) To address “what happens to endogenous wild-type full-length P53 in the context of mutant/truncated isoforms," we employed a human A549 cell line expressing endogenous wild-type p53 under DNA damage conditions such as an etoposide treatment(1). We choose the A549 cell line since similar to H1299, it is a lung cancer cell line (www.atcc.org). For comparison, we also transfected the cells with 2 μg of V5-tagged plasmids encoding FLp53 and its isoforms Δ133p53 and Δ160p53. As shown in Author response image 1A, lanes 1 and 2, endogenous p53 expression, remained undetectable in A549 cells despite etoposide treatment, which limits our ability to assess the effects of the isoforms on the endogenous wild-type FLp53. We could, however, detect the V5-tagged FLp53 expressed from the plasmid using anti-V5 (rabbit) as well as with antiDO-1 (mouse) antibody (Author response image 1). The latter detects both endogenous wildtype p53 and the V5-tagged FLp53 since the antibody epitope is within the Nterminus (aa 20-25). This result supports the reviewer’s comment regarding the low level of expression of endogenous p53 that is insufficient for detection in our experiments.   

In summary, in line with the reviewer’s comment that ‘under normal physiological conditions p53 expression is usually low,’ we could not detect p53 with an anti-DO-1 antibody. Thus, we proceeded with V5/FLAG-tagged p53 for detection of the effects of the isoforms on p53 stability and function. We also found that protein expression in H1299 cells was more easily detectable than in A549 cells (Compare Author response image 1A and B). Thus, we decided to continue with the H1299 cells (p53-null), which would serve as a more suitable model system for this study.  

(2) We agree with the reviewer that ‘It is hard to differentiate if aggregation of full-length p53 happens only in overexpression scenario’. However, it is not impossible to imagine that such aggregation of FLp53 happens under conditions when p53 and its isoforms are over-expressed in the cell. Although the exact physiological context is not known and beyond the scope of the current work, our results indicate that at higher expression, p53 isoforms drive aggregation of FLp53. Given the challenges of detecting endogenous FLp53, we had to rely on the results obtained with plasmid mediated expression of p53 and its isoforms in p53-null cells.

Author response image 1.

Comparative analysis of protein expression in A549 and H1299 cells. (A) A549 cells (p53 wild-type) were treated with etoposide to induce endogenous wild-type p53 expression. To assess the effects of FLp53 and its isoforms Δ133p53 and Δ160p53 on endogenous wild-type p53 aggregation, A549 cells were transfected with 2 μg of V5-tagged p53 expression plasmids, with or without etoposide (20μM for 8h) treatment. Western blot analysis was done with the anti-V5 (rabbit) to detect V5-tagged proteins and anti-DO-1 (mouse), the latter detects both endogenous wild-type p53 and V5-tagged FLp53. The merged image corresponds to the overlay between the V5 and DO1 antibody signals. (B) H1299 cells (p53-null) were transfected with 2 μg V5tagged p53 expression plasmids or the empty vector control pcDNA3.1. Western blot analysis was done with the anti-V5 (mouse) antibody. 

(2) Can presence of mutant P53 isoforms can cause functional impairment of wild type full length endogenous P53? That could be tested as well using similar ChIP assay authors has performed, but instead of antibody against the Tagged protein if the authors could check endogenous P53 enrichment in the gene promoter such as P21 following overexpression of mutant isoforms. May be introducing a condition such as DNA damage in such experiment might help where endogenous P53 is induced and more prone to bind to P53 target such as P21.

Thank you very much for your valuable comments and suggestions. To investigate the potential functional impairment of endogenous wild-type p53 by p53 isoforms, we initially utilized A549 cells (p53 wild-type), aiming to monitor endogenous wild-type p53 expression following DNA damage. However, as mentioned and demonstrated in Author response image 1, endogenous p53 expression was too low to be detected under these conditions, making the ChIP assay for analyzing endogenous p53 activity unfeasible. Thus, we decided to utilize plasmid-based expression of FLp53 and focus on the potential functional impairment induced by the isoforms.

(3) On similar lines, authors described:

"To test this hypothesis, we escalated the ratio of FLp53 to isoforms to 1:10. As expected, the activity of all four promoters decreased significantly at this ratio (Figure 4A-D). Notably, Δ160p53 showed a more potent inhibitory effect than Δ133p53 at the 1:5 ratio on all promoters except for the p21 promoter, where their impacts were similar (Figure 4E-H). However, at the 1:10 ratio, Δ133p53 and Δ160p53 had similar effects on all transactivation except for the MDM2 promoter (Figure 4E-H)."

Again, in such assay authors used ratio 1:5 to 1:10 full length vs mutant. How authors justify this result in context (which is more relevant context) where one allele is Wild type (functional P53) and another allele is mutated (truncated, can induce aggregation). In this case one would except 1:1 ratio of full-length vs mutant protein, unless other regulation is going which induces expression of mutant isoforms more than wild type full length protein. Probably discussing on these lines might provide more physiological relevance to the observed data.

Thank you for raising this point regarding the physiological relevance of the ratios used in our study.

(1) In the revised manuscript (lines 193-195), we added in this direction that “The elevated Δ133p53 protein modulates p53 target genes such as miR‑34a and p21, facilitating cancer development(2, 3). To mimic conditions where isoforms are upregulated relative to FLp53, we increased the ratios to 1:5 and 1:10.” This approach aims to simulate scenarios where isoforms accumulate at higher levels than FLp53, which may be relevant in specific contexts, as also elaborated above.

(2) Regarding the issue of protein expression, where one allele is wild-type and the other is isoform, this assumption is not valid in most contexts. First, human cells have two copies of TPp53 gene (one from each parent). Second, the TP53 gene has two distinct promoters: the proximal promoter (P1) primarily regulates FLp53 and ∆40p53, whereas the second promoter (P2) regulates ∆133p53 and ∆160p53(4, 5). Additionally, ∆133TP53 is a p53 target gene(6, 7) and the expression of Δ133p53 and FLp53 is dynamic in response to various stimuli. Third, the expression of p53 isoforms is regulated at multiple levels, including transcriptional, post-transcriptional, translational, and post-translational processing(8). Moreover, different degradation mechanisms modify the protein level of p53 isoforms and FLp53(8). These differential regulation mechanisms are regulated by various stimuli, and therefore, the 1:1 ratio of FLp53 to ∆133p53 or ∆160p53 may be valid only under certain physiological conditions. In line with this, varied expression levels of FLp53 and its isoforms, including ∆133p53 and ∆160p53, have been reported in several studies(3, 4, 9, 10). 

(3) In our study, using the pcDNA 3.1 vector under the human cytomegalovirus (CMV) promoter, we observed moderately higher expression levels of ∆133p53 and ∆160p53 relative to FLp53 (Author response image 1B). This overexpression scenario provides a model for studying conditions where isoform accumulation might surpass physiological levels, impacting FLp53 function. By employing elevated ratios of these isoforms to FLp53, we aim to investigate the potential effects of isoform accumulation on FLp53.

(4) Finally does this altered function of full length P53 (preferably endogenous one) in presence of truncated P53 has any phenotypic consequence on the cells (if authors choose a cell type which is having wild type functional P53). Doing assay such as apoptosis/cell cycle could help us to get this visualization.

Thank you for your insightful comments. In the experiment with A549 cells (p53 wild-type), endogenous p53 levels were too low to be detected, even after DNA damage induction. The evaluation of the function of endogenous p53 in the presence of isoforms is hindered, as mentioned above. In the revised manuscript, we utilized H1299 cells with overexpressed proteins for apoptosis studies using the Caspase-Glo® 3/7 assay (Figure 7). This has been shown in the Results section (lines 254-269). “The Δ133p53 and Δ160p53 proteins block pro-apoptotic function of FLp53.

One of the physiological read-outs of FLp53 is its ability to induce apoptotic cell death(11). To investigate the effects of p53 isoforms Δ133p53 and Δ160p53 on FLp53-induced apoptosis, we measured caspase-3 and -7 activities in H1299 cells expressing different p53 isoforms (Figure 7). Caspase activation is a key biochemical event in apoptosis, with the activation of effector caspases (caspase-3 and -7) ultimately leading to apoptosis(12). The caspase-3 and -7 activities induced by FLp53 expression was approximately 2.5 times higher than that of the control vector (Figure 7). Co-expression of FLp53 and the isoforms Δ133p53 or Δ160p53 at a ratio of 1: 5 significantly diminished the apoptotic activity of FLp53 (Figure 7). This result aligns well with our reporter gene assay, which demonstrated that elevated expression of Δ133p53 and Δ160p53 impaired the expression of apoptosis-inducing genes BAX and PUMA (Figure 4G and H). Moreover, a reduction in the apoptotic activity of FLp53 was observed irrespective of whether Δ133p53 or Δ160p53 protein was expressed with or without a FLAG tag (Figure 7). This result, therefore, also suggests that the FLAG tag does not affect the apoptotic activity or other physiological functions of FLp53 and its isoforms. Overall, the overexpression of p53 isoforms Δ133p53 and Δ160p53 significantly attenuates FLp53-induced apoptosis, independent of the protein tagging with the FLAG antibody epitope.”

Referees cross-commenting

I think the comments from the other reviewers are very much reasonable and logical.

Especially all 3 reviewers have indicated, a better way to visualize the aggregation of full-length wild type P53 by truncated P53 (such as looking at endogenous P53# by reviewer 1, having fluorescent tag #by reviewer 2 and reviewer 3 raised concern on the FLAG tag) would add more value to the observation.

Thank you for these comments. The endogenous p53 protein was undetectable in A549 cells induced by etoposide (Figure R1A). Therefore, we conducted experiments using FLAG/V5-tagged FLp53.  To avoid any potential side effects of the FLAG tag on p53 aggregation, we introduced untagged p53 isoforms in the H1299 cells and performed subcellular fractionation. Our revised results, consistent with previous FLAG-tagged p53 isoforms findings, demonstrate that co-expression of untagged isoforms with FLAG-tagged FLp53 significantly induced the aggregation of FLAG-FLp53, while no aggregation was observed when FLAG-tagged FLp53 was expressed alone (Supplementary Figure 6). These results clearly indicate that the FLAG tag itself does not contribute to protein aggregation. 

Additionally, we utilized the A11 antibody to detect protein aggregation, providing additional validation (Figure 8 from Jean-Christophe Bourdon et al. Genes Dev. 2005;19:2122-2137). Given that the fluorescent proteins (~30 kDa) are substantially bigger than the tags used here (~1 kDa) and may influence oligomerization (especially GFP), stability, localization, and function of p53 and its isoforms, we avoided conducting these vital experiments with such artificial large fusions. 

Reviewer #1 (Significance):

The work in significant, since it points out more mechanistic insight how wild type full length P53 could be inactivated in the presence of truncated isoforms, this might offer new opportunity to recover P53 function as treatment strategies against cancer.

Thank you for your insightful comments. We appreciate your recognition of the significance of our work in providing mechanistic insights into how wild-type FLp53 can be inactivated by truncated isoforms. We agree that these findings have potential for exploring new strategies to restore p53 function as a therapeutic approach against cancer. 

Reviewer #2 (Evidence, reproducibility and clarity):

The manuscript by Zhao and colleagues presents a novel and compelling study on the p53 isoforms, Δ133p53 and Δ160p53, which are associated with aggressive cancer types. The main objective of the study was to understand how these isoforms exert a dominant negative effect on full-length p53 (FLp53). The authors discovered that the Δ133p53 and Δ160p53 proteins exhibit impaired binding to p53-regulated promoters. The data suggest that the predominant mechanism driving the dominant-negative effect is the coaggregation of FLp53 with Δ133p53 and Δ160p53.

This study is innovative, well-executed, and supported by thorough data analysis. However, the authors should address the following points:

(1) Introduction on Aggregation and Co-aggregation: Given that the focus of the study is on the aggregation and co-aggregation of the isoforms, the introduction should include a dedicated paragraph discussing this issue. There are several original research articles and reviews that could be cited to provide context.

Thank you very much for the valuable comments. We have added the following paragraph in the revised manuscript (lines 74-82): “Protein aggregation has become a central focus of modern biology research and has documented implications in various diseases, including cancer(13, 14, 15). Protein aggregates can be of different types ranging from amorphous aggregates to highly structured amyloid or fibrillar aggregates, each with different physiological implications. In the case of p53, whether protein aggregation, and in particular, co-aggregation with large N-terminal deletion isoforms, plays a mechanistic role in its inactivation is yet underexplored. Interestingly, the Δ133p53β isoform has been shown to aggregate in several human cancer cell lines(16). Additionally, the Δ40p53α isoform exhibits a high aggregation tendency in endometrial cancer cells(17). Although no direct evidence exists for Δ160p53 yet, these findings imply that p53 isoform aggregation may play a major role in their mechanisms of actions.”

(2) Antibody Use for Aggregation: To strengthen the evidence for aggregation, the authors should consider using antibodies that specifically bind to aggregates.

Thank you for your insightful suggestion. We addressed protein aggregation using the A11 antibody which specifically recognizes amyloid-like protein aggregates. We analyzed insoluble nuclear pellet samples prepared under identical conditions as described in Figure 6B. To confirm the presence of p53 proteins, we employed the anti-p53 M19 antibody (Santa Cruz, Cat No. sc-1312) to detect bands corresponding to FLp53 and its isoforms Δ133p53 and Δ160p53. The monomer FLp53 was not detected (Figure 8, lower panel, Jean-Christophe Bourdon et al. Genes Dev. 2005;19:2122-2137), which may be attributed to the lower binding affinity of the anti-p53 M19 antibody to it. These samples were also immunoprecipitated using the A11 antibody (Thermo Fischer Scientific, Cat No. AHB0052) to detect aggregated proteins. Interestingly, FLp53 and its isoforms, Δ133p53 and Δ160p53, were clearly visible with Anti-A11 antibody when co-expressed at a 1:5 ratio suggesting that they underwent co-aggregation. However, no FLp53 aggregates were observed when it was expressed alone (Author response image 2). These results support the conclusion in our manuscript that Δ133p53 and Δ160p53 drive FLp53 aggregation. 

Author response image 2.

Induction of FLp53 Aggregation by p53 Isoforms Δ133p53 and Δ160p53. H1299 cells transfected with the FLAG-tagged FLp53 and V5-tagged Δ133p53 or Δ160p53 at a 1:5 ratio. The cells were subjected to subcellular fractionation, and the resulting insoluble nuclear pellet was resuspended in RIPA buffer. The samples were heated at 95°C until the pellet was completely dissolved, and then analyzed by Western blotting. Immunoprecipitation was performed using the A11 antibody, which specifically recognizes amyloid protein aggregates, and the anti-p53 M19 antibody, which detects FLp53 as well as its isoforms Δ133p53 and Δ160p53. 

(3) Fluorescence Microscopy: Live-cell fluorescence microscopy could be employed to enhance visualization by labeling FLp53 and the isoforms with different fluorescent markers (e.g., EGFP and mCherry tags).

We appreciate the suggestion to use live-cell fluorescence microscopy with EGFP and mCherry tags for the visualization FLp53 and its isoforms. While we understand the advantages of live-cell imaging with EGFP / mCherry tags, we restrained us from doing such fusions as the GFP or corresponding protein tags are very big (~30 kDa) with respect to the p53 isoform variants (~30 kDa).  Other studies have shown that EGFP and mCherry fusions can alter protein oligomerization, solubility and aggregation(18, 19) Moreover, most fluorescence proteins are prone to dimerization (i.e. EGFP) or form obligate tetramers (DsRed)(20, 21, 22), potentially interfering with the oligomerization and aggregation properties of p53 isoforms, particularly Δ133p53 and Δ160p53.

Instead, we utilized FLAG- or V5-tag-based immunofluorescence microscopy, a well-established and widely accepted method for visualizing p53 proteins. This method provided precise localization and reliable quantitative data, which we believe meet the needs of the current study. We believe our chosen method is both appropriate and sufficient for addressing the research question.

Reviewer #2 (Significance):

The manuscript by Zhao and colleagues presents a novel and compelling study on the p53 isoforms, Δ133p53 and Δ160p53, which are associated with aggressive cancer types. The main objective of the study was to understand how these isoforms exert a dominant negative effect on full-length p53 (FLp53). The authors discovered that the Δ133p53 and Δ160p53 proteins exhibit impaired binding to p53-regulated promoters. The data suggest that the predominant mechanism driving the dominant-negative effect is the coaggregation of FLp53 with Δ133p53 and Δ160p53.

We sincerely thank the reviewer for the thoughtful and positive comments on our manuscript and for highlighting the significance of our findings on the p53 isoforms, Δ133p53 and Δ160p53. 

Reviewer #3 (Evidence, reproducibility and clarity):

In this manuscript entitled "Δ133p53 and Δ160p53 isoforms of the tumor suppressor protein p53 exert dominant-negative effect primarily by coaggregation", the authors suggest that the Δ133p53 and Δ160p53 isoforms have high aggregation propensity and that by co-aggregating with canonical p53 (FLp53), they sequestrate it away from DNA thus exerting a dominantnegative effect over it.

First, the authors should make it clear throughout the manuscript, including the title, that they are investigating Δ133p53α and Δ160p53α since there are 3 Δ133p53 isoforms (α, β, γ), and 3 Δ160p53 isoforms (α, β, γ).

Thank you for your suggestion. We understand the importance of clearly specifying the isoforms under study. Following your suggestion, we have added α in the title, abstract, and introduction and added the following statement in the Introduction (lines 57-59): “For convenience and simplicity, we have written Δ133p53 and Δ160p53 to represent the α isoforms (Δ133p53α and Δ160p53α) throughout this manuscript.” 

One concern is that the authors only consider and explore Δ133p53α and Δ160p53α isoforms as exclusively oncogenic and FLp53 dominant-negative while not discussing evidences of different activities. Indeed, other manuscripts have also shown that Δ133p53α is non-oncogenic and non-mutagenic, do not antagonize every single FLp53 functions and are sometimes associated with good prognosis. To cite a few examples:

(1) Hofstetter G. et al. D133p53 is an independent prognostic marker in p53 mutant advanced serous ovarian cancer. Br. J. Cancer 2011, 105, 15931599.

(2) Bischof, K. et al. Influence of p53 Isoform Expression on Survival in HighGrade Serous Ovarian Cancers. Sci. Rep. 2019, 9,5244.

(3) Knezovi´c F. et al. The role of p53 isoforms' expression and p53 mutation status in renal cell cancer prognosis. Urol. Oncol. 2019, 37, 578.e1578.e10.

(4) Gong, L. et al. p53 isoform D113p53/D133p53 promotes DNA doublestrand break repair to protect cell from death and senescence in response to DNA damage. Cell Res. 2015, 25, 351-369.

(5) Gong, L. et al. p53 isoform D133p53 promotes efficiency of induced pluripotent stem cells and ensures genomic integrity during reprogramming. Sci. Rep. 2016, 6, 37281.

(6) Horikawa, I. et al. D133p53 represses p53-inducible senescence genes and enhances the generation of human induced pluripotent stem cells. Cell Death Differ. 2017, 24, 1017-1028.

(7) Gong, L. p53 coordinates with D133p53 isoform to promote cell survival under low-level oxidative stress. J. Mol. Cell Biol. 2016, 8, 88-90.

Thank you very much for your comment and for highlighting these important studies. 

We agree that Δ133p53 isoforms exhibit complex biological functions, with both oncogenic and non-oncogenic potentials. However, our mission here was primarily to reveal the molecular mechanism for the dominant-negative effects exerted by the Δ133p53α and Δ160p53α isoforms on FLp53 for which the Δ133p53α and Δ160p53α isoforms are suitable model systems. Exploring the oncogenic potential of the isoforms is beyond the scope of the current study and we have not claimed anywhere that we are reporting that. We have carefully revised the manuscript and replaced the respective terms e.g. ‘prooncogenic activity’ with ‘dominant-negative effect’ in relevant places (e.g. line 90). We have now also added a paragraph with suitable references that introduces the oncogenic and non-oncogenic roles of the p53 isoforms.

After reviewing the papers you cited, we are not sure that they reflect on oncogenic /non-oncogenic role of the Δ133p53α isoform in different cancer cases.  Although our study is not about the oncogenic potential of the isoforms, we have summarized the key findings below:

(1) Hofstetter et al., 2011: Demonstrated that Δ133p53α expression improved recurrence-free and overall survival (in a p53 mutant induced advanced serous ovarian cancer, suggesting a potential protective role in this context.

(2) Bischof et al., 2019: Found that Δ133p53 mRNA can improve overall survival in high-grade serous ovarian cancers. However, out of 31 patients, only 5 belong to the TP53 wild-type group, while the others carry TP53 mutations.

(3) Knezović et al., 2019: Reported downregulation of Δ133p53 in renal cell carcinoma tissues with wild-type p53 compared to normal adjacent tissue, indicating a potential non-oncogenic role, but not conclusively demonstrating it.

(4) Gong et al., 2015: Showed that Δ133p53 antagonizes p53-mediated apoptosis and promotes DNA double-strand break repair by upregulating RAD51, LIG4, and RAD52 independently of FLp53.

(5) Gong et al., 2016: Demonstrated that overexpression of Δ133p53 promotes efficiency of cell reprogramming by its anti-apoptotic function and promoting DNA DSB repair. The authors hypotheses that this mechanism is involved in increasing RAD51 foci formation and decrease γH2AX foci formation and chromosome aberrations in induced pluripotent stem (iPS) cells, independent of FL p53.

(6) Horikawa et al., 2017: Indicated that induced pluripotent stem cells derived from fibroblasts that overexpress Δ133p53 formed noncancerous tumors in mice compared to induced pluripotent stem cells derived from fibroblasts with complete p53 inhibition. Thus, Δ133p53 overexpression is "non- or less oncogenic and mutagenic" compared to complete p53 inhibition, but it still compromises certain p53-mediated tumor-suppressing pathways. “Overexpressed Δ133p53 prevented FL-p53 from binding to the regulatory regions of p21WAF1 and miR-34a promoters, providing a mechanistic basis for its dominant-negative

inhibition of a subset of p53 target genes.”

(7) Gong, 2016: Suggested that Δ133p53 promotes cell survival under lowlevel oxidative stress, but its role under different stress conditions remains uncertain.

We have revised the Introduction to provide a more balanced discussion of Δ133p53’s dule role (lines 62-73):

“The Δ133p53 isoform exhibit complex biological functions, with both oncogenic and non-oncogenic potentials. Recent studies demonstrate the non-oncogenic yet context-dependent role of the Δ133p53 isoform in cancer development. Δ133p53 expression has been reported to correlate with improved survival in patients with TP53 mutations(23, 24), where it promotes cell survival in a nononcogenic manner(25, 26), especially under low oxidative stress(27). Alternatively, other recent evidences emphasize the notable oncogenic functions of Δ133p53 as it can inhibit p53-dependent apoptosis by directly interacting with the FLp53 (4, 6). The oncogenic function of the newly identified Δ160p53 isoform is less known, although it is associated with p53 mutation-driven tumorigenesis(28) and in melanoma cells’ aggressiveness(10). Whether or not the Δ160p53 isoform also impedes FLp53 function in a similar way as Δ133p53 is an open question. However, these p53 isoforms can certainly compromise p53-mediated tumor suppression by interfering with FLp53 binding to target genes such as p21 and miR-34a(2, 29) by dominant-negative effect, the exact mechanism is not known.” On the figures presented in this manuscript, I have three major concerns:

(1) Most results in the manuscript rely on the overexpression of the FLAGtagged or V5-tagged isoforms. The validation of these construct entirely depends on Supplementary figure 3 which the authors claim "rules out the possibility that the FLAG epitope might contribute to this aggregation. However, I am not entirely convinced by that conclusion. Indeed, the ratio between the "regular" isoform and the aggregates is much higher in the FLAG-tagged constructs than in the V5-tagged constructs. We can visualize the aggregates easily in the FLAG-tagged experiment, but the imaging clearly had to be overexposed (given the white coloring demonstrating saturation of the main bands) to visualize them in the V5-tagged experiments. Therefore, I am not convinced that an effect of the FLAG-tag can be ruled out and more convincing data should be added. 

Thank you for raising this important concern. We have carefully considered your comments and have made several revisions to clarify and strengthen our conclusions.

First, to address the potential influence of the FLAG and V5 tags on p53 isoform aggregation, we have revised Figure 2 and removed the previous Supplementary Figure 3, where non-specific antibody bindings and higher molecular weight aggregates were not clearly interpretable. In the revised Figure 2, we have removed these potential aggregates, improving the clarity and accuracy of the data.

To further rule out any tag-related artifacts, we conducted a coimmunoprecipitation assay with FLAG-tagged FLp53 and untagged Δ133p53 and Δ160p53 isoforms. The results (now shown in the new Supplementary Figure 3) completely agree with our previous result with FLAG-tagged and V5tagged Δ133p53 and Δ160p53 isoforms and show interaction between the partners. This indicates that the FLAG / V5-tags do not influence / interfere with the interaction between FLp53 and the isoforms. We have still used FLAGtagged FLp53 as the endogenous p53 was undetectable and the FLAG-tagged FLp53 did not aggregate alone. 

In the revised paper, we added the following sentences (Lines 146-152): “To rule out the possibility that the observed interactions between FLp53 and its isoforms Δ133p53 and Δ160p53 were artifacts caused by the FLAG and V5 antibody epitope tags, we co-expressed FLAG-tagged FLp53 with untagged Δ133p53 and Δ160p53. Immunoprecipitation assays demonstrated that FLAGtagged FLp53 could indeed interact with the untagged Δ133p53 and Δ160p53 isoforms (Supplementary Figure 3, lanes 3 and 4), confirming formation of hetero-oligomers between FLp53 and its isoforms. These findings demonstrate that Δ133p53 and Δ160p53 can oligomerize with FLp53 and with each other.”

Additionally, we performed subcellular fractionation experiments to compare the aggregation and localization of FLAG-tagged FLp53 when co-expressed either with V5-tagged or untagged Δ133p53/Δ160p53. In these experiments, the untagged isoforms also induced FLp53 aggregation, mirroring our previous results with the tagged isoforms (Supplementary Figure 5). We’ve added this result in the revised manuscript (lines 236-245): “To exclude the possibility that FLAG or V5 tags contribute to protein aggregation, we also conducted subcellular fractionation of H1299 cells expressing FLAG-tagged FLp53 along with untagged Δ133p53 or Δ160p53 at a 1:5 ratio. The results showed (Supplementary Figure 6) a similar distribution of FLp53 across cytoplasmic, nuclear, and insoluble nuclear fractions as in the case of tagged Δ133p53 or Δ160p53 (Figure 6A to D). Notably, the aggregation of untagged Δ133p53 or Δ160p53 markedly promoted the aggregation of FLAG-tagged FLp53 (Supplementary Figure 6B and D), demonstrating that the antibody epitope tags themselves do not contribute to protein aggregation.” 

We’ve also discussed this in the Discussion section (lines 349-356): “In our study, we primarily utilized an overexpression strategy involving FLAG/V5tagged proteins to investigate the effects of p53 isoforms Δ133p53 and Δ160p53 on the function of FLp53. To address concerns regarding potential overexpression artifacts, we performed the co-immunoprecipitation (Supplementary Figure 6) and caspase-3 and -7 activity (Figure 7) experiments with untagged Δ133p53 and Δ160p53. In both experimental systems, the untagged proteins behaved very similarly to the FLAG/V5 antibody epitopecontaining proteins (Figures 6 and 7 and Supplementary Figure 6). Hence, the C-terminal tagging of FLp53 or its isoforms does not alter the biochemical and physiological functions of these proteins.”

In summary, the revised data set and newly added experiments provide strong evidence that neither the FLAG nor the V5 tag contributes to the observed p53 isoform aggregation.

(2) The authors demonstrate that to visualize the dominant-negative effect, Δ133p53α and Δ160p53α must be "present in a higher proportion than FLp53 in the tetramer" and the need at least a transfection ratio 1:5 since the 1:1 ration shows no effect. However, in almost every single cell type, FLp53 is far more expressed than the isoforms which make it very unlikely to reach such stoichiometry in physiological conditions and make me wonder if this mechanism naturally occurs at endogenous level. This limitation should be at least discussed.

Thank you for your insightful comment. However, evidence suggests that the expression levels of these isoforms such as Δ133p53, can be significantly elevated relative to FLp53 in certain physiological conditions(3, 4, 9). For example, in some breast tumors, with Δ133p53 mRNA is expressed at a much levels than FLp53, suggesting a distinct expression profile of p53 isoforms compared to normal breast tissue(4). Similarly, in non-small cell lung cancer and the A549 lung cancer cell line, the expression level of Δ133p53 transcript is significantly elevated compared to non-cancerous cells(3). Moreover, in specific cholangiocarcinoma cell lines, the Δ133p53 /TAp53 expression ratio has been reported to increase to as high as 3:1(9). These observations indicate that the dominant-negative effect of isoform Δ133p53 on FLp53 can occur under certain pathological conditions where the relative amounts of the FLp53 and the isoforms would largely vary. Since data on the Δ160p53 isoform are scarce, we infer that the long N-terminal truncated isoforms may share a similar mechanism.

(3) Figure 5C: I am concerned by the subcellular location of the Δ133p53α and Δ160p53α as they are commonly considered nuclear and not cytoplasmic as shown here, particularly since they retain the 3 nuclear localization sequences like the FLp53 (Bourdon JC et al. 2005; Mondal A et al. 2018; Horikawa I et al, 2017; Joruiz S. et al, 2024). However, Δ133p53α can form cytoplasmic speckles (Horikawa I et al, 2017) when it colocalizes with autophagy markers for its degradation.

The authors should discuss this issue. Could this discrepancy be due to the high overexpression level of these isoforms? A co-staining with autophagy markers (p62, LC3B) would rule out (or confirm) activation of autophagy due to the overwhelming expression of the isoform.

Thank you for your thoughtful comments. We have thoroughly reviewed all the papers you recommended (Bourdon JC et al., 2005; Mondal A et al., 2018; Horikawa I et al., 2017; Joruiz S. et al., 2024)(4, 29, 30, 31). Among these, only the study by Bourdon JC et al. (2005) provided data regarding the localization of Δ133p53(4). Interestingly, their findings align with our observations, indicating that the protein does not exhibit predominantly nuclear localization in the Figure 8 from Jean-Christophe Bourdon et al. Genes Dev. 2005;19:2122-2137. The discrepancy may be caused by a potentially confusing statement in that paper(4).

The localization of p53 is governed by multiple factors, including its nuclear import and export(32). The isoforms Δ133p53 and Δ160p53 contain three nuclear localization sequences (NLS)(4). However, the isoforms Δ133p53 and Δ160p53 were potentially trapped in the cytoplasm by aggregation and masking the NLS. This mechanism would prevent nuclear import. 

Further, we acknowledge that Δ133p53 co-aggregates with autophagy substrate p62/SQSTM1 and autophagosome component LC3B in cytoplasm by autophagic degradation during replicative senescence(33). We agree that high overexpression of these aggregation-prone proteins may induce endoplasmic reticulum (ER) stress and activates autophagy(34). This could explain the cytoplasmic localization in our experiments. However, it is also critical to consider that we observed aggregates in both the cytoplasm and the nucleus (Figures 6B and E and Supplementary Figure 6B). While cytoplasmic localization may involve autophagy-related mechanisms, the nuclear aggregates likely arise from intrinsic isoform properties, such as altered protein folding, independent of autophagy. These dual localizations reflect the complex behavior of Δ133p53 and Δ160p53 isoforms under our experimental conditions.

In the revised manuscript, we discussed this in Discussion (lines 328-335): “Moreover, the observed cytoplasmic isoform aggregates may reflect autophagy-related degradation, as suggested by the co-localization of Δ133p53 with autophagy substrate p62/SQSTM1 and autophagosome component LC3B(33). High overexpression of these aggregation-prone proteins could induce endoplasmic reticulum stress and activate autophagy(34). Interestingly, we also observed nuclear aggregation of these isoforms (Figure 6B and E and Supplementary Figure 6B), suggesting that distinct mechanisms, such as intrinsic properties of the isoforms, may govern their localization and behavior within the nucleus. This dual localization underscores the complexity of Δ133p53 and Δ160p53 behavior in cellular systems.”

Minor concerns:

-  Figure 1A: the initiation of the "Δ140p53" is shown instead of "Δ40p53"

Thank you! The revised Figure 1A has been created in the revised paper.

-  Figure 2A: I would like to see the images cropped a bit higher, so the cut does not happen just above the aggregate bands

Thank you for this suggestion. We’ve changed the image and the new Figure 2 has been shown in the revised paper.

-  Figure 3C: what ratio of FLp53/Delta isoform was used?

We have added the ratio in the figure legend of Figure 3C (lines 845-846) “Relative DNA-binding of the FLp53-FLAG protein to the p53-target gene promoters in the presence of the V5-tagged protein Δ133p53 or Δ160p53 at a 1: 1 ratio.”

-  Figure 3C suggests that the "dominant-negative" effect is mostly senescencespecific as it does not affect apoptosis target genes, which is consistent with Horikawa et al, 2017 and Gong et al, 2016 cited above. Furthermore, since these two references and the others from Gong et al. show that Δ133p53α increases DNA repair genes, it would be interesting to look at RAD51, RAD52 or Lig4, and maybe also induce stress.

Thank you for your thoughtful comments and suggestions. In Figure 3C, the presence of Δ133p53 or Δ160p53 only significantly reduced the binding of FLp53 to the p21 promoter. However, isoforms Δ133p53 and Δ160p53 demonstrated a significant loss of DNA-binding activity at all four promoters: p21, MDM2, and apoptosis target genes BAX and PUMA (Figure 3B). This result suggests that Δ133p53 and Δ160p53 have the potential to influence FLp53 function due to their ability to form hetero-oligomers with FLp53 or their intrinsic tendency to aggregate. To further investigate this, we increased the isoform to FLp53 ratio in Figure 4, which demonstrate that the isoforms Δ133p53 and Δ160p53 exert dominant-negative effects on the function of FLp53. 

These results demonstrate that the isoforms can compromise p53-mediated pathways, consistent with Horikawa et al. (2017), which showed that Δ133p53α overexpression is "non- or less oncogenic and mutagenic" compared to complete p53 inhibition, but still affects specific tumor-suppressing pathways. Furthermore, as noted by Gong et al. (2016), Δ133p53’s anti-apoptotic function under certain conditions is independent of FLp53 and unrelated to its dominantnegative effects.

We appreciate your suggestion to investigate DNA repair genes such as RAD51, RAD52, or Lig4, especially under stress conditions. While these targets are intriguing and relevant, we believe that our current investigation of p53 targets in this manuscript sufficiently supports our conclusions regarding the dominant-negative effect. Further exploration of additional p53 target genes, including those involved in DNA repair, will be an important focus of our future studies.

- Figure 5A and B: directly comparing the level of FLp53 expressed in cytoplasm or nucleus to the level of Δ133p53α and Δ160p53α expressed in cytoplasm or nucleus does not mean much since these are overexpressed proteins and therefore depend on the level of expression. The authors should rather compare the ratio of cytoplasmic/nuclear FLp53 to the ratio of cytoplasmic/nuclear Δ133p53α and Δ160p53α.

Thank you very much for this valuable suggestion. In the revised paper, Figure 5B has been recreated.  Changes have been made in lines 214215: “The cytoplasm-to-nucleus ratio of Δ133p53 and Δ160p53 was approximately 1.5-fold higher than that of FLp53 (Figure 5B).” 

Referees cross-commenting

I agree that the system needs to be improved to be more physiological.

Just to precise, the D133 and D160 isoforms are not truncated mutants, they are naturally occurring isoforms expressed in almost every normal human cell type from an internal promoter within the TP53 gene.

Using overexpression always raises concerns, but in this case, I am even more careful because the isoforms are almost always less expressed than the FLp53, and here they have to push it 5 to 10 times more expressed than the FLp53 to see the effect which make me fear an artifact effect due to the overwhelming overexpression (which even seems to change the normal localization of the protein).

To visualize the endogenous proteins, they will have to change cell line as the H1299 they used are p53 null.

Thank you for these comments. We’ve addressed the motivation of overexpression in the above responses. We needed to use the plasmid constructs in the p53-null cells to detect the proteins but the expression level was certainly not ‘overwhelmingly high’. 

First, we tried the A549 cells (p53 wild-type) under DNA damage conditions, but the endogenous p53 protein was undetectable. Second, several studies reported increased Δ133p53 level compared to wild-type p53 and that it has implications in tumor development(2, 3, 4, 9). Third, the apoptosis activity of H1299 cells overexpressing p53 proteins was analyzed in the revised manuscript (Figure 7). The apoptotic activity induced by FLp53 expression was approximately 2.5 times higher than that of the control vector under identical plasmid DNA transfection conditions (Figure 7). These results rule out the possibility that the plasmid-based expression of p53 and its isoforms introduced artifacts in the results. We’ve discussed this in the Results section (lines 254269).

Reviewer #3 (Significance):

Overall, the paper is interesting particularly considering the range of techniques used which is the main strength.

The main limitation to me is the lack of contradictory discussion as all argumentation presents Δ133p53α and Δ160p53α exclusively as oncogenic and strictly FLp53 dominant-negative when, particularly for Δ133p53α, a quite extensive literature suggests a not so clear-cut activity.

The aggregation mechanism is reported for the first time for Δ133p53α and Δ160p53α, although it was already published for Δ40p53α, Δ133p53β or in mutant p53.

This manuscript would be a good basic research addition to the p53 field to provide insight in the mechanism for some activities of some p53 isoforms.

My field of expertise is the p53 isoforms which I have been working on for 11 years in cancer and neuro-degenerative diseases

Thank you very much for your positive and critical comments. We’ve included a fair discussion on the oncogenic and non-oncogenic function of Δ133p53 in the Introduction following your suggestion (lines 62-73). 

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Author Response

Reviewer #1 (Public Review):

Weaknesses:

1) The authors should better review what we know of fungal Drosophila microbiota species as well as the ecology of rotting fruit. Are the microbiota species described in this article specific to their location/setting? It would have been interesting to know if similar species can be retrieved in other locations using other decaying fruits. The term 'core' in the title suggests that these species are generally found associated with Drosophila but this is not demonstrated. The paper is written in a way that implies the microbiota members they have found are universal. What is the evidence for this? Have the fungal species described in this paper been found in other studies? Even if this is not the case, the paper is interesting, but there should be a discussion of how generalizable the findings are.

The reviewer inquires as to whether the microbial species described in this article are ubiquitously associated with Drosophila or not. Indeed, most of the microbes described in this manuscript are generally recognized as species associated with Drosophila spp. For example, species such as Hanseniaspora uvarum, Pichia kluyveri, and Starmerella bacillaris have been detected in or isolated from Drosophila spp. collected in European countries as well as the United States and Oceania (Chandler et al., 2012; Solomon et al., 2019). As for the bacteria, species belonging to the genera Pantoea, Lactobacillus, Leuconostoc, and Acetobacter have also previously been detected in wild Drosophila spp. (Chandler et al., 2011). These elucidations will be incorporated into our revised manuscript.

Nevertheless, the term “core” in the manuscript title may lead to misunderstanding, as the generality does not ensure the ubiquitous presence of these microbial species in every individual fly. Considering this point, we will replace the term with an expression more appropriate to our context.

2) Can the authors clearly demonstrate that the microbiota species that develop in the banana trap are derived from flies? Are these species found in flies in the wild? Did the authors check that the flies belong to the D. melanogaster species and not to the sister group D. simulans?

Can the authors clearly demonstrate that the microbiota species that develop in the banana trap are derived from flies? Are these species found in flies in the wild?

The reviewer asked whether the microbial species identified in the fermented banana samples were derived from flies. To address this question, additional experiments under more controlled conditions, such as the inoculation of specific species of wild flies onto fresh bananas, would be needed. Nevertheless, the microbes may potentially originate from wild flies, as supported by the literature cited in our response to the Weakness 1).

Alternative sources for microbial provenance also merit consideration. For example, microbial entities may be inherently present in unfermented bananas through the infiltration of peel injuries (lines 1141-1142 of the original manuscript). In addition, they could be introduced by insects other than flies, given that both rove beetles (Staphylinidae) and sap beetles (Nitidulidae) were observed in some of the traps. These possibilities will be incorporated into the 'MATERIALS AND METHODS' and 'DISCUSSION' sections of our revised manuscript.

Did the authors check that the flies belong to the D. melanogaster species and not to the sister group D. simulans?

Our sampling strategy was designed to target not only D. melanogaster but also other domestic Drosophila species, such as D. simulans, that inhabit human residential areas. After adult flies were caught in each trap, we identified the species as shown in Table S1, thereby showing the presence of either or both D. melanogaster and D. simulans. We will provide these descriptions in MATERIALS AND METHODS and DISCUSSION.

3) Did the microarrays highlight a change in immune genes (ex. antibacterial peptide genes)? Whatever the answer, this would be worth mentioning. The authors described their microarray data in terms of fed/starved in relation to the Finke article. They should clarify if they observed significant differences between species (differences between species within bacteria or fungi, and more generally differences between bacteria versus fungi).

Did the microarrays highlight a change in immune genes (ex. antibacterial peptide genes)? Whatever the answer, this would be worth mentioning.

Regarding the antimicrobial peptide genes, statistical comparisons of our RNA-seq data across different conditions were impracticable because most of them showed low expression levels (refer to Author response table 1, which exhibits the RNA-seq data of the yeast-fed larvae; similar expression profiles were observed in the bacteria-fed larvae). While a subset of genes exhibited significantly elevated expression in the non-supportive conditions relative to the supportive ones, this can be due to intra-sample variability rather than due to distinct nutritional environments. Therefore, it would be difficult to discuss a change in immune genes in the paper. Additionally, the previous study that conducted larval microarray analysis (Zinke et al., 2002) did not explicitly focus on immune genes.

Author response table 1.

Antimicrobial peptide genes are not up-regulated by any of the microbes. Antimicrobial peptides gene expression profiles of whole bodies of first-instar larvae fed on yeasts. TPM values of all samples and comparison results of gene expression levels in the larvae fed on supportive and non-supportive yeasts are shown. Antibacterial peptide genes mentioned in Hanson and Lemaitre, 2020 are listed. NA or na, not available.

They should clarify if they observed significant differences between species (differences between species within bacteria or fungi, and more generally differences between bacteria versus fungi).

We did not observe significant differences between species within bacteria or fungi, or between bacteria and fungi. For example, the gene expression profiles of larvae fed on the various supporting microbes showed striking similarities to each other, as evidenced by the heat map showing the expression of all genes detected in larvae fed either yeast or bacteria (Author response image 1). Similarities were also observed among larvae fed on distinct non-supporting microbes.

Author response image 1.

Gene expression profiles of larvae fed on the various supporting microbes show striking similarities to each other. Heat map showing the gene expression of the first-instar larvae that fed on yeasts or bacteria. Freshly hatched germ-free larvae were placed on banana agar inoculated with each microbe and collected after 15 h feeding to examine gene expression of the whole body. Note that data presented in Figures 3A and 4C in the original manuscript, which are obtained independently, are combined to generate this heat map. The labels under the heat map indicate the microbial species fed to the larvae, with three samples analyzed for each condition. The lactic acid bacteria (“LAB”) include Lactiplantibacillus plantarum and Leuconostoc mesenteroides, while the lactic acid bacterium (“AAB”) represents Acetobacter orientalis. “LAB + AAB” signifies mixtures of the AAB and either one of the LAB species. The asterisk in the label highlights a sample in a “LAB” condition (Leuconostoc mesenteroides), which clustered separately from the other “LAB” samples. Brown abbreviations of scientific names are for the yeast-fed conditions. H. uva, Hanseniaspora uvarum; K. hum, Kazachstania humilis; M. asi, Martiniozyma asiatica; S. cra, Saccharomycopsis crataegensis; P. klu, Pichia kluyveri; S. bac, Starmerella bacillaris; S. cer, S. cerevisiae BY4741 strain.

Only a handful of genes showed different expression patterns between larvae fed on yeast and those fed on bacteria, without any enrichment for specialized gene functions. Thus, it is challenging to discuss the potential differential impacts, if any, of yeast and bacteria on larval growth.

4) The whole paper - and this is one of its merits - points to a role of the Drosophila larval microbiota in processing the fly food. Are these bacterial and fungal species found in the gut of larvae/adults? Are these species capable of establishing a niche in the cardia of adults as shown recently in the Ludington lab (Dodge et al.,)? Previous studies have suggested that microbiota members stimulate the Imd pathway leading to an increase in digestive proteases (Erkosar/Leulier). Are the microbiota species studied here affecting gut signaling pathways beyond providing branched amino acids?

The whole paper - and this is one of its merits - points to a role of the Drosophila larval microbiota in processing the fly food. Are these bacterial and fungal species found in the gut of larvae/adults? Are these species capable of establishing a niche in the cardia of adults as shown recently in the Ludington lab (Dodge et al.,)?

Although we did not investigate the microbiota in the gut of either larvae or adults, we did compare the microbiota within surface-sterilized larvae or adults with those in food samples. We found that adult flies and early-stage food sources, as well as larvae and late-stage food sources, harbor similar microbial species (Figure 1F). Additionally, previous examinations of the gut microbiota in wild adult flies have identified microbial species or taxa congruent with those we isolated from our foods (Chandler et al., 2011; Chandler et al., 2012). We have elaborated on this in our response to Weakness 1).

While we did not investigate whether these species are capable of establishing a niche in the cardia of adults, we will cite the study by Dodge et al., 2023 in our revised manuscript and discuss the possibility that predominant microbes in adult flies may show a propensity for colonization.

Previous studies have suggested that microbiota members stimulate the Imd pathway leading to an increase in digestive proteases (Erkosar/Leulier). Are the microbiota species studied here affecting gut signaling pathways beyond providing branched amino acids?

The reviewer inquires whether the supportive microbes in our study stimulate gut Imd signaling pathways and induce the expression of digestive protease genes, as demonstrated in a previous study (Erkosar et al., 2015). According to our RNA-seq data, it seems unlikely that the supportive microbes stimulate the signaling pathway. Figures contained in Author response image 2 provide the statistical comparisons of expression levels for seven protease genes between the supportive and the non-supportive conditions. These genes did not exhibit a consistent upregulation in the presence of the supportive microbes (H. uva or K. hum in Author response image 2A; Le mes + A. ori in Author response image 2B). Rather, they exhibited a tendency to be upregulated under the non-supportive microbes (St. bac or Pi. klu in Author response image 2A; La. pla in Author response image 2B).

Author response image 2.

Most of the peptidase genes reported by Erkosar et al., 2015 are more highly expressed under the non-supportive conditions than the supportive conditions. Comparison of the expression levels of seven peptidase genes derived from the RNA-seq analysis of yeast-fed (A) or bacteria-fed (B) first-instar larvae. A previous report demonstrated that the expression of these genes is upregulated upon association with a strain of Lactiplantibacillus plantarum, and that the PGRP-LE/Imd/Relish signaling pathway, at least partially, mediates the induction (Erkosar et al., 2015). H. uva, Hanseniaspora uvarum; K. hum, Kazachstania humilis; P. klu, Pichia kluyveri; S. bac, Starmerella bacillaris; La. pla, Lactiplantibacillus plantarum; Le. mes, Leuconostoc mesenteroides; A. ori, Acetobacter orientalis; ns, not significant.

Reviewer #2 (Public Review):

Weaknesses:

The experimental setting that, the authors think, reflects host-microbe interactions in nature is one of the key points. However, it is not explicitly mentioned whether isolated microbes are indeed colonized in wild larvae of Drosophila melanogaster who eat bananas. Another matter is that this work is rather descriptive and a few mechanical insights are presented. The evidence that the nutritional role of BCAAs is incomplete, and molecular level explanation is missing in "interspecies interactions" between lactic acid bacteria (or yeast) and acetic acid bacteria that assure their inhabitation. Apart from these matters, the future directions or significance of this work could be discussed more in the manuscript.

The experimental setting that, the authors think, reflects host-microbe interactions in nature is one of the key points. However, it is not explicitly mentioned whether isolated microbes are indeed colonized in wild larvae of Drosophila melanogaster who eat bananas.

The reviewer asks whether the isolated microbes were colonized in the larval gut. Previous studies on microbial colonization associated with Drosophila have predominantly focused on adults (Pais et al. PLOS Biology, 2018), rather than larval stages. Developing larvae continually consume substrates which are already subjected to microbial fermentation and abundant in live microbes until the end of the feeding larval stage. Therefore, we consider it difficult to discuss microbial colonization in the larval gut. We will add this point in the DISCUSSION of the revised manuscript.

Another matter is that this work is rather descriptive and a few mechanical insights are presented. The evidence that the nutritional role of BCAAs is incomplete, and molecular level explanation is missing in "interspecies interactions" between lactic acid bacteria (or yeast) and acetic acid bacteria that assure their inhabitation.

While recognizing the importance of comprehensive mechanistic analysis, this study includes all experimentally feasible data. Elucidation of more detailed molecular mechanisms lies beyond the scope of this study and will be the subject of future research.

Regarding the nutritional role of BCAAs, the incorporation of BCAAs enabled larvae fed with the non-supportive yeast to grow to the second instar. This observation suggests that consumption of BCAAs upregulates diverse genes involved in cellular growth processes in larvae. We have discussed the hypothetical interaction between lactic acid bacteria (LAB) and acetic acid bacteria (AAB) in the manuscript (lines 402-405): LAB may facilitate lactate provision to AAB, consequently enhancing the biosynthesis of essential nutrients such as amino acids. To test this hypothesis, future experiments will include the supplementation of lactic acid to AAB culture plates and the co-inoculating LAB mutant strains defective in lactate production with AABs, to assess both larval growth and continuous larval association with AABs. With respect to AAB-yeast interactions, metabolites released from yeast cells might benefit AAB growth, and this possibility will be investigated through the supplementation of AAB culture plates with candidate metabolites identified in the cell suspension supernatants of the late-stage yeasts.

Apart from these matters, the future directions or significance of this work could be discussed more in the manuscript.

We appreciate the reviewer's recommendations and will include additional descriptions regarding these aspects in the DISCUSSION section.

Reviewer #3 (Public Review):

Weaknesses:

Despite describing important findings, I believe that a more thorough explanation of the experimental setup and the steps expected to occur in the exposed diet over time, starting with natural "inoculation" could help the reader, in particular the non-specialist, grasp the rationale and main findings of the manuscript. When exactly was the decision to collect early-stage samples made? Was it when embryos were detected in some of the samples? What are the implications of bacterial presence in the no-fly traps? These samples also harbored complex microbial communities, as revealed by sequencing. Were these samples colonized by microbes deposited with air currents? Were they the result of flies that touched the material but did not lay eggs? Could the traps have been visited by other insects? Another interesting observation that could be better discussed is the fact that adult flies showed a microbiome that more closely resembles that of the early-stage diet, whereas larvae have a more late-stage-like microbiome. It is easy to understand why the microbiome of the larvae would resemble that of the late-stage foods, but what about the adult microbiome? Authors should discuss or at least acknowledge the fact that there must be a microbiome shift once adults leave their food source. Lastly, the authors should provide more details about the metabolomics experiments. For instance, how were peaks assigned to leucine/isoleucine (as well as other compounds)? Were both retention times and MS2 spectra always used? Were standard curves produced? Were internal, deuterated controls used?

When exactly was the decision to collect early-stage samples made? Was it when embryos were detected in some of the samples?

We collected traps and early-stage samples 2.5 days after setting up the traps. This time frame was determined by pilot experiments. A shorter collection time resulted in a greater likelihood of obtaining no-fly traps, whereas a longer collection time caused larval overcrowding, as well as adults’ deaths from drowning in the liquid seeping out of fruits. These procedural details will be delineated in the MATERIALS AND METHODS section of the revised manuscript.

What are the implications of bacterial presence in the no-fly traps? These samples also harbored complex microbial communities, as revealed by sequencing. Were these samples colonized by microbes deposited with air currents? Were they the result of flies that touched the material but did not lay eggs? Could the traps have been visited by other insects?

We assume that the origins of the microbes detected in the no-fly trap foods vary depending on the species. For instance, Colletotrichum musae, the fungus that causes banana anthracnose, may have been present in fresh bananas before trap placement. The filamentous fungi could have originated from airborne spores, but they could also have been introduced by insects that feed on these fungi. We will include these possibilities in the DISCUSSION section of the revised manuscript.

Another interesting observation that could be better discussed is the fact that adult flies showed a microbiome that more closely resembles that of the early-stage diet, whereas larvae have a more late-stage-like microbiome. It is easy to understand why the microbiome of the larvae would resemble that of the late-stage foods, but what about the adult microbiome? Authors should discuss or at least acknowledge the fact that there must be a microbiome shift once adults leave their food source.

We are grateful for the reviewer's insightful suggestions regarding shifts in the adult microbiome. We plan to include in the DISCUSSION section of the revised manuscript the possibility that the microbial composition may change substantially during pupal stages and that microbes obtained after eclosion could potentially form the adult gut microbiota.

Lastly, the authors should provide more details about the metabolomics experiments. For instance, how were peaks assigned to leucine/isoleucine (as well as other compounds)? Were both retention times and MS2 spectra always used? Were standard curves produced? Were internal, deuterated controls used?

We appreciate the reviewer's advice. Detailed methods of the metabolomic experiments will be included in our revised manuscript.

Author Response

We would like to thank the editors and reviewers for their thoughtful comments on our manuscript. Before we can provide a point-by-point response and submit a revised version of the manuscript we would like to provisionally address and alleviate some of their main concerns.

A concern was expressed in the ‘eLife assessment’ and by two of the reviewers that a potential confound between the coding of sensory information and behavior outcome by IC neurons might have been introduced by combining data across different sound levels, which could challenge the conclusions of the study. In addressing this we have carried out the analysis (i.e. averaging the neural activity separately for different sound levels) suggested for distinguishing between the two alternative explanations offered by reviewer #1: That the difference in neural activity between hit and miss trials reflects a) behavior or b) sound level (more precisely: differences in response magnitude arising from a higher proportion of highsound-level trials in the hit trial group than in the miss trial group). If the data favored b), we would expect no difference in activity between hit and miss trials when plotted separately for different sound levels. The figure in Author response image 1 indicates that that is not the case. Hit and miss trial activity are clearly distinct even when plotted separately for different sound levels, confirming that this difference in activity reflects the animals’ behavior rather than sensory information.

Author response image 1.

A related concern was expressed with regards to the decoding analysis. Namely, that differences in the distributions of sound levels in the different trial types could confound the decoding into hit and miss trials and that, consequently, the results of the decoding analysis merely reflect differences in the processing of sound level. Our analysis actually aimed to take this into account but, unfortunately, we failed to include sufficient details in the methods section of the submitted manuscript. Rather than including all the trials in a given session, only trials of intermediate difficulty were used for the decoding analysis. More specifically, we only included trials across five sound levels, comprising the lowest sound level that exceeded a d prime of 1.5 plus the two sound levels below and above that level. That ensured that differences in sound level distributions would be small, while still giving us a sufficient number of trials to perform the decoding analysis. In this context, it is worth bearing in mind that a) the decoding analysis was done on a frame-by-frame basis, meaning that the decoding score achieved early in the trial has no impact on the decoding score at later time points in the trial, b) sound-driven activity can be observed predominantly immediately after stimulus onset and is largely over about 1 s into the trial (see cluster 3, for instance, or average miss trial activity in the plots above), c) decoding performance of the behavioral outcome starts to plateau 5001000 ms into the trial and remains high until it very gradually begins to decline after about 2 s into the trial. In other words, decoding performance remains high far longer than the stimulus would be expected to have an impact on the neurons’ activity. Therefore, we would expect any residual bias due to differences in the sound level distribution that our approach did not control for to be restricted to the very beginning of the trial and not to meaningfully impact the conclusions derived from the decoding analysis.

Another concern expressed in the reviews is that, in relation to the cluster-wise analysis of neural activity, no direct comparison (beyond the pie charts of Figure 5C) was provided between data from lesioned and non-lesioned groups, leaving unclear how similar taskrelevant activity is between these groups. In Author response image 2 we plot, analogous to Figure 5B, the average hit and miss trial activity for the 10 clusters separately for lesioned and non-lesioned mice, illustrating more clearly the high degree of similarity between the two groups.

Author response image 2.

Author response:

Reviewer #1 (Public review):

(1) Some details are not described for experimental procedures. For example, what were the pharmacological drugs dissolved in, and what vehicle control was used in experiments? How long were pharmacological drugs added to cells?

We apologise for the oversight. These details have now been added to the methods section of the manuscript as well as to the relevant figure legends.

Briefly, latrunculin was used at a final concentration of 250 nM and Y27632 at a final concentration of 50 μM. Both drugs were dissolved in DMSO. The vehicle controls were effected with the highest final concentration of DMSO of the two drugs.

The details of the drug treatments and their duration was added to the methods and to figures 6, S10, and S12.

(2) Details are missing from the Methods section and Figure captions about the number of biological and technical replicates performed for experiments. Figure 1C states the data are from 12 beads on 7 cells. Are those same 12 beads used in Figure 2C? If so, that information is missing from the Figure 2C caption. Similarly, this information should be provided in every figure caption so the reader can assess the rigor of the experiments. Furthermore, how heterogenous would the bead displacements be across different cells? The low number of beads and cells assessed makes this information difficult to determine.

We apologise for the oversight. We have now added this data to the relevant figure panels.

To gain a further understanding of the heterogeneity of bead displacements across cells, we have replotted the relevant graphs using different colours to indicate different cells. This reveals that different cells appear to behave similarly and that the behaviour appears controlled by distance to the indentation or the pipette tip rather than cell identity.

We agree with the reviewer that the number of cells examined is low. This is due to the challenging nature of the experiments that signifies that many attempts are necessary to obtain a successful measurement.

The experiments in Fig 1C are a verification of a behaviour documented in a previous publication [1]. Here, we just confirm the same behaviour and therefore we decided that only a small number of cells was needed.

The experiments in Fig 2C (that allow for a direct estimation of the cytoplasm’s hydraulic permeability) require formation of a tight seal between the glass micropipette and the cell, something known as a gigaseal in electrophysiology. The success rate of this first step is 10-30% of attempts for an experienced experimenter. The second step is forming a whole cell configuration, in which a hydraulic link is formed between the cell and the micropipette. This step has a success rate of ~ 50%. Whole cell links are very sensitive to any disturbance. After reaching the whole cell configuration, we applied relatively high pressures that occasionally resulted in loss of link between the cell and the micropipette. In summary, for the 12 successful measurements, hundreds of unsuccessful attempts were carried out.

(3) The full equation for displacement vs. time for a poroelastic material is not provided. Scaling laws are shown, but the full equation derived from the stress response of an elastic solid and viscous fluid is not shown or described.

We thank the reviewer for this comment. Based on our experiments, we found that the cytoplasm behaves as a poroelastic material. However, to understand the displacements of the cell surface in response to localised indentation, we show that we also need to take the tension of the sub membranous cortex into account. In summary, the interplay between cell surface tension generated by the cortex and the poroelastic cytoplasm controls the cell behaviour. To our knowledge, no simple analytical solutions to this type of problem exist.

In Fig 1, we show that the response of the cell to local indentation is biphasic with a short time-scale displacement followed by a longer time-scale one. In Figs 2 and 3, we directly characterise the kinetics of cell surface displacement in response to microinjection of fluid. These kinetics are consistent with the long time-scale displacement but not the short time-scale one. Scaling considerations led us to propose that tension in the cortex may play a role in mediating the short time-scale displacement. To verify this hypothesis, we have now added new data showing that the length-scale of an indentation created by an AFM probe depends on tension in the cortex (Fig S5).

In a previous publication [2], we derived the temporal dynamics of cell surface displacement for a homogenous poroelastic material in response to a change in osmolarity. In the current manuscript, the composite nature of the cell (membrane, cortex, cytoplasm) needs to be taken into account as well as a realistic cell shape. Therefore, we did not attempt to provide an analytical solution for the displacement of the cell surface versus time in the current work. Instead, we turned to finite element modelling to show that our observations are qualitatively consistent with a cell that comprises a tensed sub membranous actin cortex and a poroelastic cytoplasm (Fig 4). We have now added text to make this clearer for the reader.

Reviewer #2 (Public review):

Comments & Questions:

The authors state, "Next, we sought to quantitatively understand how the global cellular response to local indentation might arise from cellular poroelasticity." However, the evidence presented in the following paragraph appears more qualitative than strictly quantitative. For instance, the length scale estimate of ~7 μm is only qualitatively consistent with the observed ~10 μm, and the timescale 𝜏𝑧 ≈ 500 ms is similarly described as "qualitatively consistent" with experimental observations. Strengthening this point would benefit from more direct evidence linking the short timescale to cell surface tension. Have you tried perturbing surface tension and examining its impact on this short-timescale relaxation by modulating acto-myosin contractility with Y-27632, depolymerizing actin with Latrunculin, or applying hypo/hyperosmotic shocks?

Upon rereading our manuscript, we agree with the reviewer that some of our statements are too strong. We have now moderated these and clarified the goal of that section of the text.

The reviewer asks if we have examined the effect of various perturbations on the short time-scale displacements. In our experimental conditions, we cannot precisely measure the time-scale of the fast relaxation because its duration is comparable to the frame rate of our image acquisition. However, we examined the amplitude of the displacement of the first phase in response to sucrose treatment and we have carried out new experiments in which we treat cells with 250nM Latrunculin to partially depolymerise cellular F-actin. Neither of these treatments had an impact on the amplitude of vertical displacements (Author response image 1).

The absence of change in response to Latrunculin may be because the treatment decreases both the elasticity of the cytoplasm E and the cortical tension γ. As the length-scale l of the deformation of the surface scales as , the two effects of latrunculin treatment may therefore compensate one another and result in only small changes in l. We have now added this data to supplementary information and comment on this in the text.

Author response image 1:

Amplitude of the short time-scale displacements of beads in response to AFM indentation at δx=0µm for control cells, sucrose treated cells, and cells treated with Latrunculin B. n indicates the number of cells examined and N the number of beads.

The reviewer’s comment also made us want to determine how cortical tension affects the length-scale of the cell surface deformation created by localised micro indentation. To isolate the role of the cortex from that of cell shape, we decided to examine rounded mitotic cells. In our experiments, we indented a mitotic cell expressing a membrane targeted GFP with a sharp AFM tip (Author response image 2).

In our experiments, we adjusted force to generate a 2μm depth indentation and we imaged the cell profile with confocal microscopy before and during indentation. Segmentation of this data allowed us to determine the cell surface displacement resulting from indentation and measure a length scale of deformation. In control conditions, the length scale created by deformation is on the order of 1.2μm. When we inhibited myosin contractility with blebbistatin, the length-scale of deformation decreased significantly to 0.8 μm, as expected if we decrease the surface tension γ without affecting the cytoplasmic elasticity. We have now added this data to our manuscript.

Author response image 2.

(a) Overlay of the zx profiles of a mitotic cell before (green) and during indentation (red). The cell membrane is labelled with CellMask DeepRed. The arrowhead indicates the position of the AFM tip. Scale bar 10µm. (b) Position of the membrane along the top half of the cell before (green) and during (red) indentation. The membrane position is derived from segmentation of the data in (a). Deformation is highly localised and membrane profiles overlap at the edges. The tip position is marked by an *. (c) The difference in membrane height between pre-indentation and indentation profiles plotted in (b) with the tip located at x=0. (d) Schematic of the cell surface profile during indentation and the corresponding length scale of the deformation induced by indentation. (e) Measured length scale for an indentation ~2µm for DMSO control l=1.2±0.2µm (n=8 cells) and with blebbistatin treatment (100µM) l=0.8±0.4µm (n=9 cells) (p= 0.016

The authors demonstrate that the second relaxation timescale increases (Figure 1, Panel D) following a hyperosmotic shock, consistent with cytoplasmic matrix shrinkage, increased friction, and consequently a longer relaxation timescale. While this result aligns with expectations, is a seven-fold increase in the relaxation timescale realistic based on quantitative estimates given the extent of volume loss?

We thank the reviewer for this interesting question. Upon re-examining our data, we realised that the numerical values in the text related to the average rather than the median of our measurements. The median of the poroelastic time constant increases from ~0.4s in control conditions to 1.4s in sucrose, representing approximately a 3.5-fold increase.

Previous work showed that HeLa cell volume decreases by ~40% in response to hyperosmotic shock [3]. The fluid volume fraction in cells is ~65-75%. If we assume that the water is contained in N pores of volume , we can express the cell volume as with V_s the volume of the solid fraction. We can rewrite with ϕ = 0.42 -0.6. As V_s does not change in response to osmotic shock, we can rewrite the volume change to obtain the change in pore size .

The poroelastic diffusion constant scales as and the poroelastic timescale scales as . Therefore, the measured change in volume leads to a predicted increase in poroelastic diffusion time of 1.7-1.9-fold, smaller than observed in our experiments. This suggests that some intuition can be gained in a straightforward manner assuming that the cytoplasm is a homogenous porous material.

However, the reality is more complex and the hydraulic pore size is distinct from the entanglement length of the cytoskeleton mesh, as we discussed in a previous publication [4]. When the fluid fraction becomes sufficiently small, macromolecular crowding will impact diffusion further and non-linearities will arise. We have now added some of these considerations to the discussion.

If the authors' hypothesis is correct, an essential physiological parameter for the cytoplasm could be the permeability k and how it is modulated by perturbations, such as volume loss or gain. Have you explored whether the data supports the expected square dependency of permeability on hydraulic pore size, as predicted by simple homogeneity assumptions?

We thank the reviewer for this comment. As discussed above, we have explored such considerations in a previous publication (see discussion in [4]). Briefly, we find that the entanglement length of the F-actin cytoskeleton does play a role in controlling the hydraulic pore size but is distinct from it. Membrane bounded organelles could also contribute to setting the pore size. In our previous publication, we derived a scaling relationship that indicates that four different length-scales contribute to setting cellular rheology: the average filament bundle length, the size distribution of particles in the cytosol, the entanglement length of the cytoskeleton, and the hydraulic pore size. Many of these length-scales can be dynamically controlled by the cell, which gives rise to complex rheology. We have now added these considerations to our discussion.

Additionally, do you think that the observed decrease in k in mitotic cells compared to interphase cells is significant? I would have expected the opposite naively as mitotic cells tend to swell by 10-20 percent due to the mitotic overshoot at mitotic entry (see Son Journal of Cell Biology 2015 or Zlotek Journal of Cell Biology 2015).

We thank the reviewer for this interesting question. Based on the same scaling arguments as above, we would expect that a 10-20% increase in cell volume would give rise to 10-20% increase in diffusion constant. However, we also note that metaphase leads to a dramatic reorganisation of the cell interior and in particular membrane-bounded organelles. In summary, we do not know why such a decrease could take place. We now highlight this as an interesting question for further research.

Based on your results, can you estimate the pore size of the poroelastic cytoplasmic matrix? Is this estimate realistic? I wonder whether this pore size might define a threshold above which the diffusion of freely diffusing species is significantly reduced. Is your estimate consistent with nanobead diffusion experiments reported in the literature? Do you have any insights into the polymer structures that define this pore size? For example, have you investigated whether depolymerizing actin or other cytoskeletal components significantly alters the relaxation timescale?

We thank the reviewer for this comment. We cannot directly estimate the hydraulic pore size from the measurements performed in the manuscript. Indeed, while we understand the general scaling laws, the pre-factors of such relationships are unknown.

We carried out experiments aiming at estimating the hydraulic pore size in previous publications [3,4] and others have shown spatial heterogeneity of the cytoplasmic pore size [5]. In our previous experiments, we examined the diffusion of PEGylated quantum dots (14nm in hydrodynamic radius). In isosmotic conditions, these diffused freely through the cell but when the cell volume was decreased by a hyperosmotic shock, they no longer moved [3,4]. This gave an estimate of the pore radius of ~15nm.

Previous work has suggested that F-actin plays a role in dictating this pore size but microtubules and intermediate filaments do not [4].

There are no quantifications in Figure 6, nor is there a direct comparison with the model. Based on your model, would you expect the velocity of bleb growth to vary depending on the distance of the bleb from the pipette due to the local depressurization? Specifically, do blebs closer to the pipette grow more slowly?

We apologise for the oversight. The quantifications are presented in Fig S10 and Fig S12. We have now modified the figure legends accordingly.

Blebs are very heterogenous in size and growth velocity within a cell and across cells in the population in normal conditions [6]. Other work has shown that bleb size is controlled by a competition between pressure driving growth and actin polymerisation arresting it[7]. Therefore, we did not attempt to determine the impact of depressurisation on bleb growth velocity or size.

In experiments in which we suddenly increased pressure in blebbing cells, we did notice a change in the rate of growth of blebs that occurred after we increased pressure (Author response image 3). However, the experiments are technically challenging and we decided not to perform more.

Author response image 3:

A. A hydraulic link is established between a blebbing cell and a pipette. At time t>0, a step increase in pressure is applied. B. Kymograph of bleb growth in a control cell (top) an in a cell subjected to a pressure increase at t=0s (bottom). Top: In control blebs, the rate of growth is slow and approximately constant over time. The black arrow shows the start of blebbing. Bottom: The black arrow shows the start of blebbing. The dashed line shows the timing of pressure application and the red arrow shows the increase in growth rate of the bleb when the pressure increase reaches the bleb. This occurs with a delay δt.

I find it interesting that during depressurization of the interphase cells, there is no observed volume change, whereas in pressurization of metaphase cells, there is a volume increase. I assume this might be a matter of timescale, as the microinjection experiments occur on short timescales, not allowing sufficient time for water to escape the cell. Do you observe the radius of the metaphase cells decreasing later on? This relaxation could potentially be used to characterize the permeability of the cell surface.

We thank the reviewer for this comment.

First, we would like to clarify that both metaphase and interphase cells increase their volume in response to microinjection. The effect is easier to quantify in metaphase cells because we assume spherical symmetry and just monitor the evolution of the radius (Fig 3). However, the displacement of the beads in interphase cells (Fig 2) clearly shows that the cell volume increases in response to microinjection. For both interphase and metaphase cells, when the injection is prolonged, the membrane eventually detaches from the cortex and large blebs form until cell lysis. In contrast to the reviewer’s intuition, we never observe a relaxation in cell volume, probably because we inject fluid faster than the cell can compensate volume change through regulatory mechanisms involving ion channels.

When we depressurise metaphase cells, we do not observe any change in volume (Fig S10). This contrasts with the increase that we observe upon pressurisation. The main difference between these two experiments is the pressure differential. During depressurisation experiments, this is the hydraulic pressure within the cell ~500Pa (Fig 6A); whereas during pressurisation experiments, this is the pressure in the micropipette, ranging from 1.4-10 kPa (Fig 3). We note in particular that, when we used the lowest pressures in our experiments, the increase in volume was very slow (see Fig 3C). Therefore, we agree with the reviewer that it is likely the magnitude of the pressure differential that explains these differences.

I am curious about the saturation of the time lag at 30 microns from the pipette in Figure 4, Panel E for the model's prediction. A saturation which is not clearly observed in the experimental data. Could you comment on the origin of this saturation and the observed discrepancy with the experiments (Figure E panel 2)? Naively, I would have expected the time lag to scale quadratically with the distance from the pipette, as predicted by a poroelastic model and the diffusion of displacement. It seems weird to me that the beads start to move together at some distance from the pipette or else I would expect that they just stop moving. What model parameters influence this saturation? Does membrane permeability contribute to this saturation?

We thank the reviewer for pointing this out. In our opinion, the saturation occurring at 30 microns arises from the geometry of the model. At the largest distance away from the micropipette, the cortex becomes dominant in the mechanical response of the cell because it represents an increasing proportion of the cellular material.

To test this hypothesis, we will rerun our finite element models with a range of cell sizes. This will be added to the manuscript at a later date.

Reviewer #3 (Public review):

Weaknesses: I have two broad critical comments:

(1) I sense that the authors are correct that the best explanation of their results is the passive poroelastic model. Yet, to be thorough, they have to try to explain the experiments with other models and show why their explanation is parsimonious. For example, one potential explanation could be some mechanosensitive mechanism that does not involve cytoplasmic flow; another could be viscoelastic cytoskeletal mesh, again not involving poroelasticity. I can imagine more possibilities. Basically, be more thorough in the critical evaluation of your results. Besides, discuss the potential effect of significant heterogeneity of the cell.

We thank the reviewer for these comments and we agree with their general premise.

Some observations could qualitatively be explained in other ways. For example, if we considered the cell as a viscoelastic material, we could define a time constant with η the viscosity and E the elasticity of the material. The increase in relaxation time with sucrose treatment could then be explained by an increase in viscosity. However, work by others has previously shown that, in the exact same conditions as our experiment, viscoelasticity cannot account for the observations[1]. In its discussion, this study proposed poroelasticity as an alternative mechanism but did not investigate that possibility. This was consistent with our work that showed that the cytoplasm behaves as a poroelastic material and not as a viscoelastic material [4]. Therefore, we decided not to consider viscoelasticity as possibility. We now explain this reasoning better and have added a sentence about a potential role for mechanotransductory processes in the discussion.

(2) The study is rich in biophysics but a bit light on chemical/genetic perturbations. It could be good to use low levels of chemical inhibitors for, for example, Arp2/3, PI3K, myosin etc, and see the effect and try to interpret it. Another interesting question - how adhesive strength affects the results. A different interesting avenue - one can perturb aquaporins. Etc. At least one perturbation experiment would be good.

We agree with the reviewer. In our previous studies, we already examined what biological structures affect the poroelastic properties of cells [2,4]. Therefore, the most interesting aspect to examine in our current work would be perturbations to the phenomenon described in Fig 6G and, in particular, to investigate what volume regulation mechanisms enable sustained intracellular pressure gradients. However, these experiments are particularly challenging and with very low throughput. Therefore, we feel that these are out of the scope of the present report and we mention these as promising future directions.

References:

(1) Rosenbluth, M. J., Crow, A., Shaevitz, J. W. & Fletcher, D. A. Slow stress propagation in adherent cells. Biophys J 95, 6052-6059 (2008). https://doi.org/10.1529/biophysj.108.139139

(2) Esteki, M. H. et al. Poroelastic osmoregulation of living cell volume. iScience 24, 103482 (2021). https://doi.org/10.1016/j.isci.2021.103482

(3) Charras, G. T., Mitchison, T. J. & Mahadevan, L. Animal cell hydraulics. J Cell Sci 122, 3233-3241 (2009). https://doi.org/10.1242/jcs.049262

(4) Moeendarbary, E. et al. The cytoplasm of living cells behaves as a poroelastic material. Nat Mater 12, 253-261 (2013). https://doi.org/10.1038/nmat3517

(5) Luby-Phelps, K., Castle, P. E., Taylor, D. L. & Lanni, F. Hindered diffusion of inert tracer particles in the cytoplasm of mouse 3T3 cells. Proc Natl Acad Sci U S A 84, 4910-4913 (1987). https://doi.org/10.1073/pnas.84.14.4910

(6) Charras, G. T., Coughlin, M., Mitchison, T. J. & Mahadevan, L. Life and times of a cellular bleb. Biophys J 94, 1836-1853 (2008). https://doi.org/10.1529/biophysj.107.113605

(7) Tinevez, J. Y. et al. Role of cortical tension in bleb growth. Proc Natl Acad Sci U S A 106, 18581-18586 (2009). https://doi.org/10.1073/pnas.0903353106

Author Response

eLife assessment

This potentially valuable study uses classic neuroanatomical techniques and synchrotron X-ray tomography to investigate the mapping of the trunk within the brainstem nuclei of the elephant brain. Given its unique specializations, understanding the somatosensory projections from the elephant trunk would be of general interest to evolutionary neurobiologists, comparative neuroscientists, and animal behavior scientists. However, the anatomical analysis is inadequate to support the authors' conclusion that they have identified the elephant trigeminal sensory nuclei rather than a different brain region, specifically the inferior olive.

Comment: We are happy that our paper is considered to be potentially valuable. Also, the editors highlight the potential interest of our work for evolutionary neurobiologists, comparative neuroscientists, and animal behavior scientists. The editors are more negative when it comes to our evidence on the identification of the trigeminal nucleus vs the inferior olive. We have five comments on this assessment. (i) We think this assessment is heavily biased by the comments of referee 2. We will show that the referee’s comments are more about us than about our paper. Hence, the referee failed to do their job (refereeing our paper) and should not have succeeded in leveling our paper. (ii) We have no ad hoc knock-out experiments to distinguish the trigeminal nucleus vs the inferior olive. Such experiments (extracellular recording & electrolytic lesions, viral tracing would be done in a week in mice, but they cannot and should not be done in elephants. (iii) We have extraordinary evidence. Nobody has ever described a similarly astonishing match of body (trunk folds) and myeloarchitecture in the trigeminal system before. (iv) We will show that our assignment of the trigeminal nucleus vs the inferior olive is more plausible than the current hypothesis about the assignment of the trigeminal nucleus vs the inferior olive as defended by referee 2. We think this is why it is important to publish our paper. (v) We think eLife is the perfect place for our publication because the deviating views of referee 2 are published along.

Change: We performed additional peripherin-antibody staining to differentiate the inferior olive and trigeminal nucleus. Peripherin is a cytoskeletal protein that is found in peripheral nerves and climbing fibers. Specifically, climbing fibers of various species (mouse, rabbit, pig, cow, and human; Errante et al., 1998) are stained intensely with peripherin-antibodies. What is tricky for our purposes is that there is also some peripherin-antibody reactivity in the trigeminal nuclei (Errante et al., 1998). Such peripherin-antibody reactivity is weaker, however, and lacks the distinct axonal bundle signature that stems from the strong climbing fiber peripherin-reactivity as seen in the inferior olive (Errante et al., 1998). As can be seen in Author response image 1, we observe peripherin-reactivity in axonal bundles (i.e. in putative climbing fibers), in what we think is the inferior olive. We also observe weak peripherin-reactivity, in what we think is the trigeminal nucleus, but not the distinct and strong labeling of axonal bundles. These observations are in line with our ideas but are difficult to reconcile with the views of the referee. Specifically, the lack of peripherin-reactive axon bundles suggests that there are no climbing fibres in what the referee thinks is the inferior olive.

Errante, L., Tang, D., Gardon, M., Sekerkova, G., Mugnaini, E., & Shaw, G. (1998). The intermediate filament protein peripherin is a marker for cerebellar climbing fibres. Journal of neurocytology, 27, 69-84.

Author response image 1.

The putative inferior olive but not the putative trigeminal nucleus contains peripherin-positive axon bundles (presumptive climbing fibers). (A) Overview picture of a brainstem section stained with anti-peripherin-antibodies (white color). Anti-peripherin-antibodies stain climbing fibers in a wide variety of mammals. The section comes from the posterior brainstem of African elephant cow Bibi; in this posterior region, both putative inferior olive and trigeminal nucleus are visible. Note the bright staining of the dorsolateral nucleus, the putative inferior olive according to Reveyaz et al., and the trigeminal nucleus according to Maseko et al., 2013. (B) High magnification view of the dorsolateral nucleus (corresponding to the upper red rectangle in A). Anti-peripherin-positive axon bundles (putative climbing fibers) are seen in support of the inferior olive hypothesis of Reveyaz et al. (C) High magnification view of the ventromedial nucleus (corresponding to the lower red rectangle in A). The ventromedial nucleus is weakly positive for peripherin but contains no anti-peripherin-positive axon bundles (i.e. no putative climbing fibers) in support of the trigeminal nucleus hypothesis of Reveyaz et al. Note that myelin stripes – weakly visible as dark omissions – are clearly anti-peripherin-negative.

Reviewer #1:

Summary:

This fundamental study provides compelling neuroanatomical evidence underscoring the sensory function of the trunk in African and Asian elephants. Whereas myelinated tracts are classically appreciated as mediating neuronal connections, the authors speculate that myelinated bundles provide functional separation of trunk folds and display elaboration related to the "finger" projections. The authors avail themselves of many classical neuroanatomical techniques (including cytochrome oxidase stains, Golgi stains, and myelin stains) along with modern synchrotron X-ray tomography. This work will be of interest to evolutionary neurobiologists, comparative neuroscientists, and the general public, with its fascinating exploration of the brainstem of an icon sensory specialist.

Comment: We are incredibly grateful for this positive assessment.

Changes: None.

Strengths:

• The authors made excellent use of the precious sample materials from 9 captive elephants.

• The authors adopt a battery of neuroanatomical techniques to comprehensively characterize the structure of the trigeminal subnuclei and properly re-examine the "inferior olive".

• Based on their exceptional histological preparation, the authors reveal broadly segregated patterns of metabolic activity, similar to the classical "barrel" organization related to rodent whiskers.

Comment: The referee provides a concise summary of our findings.

Changes: None.

Weaknesses:

• As the authors acknowledge, somewhat limited functional description can be provided using histological analysis (compared to more invasive techniques).

• The correlation between myelinated stripes and trunk fold patterns is intriguing, and Figure 4 presents this idea beautifully. I wonder - is the number of stripes consistent with the number of trunk folds? Does this hold for both species?

Comment: We agree with the referee’s assessment. We note that cytochrome-oxidase staining is an at least partially functional stain, as it reveals constitutive metabolic activity. A significant problem of the work in elephants is that our recording possibilities are limited, which in turn limits functional analysis. As indicated in Figure 4 for the African elephant Indra, there was an excellent match of trunk folds and myelin stripes. Asian elephants have more, and less conspicuous trunk folds than African elephants. As illustrated in Figure 6, Asian elephants have more, and less conspicuous myelin stripes. Thus, species differences in myelin stripes correlate with species differences in trunk folds.

Changes: We clarify the relation of myelin stripe and trunk fold patterns in our discussion of Figure 6.  

Reviewer #2 (Public Review):

The authors describe what they assert to be a very unusual trigeminal nuclear complex in the brainstem of elephants, and based on this, follow with many speculations about how the trigeminal nuclear complex, as identified by them, might be organized in terms of the sensory capacity of the elephant trunk.

Comment: We agree with the referee’s assessment that the putative trigeminal nucleus described in our paper is highly unusual in size, position, vascularization, and myeloarchitecture. This is why we wrote this paper. We think these unusual features reflect the unique facial specializations of elephants, i.e. their highly derived trunk. Because we have no access to recordings from the elephant brainstem, we cannot back up all our functional interpretations with electrophysiological evidence; it is therefore fair to call them speculative.

Changes: None.

The identification of the trigeminal nuclear complex/inferior olivary nuclear complex in the elephant brainstem is the central pillar of this manuscript from which everything else follows, and if this is incorrect, then the entire manuscript fails, and all the associated speculations become completely unsupported.

Comment: We agree.

Changes: None.

The authors note that what they identify as the trigeminal nuclear complex has been identified as the inferior olivary nuclear complex by other authors, citing Shoshani et al. (2006; 10.1016/j.brainresbull.2006.03.016) and Maseko et al (2013; 10.1159/000352004), but fail to cite either Verhaart and Kramer (1958; PMID 13841799) or Verhaart (1962; 10.1515/9783112519882-001). These four studies are in agreement, but the current study differs.

Comment & Change: We were not aware of the papers of Verhaart and included them in the revised ms.

Let's assume for the moment that the four previous studies are all incorrect and the current study is correct. This would mean that the entire architecture and organization of the elephant brainstem is significantly rearranged in comparison to ALL other mammals, including humans, previously studied (e.g. Kappers et al. 1965, The Comparative Anatomy of the Nervous System of Vertebrates, Including Man, Volume 1 pp. 668-695) and the closely related manatee (10.1002/ar.20573). This rearrangement necessitates that the trigeminal nuclei would have had to "migrate" and shorten rostrocaudally, specifically and only, from the lateral aspect of the brainstem where these nuclei extend from the pons through to the cervical spinal cord (e.g. the Paxinos and Watson rat brain atlases), the to the spatially restricted ventromedial region of specifically and only the rostral medulla oblongata. According to the current paper, the inferior olivary complex of the elephant is very small and located lateral to their trigeminal nuclear complex, and the region from where the trigeminal nuclei are located by others appears to be just "lateral nuclei" with no suggestion of what might be there instead.

Comment: We have three comments here:

1) The referee correctly notes that we argue the elephant brainstem underwent fairly major rearrangements. In particular, we argue that the elephant inferior olive was displaced laterally, by a very large cell mass, which we argue is an unusually large trigeminal nucleus. To our knowledge, such a large compact cell mass is not seen in the ventral brain stem of any other mammal.

2) The referee makes it sound as if it is our private idea that the elephant brainstem underwent major rearrangements and that the rest of the evidence points to a conventional ‘rodent-like’ architecture. This is far from the truth, however. Already from the outside appearance (see our Figure 1B and Figure 6A) it is clear that the elephant brainstem has huge ventral bumps not seen in any other mammal. An extraordinary architecture also holds at the organizational level of nuclei. Specifically, the facial nucleus – the most carefully investigated nucleus in the elephant brainstem – has an appearance distinct from that of the facial nuclei of all other mammals (Maseko et al., 2013; Kaufmann et al., 2022). If both the overall shape and the constituting nuclei of the brainstem are very different from other mammals, it is very unlikely if not impossible that the elephant brainstem follows in all regards a conventional ‘rodent-like’ architecture.

3) The inferior olive is an impressive nucleus in the partitioning scheme we propose (Author response image 1). In fact – together with the putative trigeminal nucleus we describe – it’s the most distinctive nucleus in the elephant brainstem. We have not done volumetric measurements and cell counts here, but think this is an important direction for future work. What has informed our work is that the inferior olive nucleus we describe has the serrated organization seen in the inferior olive of all mammals. We will discuss these matters in depth below.

Changes: None.

Such an extraordinary rearrangement of brainstem nuclei would require a major transformation in the manner in which the mutations, patterning, and expression of genes and associated molecules during development occur. Such a major change is likely to lead to lethal phenotypes, making such a transformation extremely unlikely. Variations in mammalian brainstem anatomy are most commonly associated with quantitative changes rather than qualitative changes (10.1016/B978-0-12-804042-3.00045-2).

Comment: We have two comments here:

1) The referee claims that it is impossible that the elephant brainstem differs from a conventional brainstem architecture because this would lead to lethal phenotypes etc. Following our previous response, this argument does not hold. It is out of the question that the elephant brainstem looks very different from the brainstem of other mammals. Yet, it is also evident that elephants live. The debate we need to have is not if the elephant brainstem differs from other mammals, but how it differs from other mammals.

2). In principle we agree with the referee’s thinking that the model of the elephant brainstem that is most likely correct is the one that requires the least amount of rearrangements to other mammals. We therefore prepared a comparison of the model the referee is proposing (Maseko et al., 2013; see Author response table 1 below) with our proposition. We scored these models on their similarity to other mammals. We find that the referee’s ideas (Maseko et al., 2013) require more rearrangements relative to other mammals than our suggestion.

Changes: Inclusion of Author response table 1, which we discuss in depth below.

The impetus for the identification of the unusual brainstem trigeminal nuclei in the current study rests upon a previous study from the same laboratory (10.1016/j.cub.2021.12.051) that estimated that the number of axons contained in the infraorbital branch of the trigeminal nerve that innervate the sensory surfaces of the trunk is approximately 400 000. Is this number unusual? In a much smaller mammal with a highly specialized trigeminal system, the platypus, the number of axons innervating the sensory surface of the platypus bill skin comes to 1 344 000 (10.1159/000113185). Yet, there is no complex rearrangement of the brainstem trigeminal nuclei in the brain of the developing or adult platypus (Ashwell, 2013, Neurobiology of Monotremes), despite the brainstem trigeminal nuclei being very large in the platypus (10.1159/000067195). Even in other large-brained mammals, such as large whales that do not have a trunk, the number of axons in the trigeminal nerve ranges between 400,000 and 500,000 (10.1007/978-3-319-47829-6_988-1). The lack of comparative support for the argument forwarded in the previous and current study from this laboratory, and that the comparative data indicates that the brainstem nuclei do not change in the manner suggested in the elephant, argues against the identification of the trigeminal nuclei as outlined in the current study. Moreover, the comparative studies undermine the prior claim of the authors, informing the current study, that "the elephant trigeminal ganglion ... point to a high degree of tactile specialization in elephants" (10.1016/j.cub.2021.12.051). While clearly, the elephant has tactile sensitivity in the trunk, it is questionable as to whether what has been observed in elephants is indeed "truly extraordinary".

Comment: These comments made us think that the referee is not talking about the paper we submitted, but that the referee is talking about us and our work in general. Specifically, the referee refers to the platypus and other animals dismissing our earlier work, which argued for a high degree of tactile specialization in elephants. We think the referee’s intuitions are wrong and our earlier work is valid.

Changes: We prepared a Author response image 2 (below) that puts the platypus brain, a monkey brain, and the elephant trigeminal ganglion (which contains a large part of the trunk innervating cells) in perspective.

Author response image 2.

The elephant trigeminal ganglion is comparatively large. Platypus brain, monkey brain, and elephant ganglion. The elephant has two trigeminal ganglia, which contain the first-order somatosensory neurons. They serve mainly for tactile processing and are large compared to a platypus brain (from the comparative brain collection) and are similar in size to a monkey brain. The idea that elephants might be highly specialized for trunk touch is also supported by the analysis of the sensory nerves of these animals (Purkart et al., 2022). Specifically, we find that the infraorbital nerve (which innervates the trunk) is much thicker than the optic nerve (which mediates vision) and the vestibulocochlear nerve (which mediates hearing). Thus, not everything is large about elephants; instead, the data argue that these animals are heavily specialized for trunk touch.

But let's look more specifically at the justification outlined in the current study to support their identification of the unusually located trigeminal sensory nuclei of the brainstem.

(1) Intense cytochrome oxidase reactivity.

(2) Large size of the putative trunk module.

(3) Elongation of the putative trunk module.

(4) The arrangement of these putative modules corresponds to elephant head anatomy.

(5) Myelin stripes within the putative trunk module that apparently match trunk folds.

(6) Location apparently matches other mammals.

(7) Repetitive modular organization apparently similar to other mammals.

(8) The inferior olive described by other authors lacks the lamellated appearance of this structure in other mammals.

Comment: We agree those are key issues.

Changes: None.

Let's examine these justifications more closely.

(1) Cytochrome oxidase histochemistry is typically used as an indicative marker of neuronal energy metabolism. The authors indicate, based on the "truly extraordinary" somatosensory capacities of the elephant trunk, that any nuclei processing this tactile information should be highly metabolically active, and thus should react intensely when stained for cytochrome oxidase. We are told in the methods section that the protocols used are described by Purkart et al (2022) and Kaufmann et al (2022). In neither of these cited papers is there any description, nor mention, of the cytochrome oxidase histochemistry methodology, thus we have no idea of how this histochemical staining was done. To obtain the best results for cytochrome oxidase histochemistry, the tissue is either processed very rapidly after buffer perfusion to remove blood or in recently perfusion-fixed tissue (e.g., 10.1016/0165-0270(93)90122-8). Given: (1) the presumably long post-mortem interval between death and fixation - "it often takes days to dissect elephants"; (2) subsequent fixation of the brains in 4% paraformaldehyde for "several weeks"; (3) The intense cytochrome oxidase reactivity in the inferior olivary complex of the laboratory rat (Gonzalez-Lima, 1998, Cytochrome oxidase in neuronal metabolism and Alzheimer's diseases); and (4) The lack of any comparative images from other stained portions of the elephant brainstem; it is difficult to support the justification as forwarded by the authors. The histochemical staining observed is likely background reactivity from the use of diaminobenzidine in the staining protocol. Thus, this first justification is unsupported.

Comment: The referee correctly notes the description of our cytochrome-oxidase reactivity staining was lacking. This is a serious mistake of ours for which we apologize very much. The referee then makes it sound as if we messed up our cytochrome-oxidase staining, which is not the case. All successful (n = 3; please see our technical comments in the recommendation section) cytochrome-oxidase stainings were done with elephants with short post-mortem times (≤ 2 days) to brain removal/cooling and only brief immersion fixation (≤ 1 day). Cytochrome-oxidase reactivity in elephant brains appears to be more sensitive to quenching by fixation than is the case for rodent brains. We think it is a good idea to include a cytochrome-oxidase staining overview picture because we understood from the referee’s comments that we need to compare our partitioning scheme of the brainstem with that of other authors. To this end, we add a cytochrome-oxidase staining overview picture (Author response image 3) along with an alternative interpretation from Maseko et al., 2013.

Changes: 1) We added details on our cytochrome-oxidase reactivity staining protocol and the cytochrome-oxidase reactivity in the elephant brain in general recommendation.

2) We provide a detailed discussion of the technicalities of cytochrome-oxidase staining below in the recommendation section, where the referee raised further criticisms.

3) We include a cytochrome-oxidase staining overview picture (Author response image 2) along with an alternative interpretation from Maseko et al., 2013.

Author response image 3.

Cytochrome-oxidase staining overview along with the Maseko et al. (2013) scheme Left, coronal cytochrome-oxidase staining overview from African elephant cow Indra; the section is taken a few millimeters posterior to the facial nucleus. Brown is putatively neural cytochrome-reactivity, and white is the background. Black is myelin diffraction and (seen at higher resolution, when you zoom in) erythrocyte cytochrome-reactivity in blood vessels (see our Figure 1E-G); such blood vessel cytochrome-reactivity is seen, because we could not perfuse the animal. There appears to be a minimal outside-in-fixation artifact (i.e. a more whitish/non-brownish appearance of the section toward the borders of the brain). This artifact is not seen in sections from Indra that we processed earlier or in other elephant brains processed at shorter post-mortem/fixation delays (see our Figure 1C). Right, coronal partitioning scheme of Maseko et al. (2013) for the elephant brainstem at an approximately similar anterior-posterior level.

The same structures can be recognized left and right. The section is taken at an anterior-posterior level, where we encounter the trigeminal nuclei in pretty much all mammals. Note that the neural cytochrome reactivity is very high, in what we refer to as the trigeminal-nuclei-trunk-module and what Maseko et al. refer to as inferior olive. Myelin stripes can be recognized here as white omissions.

At the same time, the cytochrome-oxidase-reactivity is very low in what Maseko et al. refer to as trigeminal nuclei. The indistinct appearance and low cytochrome-oxidase-reactivity of the trigeminal nuclei in the scheme of Maseko et al. (2013) is unexpected because trigeminal nuclei stain intensely for cytochrome-oxidase-reactivity in most mammals and because the trigeminal nuclei represent the elephant’s most important body part, the trunk. Staining patterns of the trigeminal nuclei as identified by Maseko et al. (2013) are very different at more posterior levels; we will discuss this matter below.

Justifications (2), (3), and (4) are sequelae from justification (1). In this sense, they do not count as justifications, but rather unsupported extensions.

Comment: These are key points of our paper that the referee does not discuss.

Changes: None.

(4) and (5) These are interesting justifications, as the paper has clear internal contradictions, and (5) is a sequelae of (4). The reader is led to the concept that the myelin tracts divide the nuclei into sub-modules that match the folding of the skin on the elephant trunk. One would then readily presume that these myelin tracts are in the incoming sensory axons from the trigeminal nerve. However, the authors note that this is not the case: "Our observations on trunk module myelin stripes are at odds with this view of myelin. Specifically, myelin stripes show no tapering (which we would expect if axons divert off into the tissue). More than that, there is no correlation between myelin stripe thickness (which presumably correlates with axon numbers) and trigeminal module neuron numbers. Thus, there are numerous myelinated axons, where we observe few or no trigeminal neurons. These observations are incompatible with the idea that myelin stripes form an axonal 'supply' system or that their prime function is to connect neurons. What do myelin stripe axons do, if they do not connect neurons? We suggest that myelin stripes serve to separate rather than connect neurons." So, we are left with the observation that the myelin stripes do not pass afferent trigeminal sensory information from the "truly extraordinary" trunk skin somatic sensory system, and rather function as units that separate neurons - but to what end? It appears that the myelin stripes are more likely to be efferent axonal bundles leaving the nuclei (to form the olivocerebellar tract). This justification is unsupported.

Comment: The referee cites some of our observations on myelin stripes, which we find unusual. We stand by the observations and comments. The referee does not discuss the most crucial finding we report on myelin stripes, namely that they correspond remarkably well to trunk folds.

Changes: None.

(6) The authors indicate that the location of these nuclei matches that of the trigeminal nuclei in other mammals. This is not supported in any way. In ALL other mammals in which the trigeminal nuclei of the brainstem have been reported they are found in the lateral aspect of the brainstem, bordered laterally by the spinal trigeminal tract. This is most readily seen and accessible in the Paxinos and Watson rat brain atlases. The authors indicate that the trigeminal nuclei are medial to the facial nerve nucleus, but in every other species, the trigeminal sensory nuclei are found lateral to the facial nerve nucleus. This is most salient when examining a close relative, the manatee (10.1002/ar.20573), where the location of the inferior olive and the trigeminal nuclei matches that described by Maseko et al (2013) for the African elephant. This justification is not supported.

Comment: The referee notes that we incorrectly state that the position of the trigeminal nuclei matches that of other mammals. We think this criticism is justified.

Changes: We prepared a comparison of the Maseko et al. (2013) scheme of the elephant brainstem with our scheme of the elephant brainstem (see Author response table 1). Here we acknowledge the referee’s argument and we also changed the manuscript accordingly.

(7) The dual to quadruple repetition of rostrocaudal modules within the putative trigeminal nucleus as identified by the authors relies on the fact that in the neurotypical mammal, there are several trigeminal sensory nuclei arranged in a column running from the pons to the cervical spinal cord, these include (nomenclature from Paxinos and Watson in roughly rostral to caudal order) the Pr5VL, Pr5DM, Sp5O, Sp5I, and Sp5C. However, these nuclei are all located far from the midline and lateral to the facial nerve nucleus, unlike what the authors describe in the elephants. These rostrocaudal modules are expanded upon in Figure 2, and it is apparent from what is shown that the authors are attributing other brainstem nuclei to the putative trigeminal nuclei to confirm their conclusion. For example, what they identify as the inferior olive in Figure 2D is likely the lateral reticular nucleus as identified by Maseko et al (2013). This justification is not supported.

Comment: The referee again compares our findings to the scheme of Maseko et al. (2013) and rejects our conclusions on those grounds. We think such a comparison of our scheme is needed, indeed.

Changes: We prepared a comparison of the Maseko et al. (2013) scheme of the elephant brainstem with our scheme of the elephant brainstem (see Author response table 1).

(8) In primates and related species, there is a distinct banded appearance of the inferior olive, but what has been termed the inferior olive in the elephant by other authors does not have this appearance, rather, and specifically, the largest nuclear mass in the region (termed the principal nucleus of the inferior olive by Maseko et al, 2013, but Pr5, the principal trigeminal nucleus in the current paper) overshadows the partial banded appearance of the remaining nuclei in the region (but also drawn by the authors of the current paper). Thus, what is at debate here is whether the principal nucleus of the inferior olive can take on a nuclear shape rather than evince a banded appearance. The authors of this paper use this variance as justification that this cluster of nuclei could not possibly be the inferior olive. Such a "semi-nuclear/banded" arrangement of the inferior olive is seen in, for example, giraffe (10.1016/j.jchemneu.2007.05.003), domestic dog, polar bear, and most specifically the manatee (a close relative of the elephant) (brainmuseum.org; 10.1002/ar.20573). This justification is not supported.

Comment: We carefully looked at the brain sections referred to by the referee in the brainmuseum.org collection. We found contrary to the referee’s claims that dogs, polar bears, and manatees have a perfectly serrated (a cellular arrangement in curved bands) appearance of the inferior olive. Accordingly, we think the referee is not reporting the comparative evidence fairly and we wonder why this is the case.

Changes: None.

Thus, all the justifications forwarded by the authors are unsupported. Based on methodological concerns, prior comparative mammalian neuroanatomy, and prior studies in the elephant and closely related species, the authors fail to support their notion that what was previously termed the inferior olive in the elephant is actually the trigeminal sensory nuclei. Given this failure, the justifications provided above that are sequelae also fail. In this sense, the entire manuscript and all the sequelae are not supported.

Comment: We disagree. To summarize:

(1) Our description of the cytochrome oxidase staining lacked methodological detail, which we have now added; the cytochrome oxidase reactivity data are great and support our conclusions.

(2)–(5)The referee does not really discuss our evidence on these points.

(6) We were wrong and have now fixed this mistake.

(7) The referee asks for a comparison to the Maseko et al. (2013) scheme (agreed, see Author response image 4 4 and Author response table 1).

(8) The referee bends the comparative evidence against us.

Changes: None.

A comparison of the elephant brainstem partitioning schemes put forward by Maseko et al 2013 and by Reveyaz et al.

To start with, we would like to express our admiration for the work of Maseko et al. (2013). These authors did pioneering work on obtaining high-quality histology samples from elephants. Moreover, they made a heroic neuroanatomical effort, in which they assigned 147 brain structures to putative anatomical entities. Most of their data appear to refer to staining in a single elephant and one coronal sectioning plane. The data quality and the illustration of results are excellent.

We studied mainly two large nuclei in six (now 7) elephants in three (coronal, parasagittal, and horizontal) sectioning planes. The two nuclei in question are the two most distinct nuclei in the elephant brainstem, namely an anterior ventromedial nucleus (the trigeminal trunk module in our terminology; the inferior olive in the terminology of Maseko et al., 2013) and a more posterior lateral nucleus (the inferior olive in our terminology; the posterior part of the trigeminal nuclei in the terminology of Maseko et al., 2013).

Author response image 4 gives an overview of the two partitioning schemes for inferior olive/trigeminal nuclei along with the rodent organization (see below).

Author response image 4.

Overview of the brainstem organization in rodents & elephants according to Maseko et. (2013) and Reveyaz et al. (this paper).

The strength of the Maseko et al. (2013) scheme is the excellent match of the position of elephant nuclei to the position of nuclei in the rodent (Author response image 4). We think this positional match reflects the fact that Maseko et al. (2013) mapped a rodent partitioning scheme on the elephant brainstem. To us, this is a perfectly reasonable mapping approach. As the referee correctly points out, the positional similarity of both elephant inferior olive and trigeminal nuclei to the rodent strongly argues in favor of the Maseko et al. (2013), because brainstem nuclei are positionally very conservative.

Other features of the Maseko et al. (2013) scheme are less favorable. The scheme marries two cyto-architectonically very distinct divisions (an anterior indistinct part) and a super-distinct serrated posterior part to be the trigeminal nuclei. We think merging entirely distinct subdivisions into one nucleus is a byproduct of mapping a rodent partitioning scheme on the elephant brainstem. Neither of the two subdivisions resemble the trigeminal nuclei of other mammals. The cytochrome oxidase staining patterns differ markedly across the anterior indistinct part (see our Author response image 4) and the posterior part of the trigeminal nuclei and do not match with the intense cytochrome oxidase reactivity of other mammalian trigeminal nuclei (Referee Figure 3). Our anti-peripherin staining indicates that there probably no climbing fibers, in what Maseko et al. think. is inferior olive; this is a potentially fatal problem for the hypothesis. The posterior part of Maseko et al. (2013) trigeminal nuclei has a distinct serrated appearance that is characteristic of the inferior olive in other mammals. Moreover, the inferior olive of Maseko et al. (2013) lacks the serrated appearance of the inferior olive seen in pretty much all mammals; this is a serious problem.

The partitioning scheme of Reveyaz et al. comes with poor positional similarity but avoids the other problems of the Maseko et al. (2013) scheme. Our explanation for the positionally deviating location of trigeminal nuclei is that the elephant grew one of the if not the largest trigeminal systems of all mammals. As a result, the trigeminal nuclei grew through the floor of the brainstem. We understand this is a post hoc just-so explanation, but at least it is an explanation.

The scheme of Reveyaz et al. was derived in an entirely different way from the Maseko model. Specifically, we were convinced that the elephant trigeminal nuclei ought to be very special because of the gigantic trigeminal ganglia (Purkart et al., 2022). Cytochrome-oxidase staining revealed a large distinct nucleus with an elongated shape. Initially, we were freaked out by the position of the nucleus and the fact that it was referred to as inferior olive by other authors. When we found an inferior-olive-like nucleus at a nearby (although at an admittedly unusual) location, we were less worried. We then optimized the visualization of myelin stripes (brightfield imaging etc.) and were able to collect an entire elephant trunk along with the brain (African elephant cow Indra). When we made the one-to-one match of Indra’s trunk folds and myelin stripes (Figure 4) we were certain that we had identified the trunk module of the trigeminal nuclei. We already noted at the outset of our rebuttal that we now consider such certainty a fallacy of overconfidence. In light of the comments of Referee 2, we feel that a further discussion of our ideas is warranted. A strength of the Reveyaz model is that nuclei look like single anatomical entities. The trigeminal nuclei look like trigeminal nuclei of other mammals, the trunk module has a striking resemblance to the trunk and the inferior olive looks like the inferior olive of other mammals.

We evaluated the fit of the two models in the form of a table (Author response table 1; below). Unsurprisingly, Author response table 1 aligns with our views of elephant brainstem partitioning.

Author response table 1.

Qualitative evaluation of elephant brainstem partitioning schemes

++ = Very attractive; + = attractive; - = unattractive; -- = very unattractive We scored features that are clear and shared by all mammals – as far as we know them – as very attractive. We scored features that are clear and are not shared by all mammals – as far as we know them – as very unattractive. Attractive features are either less clear or less well-shared features. Unattractive features are either less clear or less clearly not shared features.

Author response table 1 suggests two conclusions to us. (i) The Reveyaz et al. model has mainly favorable properties. The Maseko et al. (2013) model has mainly unfavorable properties. Hence, the Reveyaz et al. model is more likely to be true. (ii) The outcome is not black and white, i.e., both models have favorable and unfavorable properties. Accordingly, we overstated our case in our initial submission and toned down our claims in the revised manuscript.

What the authors have not done is to trace the pathway of the large trigeminal nerve in the elephant brainstem, as was done by Maseko et al (2013), which clearly shows the internal pathways of this nerve, from the branch that leads to the fifth mesencephalic nucleus adjacent to the periventricular grey matter, through to the spinal trigeminal tract that extends from the pons to the spinal cord in a manner very similar to all other mammals. Nor have they shown how the supposed trigeminal information reaches the putative trigeminal nuclei in the ventromedial rostral medulla oblongata. These are but two examples of many specific lines of evidence that would be required to support their conclusions. Clearly, tract tracing methods, such as cholera toxin tracing of peripheral nerves cannot be done in elephants, thus the neuroanatomy must be done properly and with attention to detail to support the major changes indicated by the authors.

Comment: The referee claims that Maseko et al. (2013) showed by ‘tract tracing’ that the structures they refer to trigeminal nuclei receive trigeminal input. This statement is at least slightly misleading. There is nothing of what amounts to proper ‘tract tracing’ in the Maseko et al. (2013) paper, i.e. tracing of tracts with post-mortem tracers. We tried proper post-mortem tracing but failed (no tracer transport) probably as a result of the limitations of our elephant material. What Maseko et al. (2013) actually did is look a bit for putative trigeminal fibers and where they might go. We also used this approach. In our hands, such ‘pseudo tract tracing’ works best in unstained material under bright field illumination, because myelin is very well visualized. In such material, we find: (i) massive fiber tracts descending dorsoventrally roughly from where both Maseko et al. 2013 and we think the trigeminal tract runs. (ii) These fiber tracts run dorsoventrally and approach, what we think is the trigeminal nuclei from lateral.

Changes: Ad hoc tract tracing see above.

So what are these "bumps" in the elephant brainstem?

Four previous authors indicate that these bumps are the inferior olivary nuclear complex. Can this be supported?

The inferior olivary nuclear complex acts "as a relay station between the spinal cord (n.b. trigeminal input does reach the spinal cord via the spinal trigeminal tract) and the cerebellum, integrating motor and sensory information to provide feedback and training to cerebellar neurons" (https://www.ncbi.nlm.nih.gov/books/NBK542242/). The inferior olivary nuclear complex is located dorsal and medial to the pyramidal tracts (which were not labeled in the current study by the authors but are clearly present in Fig. 1C and 2A) in the ventromedial aspect of the rostral medulla oblongata. This is precisely where previous authors have identified the inferior olivary nuclear complex and what the current authors assign to their putative trigeminal nuclei. The neurons of the inferior olivary nuclei project, via the olivocerebellar tract to the cerebellum to terminate in the climbing fibres of the cerebellar cortex.

Comment: We agree with the referee that in the Maseko et al. (2013) scheme the inferior olive is exactly where we expect it from pretty much all other mammals. Hence, this is a strong argument in favor of the Maseko et al. (2013) scheme and a strong argument against the partitioning scheme suggested by us.

Changes: Please see our discussion above.

Elephants have the largest (relative and absolute) cerebellum of all mammals (10.1002/ar.22425), this cerebellum contains 257 x109 neurons (10.3389/fnana.2014.00046; three times more than the entire human brain, 10.3389/neuro.09.031.2009). Each of these neurons appears to be more structurally complex than the homologous neurons in other mammals (10.1159/000345565; 10.1007/s00429-010-0288-3). In the African elephant, the neurons of the inferior olivary nuclear complex are described by Maseko et al (2013) as being both calbindin and calretinin immunoreactive. Climbing fibres in the cerebellar cortex of the African elephant are clearly calretinin immunopositive and also are likely to contain calbindin (10.1159/000345565). Given this, would it be surprising that the inferior olivary nuclear complex of the elephant is enlarged enough to create a very distinct bump in exactly the same place where these nuclei are identified in other mammals?

Comment: We agree with the referee that it is possible and even expected from other mammals that there is an enlargement of the inferior olive in elephants. Hence, a priori one might expect the ventral brain stem bumps to the inferior olive, this is perfectly reasonable and is what was done by previous authors. The referee also refers to calbindin and calretinin antibody reactivity. Such antibody reactivity is indeed in line with the referee’s ideas and we considered these findings in our Referee Table 1. The problem is, however, that neither calbindin nor calretinin antibody reactivity are highly specific and indeed both nuclei in discussion (trigeminal nuclei and inferior olive) show such reactivity. Unlike the peripherin-antibody staining advanced by us, calbindin nor calretinin antibody reactivity cannot distinguish the two hypotheses debated.

Changes: Please see our discussion above.

What about the myelin stripes? These are most likely to be the origin of the olivocerebellar tract and probably only have a coincidental relationship with the trunk. Thus, given what we know, the inferior olivary nuclear complex as described in other studies, and the putative trigeminal nuclear complex as described in the current study, is the elephant inferior olivary nuclear complex. It is not what the authors believe it to be, and they do not provide any evidence that discounts the previous studies. The authors are quite simply put, wrong. All the speculations that flow from this major neuroanatomical error are therefore science fiction rather than useful additions to the scientific literature.

Comment: It is unlikely that the myelin stripes are the origin of the olivocerebellar tract as suggested by the referee. Specifically, the lack of peripherin-reactivity indicates that these fibers are not climbing fibers (Referee Figure 1). In general, we feel the referee does not want to discuss the myelin stripes and obviously thinks we made up the strange correspondence of myelin stripes and trunk folds.

Changes: Please see our discussion above.

What do the authors actually have?

The authors have interesting data, based on their Golgi staining and analysis, of the inferior olivary nuclear complex in the elephant.

Comment: The referee reiterates their views.

Changes: None.

Reviewer #3 (Public Review):

Summary:

The study claims to investigate trunk representations in elephant trigeminal nuclei located in the brainstem. The researchers identified large protrusions visible from the ventral surface of the brainstem, which they examined using a range of histological methods. However, this ventral location is usually where the inferior olivary complex is found, which challenges the author's assertions about the nucleus under analysis. They find that this brainstem nucleus of elephants contains repeating modules, with a focus on the anterior and largest unit which they define as the putative nucleus principalis trunk module of the trigeminal. The nucleus exhibits low neuron density, with glia outnumbering neurons significantly. The study also utilizes synchrotron X-ray phase contrast tomography to suggest that myelin-stripe-axons traverse this module. The analysis maps myelin-rich stripes in several specimens and concludes that based on their number and patterning they likely correspond with trunk folds; however, this conclusion is not well supported if the nucleus has been misidentified.

Comment: The referee gives a concise summary of our findings. The referee acknowledges the depth of our analysis and also notes our cellular results. The referee – in line with the comments of Referee 2 – also points out that a misidentification of the nucleus under study is potentially fatal for our analysis. We thank the referee for this fair assessment.

Changes: We feel that we need to alert the reader more broadly to the misidentification concern. We think the critical comments of Referee 2, which will be published along with our manuscript, will go a long way in doing so. We think the eLife publishing format is fantastic in this regard. We will also include pointers to these concerns in the revised manuscript.

Strengths:

The strength of this research lies in its comprehensive use of various anatomical methods, including Nissl staining, myelin staining, Golgi staining, cytochrome oxidase labeling, and synchrotron X-ray phase contrast tomography. The inclusion of quantitative data on cell numbers and sizes, dendritic orientation and morphology, and blood vessel density across the nucleus adds a quantitative dimension. Furthermore, the research is commendable for its high-quality and abundant images and figures, effectively illustrating the anatomy under investigation.

Comment: Again, a very fair and balanced set of comments. We are thankful for these comments.

Changes: None.

Weaknesses:

While the research provides potentially valuable insights if revised to focus on the structure that appears to be the inferior olivary nucleus, there are certain additional weaknesses that warrant further consideration. First, the suggestion that myelin stripes solely serve to separate sensory or motor modules rather than functioning as an "axonal supply system" lacks substantial support due to the absence of information about the neuronal origins and the termination targets of the axons. Postmortem fixed brain tissue limits the ability to trace full axon projections. While the study acknowledges these limitations, it is important to exercise caution in drawing conclusions about the precise role of myelin stripes without a more comprehensive understanding of their neural connections.

Comment: The referee points out a significant weakness of our study, namely our limited understanding of the origin and targets of the axons constituting the myelin stripes. We are very much aware of this problem and this is also why we directed high-powered methodology like synchrotron X-ray tomograms to elucidate the structure of myelin stripes. Such analysis led to advances, i.e., we now think, what looks like stripes are bundles and we understand the constituting axons tend to transverse the module. Such advances are insufficient, however, to provide a clear picture of myelin stripe connectivity.

Changes: We think solving the problems raised by the referee will require long-term methodological advances and hence we will not be able to solve these problems in the current revision. Our long-term plans for confronting these issues are the following: (i) Improving our understanding of long-range connectivity by post-mortem tracing and MR-based techniques such as Diffusion-Tensor-Imaging. (ii) Improving our understanding of mid and short-range connectivity by applying even larger synchrotron X-ray tomograms and possible serial EM.

Second, the quantification presented in the study lacks comparison to other species or other relevant variables within the elephant specimens (i.e., whole brain or brainstem volume). The absence of comparative data for different species limits the ability to fully evaluate the significance of the findings. Comparative analyses could provide a broader context for understanding whether the observed features are unique to elephants or more common across species. This limitation in comparative data hinders a more comprehensive assessment of the implications of the research within the broader field of neuroanatomy. Furthermore, the quantitative comparisons between African and Asian elephant specimens should include some measure of overall brain size as a covariate in the analyses. Addressing these weaknesses would enable a richer interpretation of the study's findings.

Comment: The referee suggests another series of topics, which include the analysis of brain parts volumes or overall brain size. We agree these are important issues, but we also think such questions are beyond the scope of our study.

Changes: We hope to publish comparative data on elephant brain size and shape later this year.  

Author Response

eLife assessment

This study presents a valuable method to visualize the location of the cell types discovered through single-cell RNA sequencing. The evidence supporting the claims is solid, but the inclusion of a larger number of samples would strengthen the study. It would also be helpful to have the methods explained in more detail. The work will be of interest to those seeking to identify new cell types from scRNA-seq and snRNA-seq data.

Response: We are surprised about the editor’s assessment of our paper as a “valuable” method. This is the first Drosophila adult spatial transcriptomics paper. Hence, we would at least consider this being an “important” method. Spatial transcriptomics has thus far only been done in embryos, which are easy to process for FISH for many decades. Integration with single-cell data is also new. We are further surprised that this assessment does not mention the identification of subcellular mRNA patterns in adult muscles as an “important” biological finding of this paper. We are not aware that any localized mRNAs in Drosophila muscles were known prior to our study. This shows the advantage of spatial transcriptomics over single-cell techniques.

The work indeed does not represent a full spatial fly adult atlas – however, a proof of principle study covering both the head and body that we consider at least “important”.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this manuscript, Janssens et al. addressed the challenge of mapping the location of transcriptionally unique cell types identified by single nuclei sequencing (snRNA-seq) data available through the Fly Cell Atlas. They identified 100 transcripts for head samples and 50 transcripts for fly body samples allowing the identification of every unique cell type discovered through the Fly Cell Atlas. To map all of these cell types, the authors divided the fly body into head and body samples and used the Molecular Cartography (Resolve Biosciences) method to visualize these transcripts. This approach allowed them to build spatial tissue atlases of the fly head and body, to identify the location of previously unknown cell types and the subcellular localization of different transcripts. By combining snRNA-seq data from the Fly Cell Atlas with their spatially resolved transcriptomics (SRT) data, they demonstrated an automated cell type annotation strategy to identify unknown clusters and infer their location in the fly body. This manuscript constitutes a proof-of-principle study to map the location of the cells identified by ever-growing single-cell transcriptomic datasets generated by others.

Strengths:

The authors used the Molecular Cartography (Resolve Biosciences) method to visualize 100 transcripts for head samples and 50 transcripts for fly body samples in high resolution. This method achieves high resolution by multiplexing a large number of transcript visualization steps and allows the authors to map the location of unique cell types identified by the Fly Cell Atlas.

Response: We thank the reviewer for their comment, but are surprised that this assessment does not mention the identification of subcellular mRNA patterns in adult muscles as an important biological finding of this paper. This might be due to the visualization problem that this reviewer was facing with a greyscale version of the PDF as mentioned in the comments below. We do not know what caused the technical problem for this reviewer (the PDF figures are in color on the eLife website and on bioRxiv). We are surprised that the eLife discussion session did not resolve this issue.

Weaknesses:

Combining single-nuclei sequencing (snRNA-seq) data with spatially resolved transcriptomics (SRT) data is challenging, and the methods used by the authors in this study cannot reliably distinguish between cells, especially in brain regions where the processes of different neurons are clustered, such as in neuropils. This means that a grid that the authors mark as a unique cell may actually be composed of processes from multiple cells.

Response: The size of the fly is one of the most challenging aspects of performing spatial transcriptomics. The small size of the samples led to detachment from the slides, which we solved by coating the slides with gelatin. While the resolution of Molecular Cartography is high (<200nm), in the brain challenges remain as noted by the reviewer. Drosophila neuronal nuclei are notoriously small and cannot be easily resolved with current techniques. We agree that for a full atlas either expansion microscopy, 3D techniques or even higher resolution will be required.

Reviewer #2 (Public Review):

Summary:

The landmark publication of the "Fly Atlas" in 2022 provided a single cell/nuclear transcriptomic dataset from 15 individually dissected tissues, the entire head, and the body of male and female flies. These data led to the annotation of more than 250 cell types. While certainly a powerful and data-rich approach, a significant step forward relies on mapping these data back to the organism in time and space. The goal of this manuscript is to map 150 transcripts defined by the Fly Atlas by FISH and in doing so, provide, for the first time, a spatial transcriptomic dataset of the adult fly. Using this approach (Molecular Cartography with Resolve Biosciences), the authors, furthermore, distinguish different RNA localizations within a cell type. In addition, they seek to use this approach to define previously unannotated clusters found in the Fly Atlas. As a resource for the community at large interested in the computational aspects of their pipeline, the authors compare the strengths and weaknesses of their approach to others currently being performed in the field.

Strengths:

1. The authors use Resolve Biosciences and a novel bioinformatics approach to generate a FISH-based spatial transcriptomics map. To achieve this map, they selected 150 genes (50 body; 100 head) that were highly expressed in the single nuclear RNA sequencing dataset and were used in the 2022 paper to annotate specific cell types; moreover, the authors chose several highly expressed genes characteristic of unannotated cell types. Together, the approach and generated data are important next steps in translating the transcriptomic data to spatial data in the organism.

Response: We thank the reviewer for this comment but would like to add that the statement that we selected “150 genes (50 body; 100 head) that were highly expressed in the single nuclear RNA sequencing dataset” is not correct. We have chosen genes with widely differing expression levels (log-scale range of 3.95 in body, 5.76 in head). Many of the chosen genes are also transcription factors. In fact, the here introduced method is more sensitive than the single cell atlas: the tinman positive cells were readily located (even non-heart cells were found to express tinman), whereas in the single cell FCA data tinman expression is often not detected in the cardiomyocytes (Tinman is detected in 273 cells in the entire FCA (mean expression of 1.44 UMI in positive cells), and in 71 cells out of 273 cardial cells (26%)).

Author response image 1.

Density plots for body (left) and head (right) showing levels of gene expression detected in scRNA-seq (body: Fly Cell Atlas, Li et al. 2022, head: Pech et al. (2023)). Blue: all genes, red: genes used in the spatial study.

1. Working with Resolve, the authors developed a relatively high throughput approach to analyze the location of transcripts in Drosophila adults. This approach confirmed the identification of particular cell types suggested by the FlyAtlas as well as revealed interesting subcellular locations of the transcripts within the cell/tissue type. In addition, the authors used co-expression of different RNAs to unbiasedly identify "new cell types". This pipeline and data provide a roadmap for additional analyses of other time points, female flies, specific mutants, etc.

2. The authors show that their approach reveals interesting patterns of mRNA distribution (e.g alpha- and beta-Trypsin in apical and basal regions of gut enterocytes or striped patterns of different sarcomeric proteins in body muscle). These observations are novel and reveal unexpected patterns. Likewise, the authors use their more extensive head database to identify the location of cells in the brain. They report the resolution of 23 clusters suggested by the single-cell sequencing data, given their unsupervised clustering approach. This identification supports the use of spatial cell transcriptomics to characterize cell types (or cell states).

3. Lastly, the authors compare three different approaches --- their own described in this manuscript, Tangram, and SpaGE - which allow integration of single cell/nuclear RNA-seq data with spatial localization FISH. This was a very helpful section as the authors compared the advantages and disadvantages (including practical issues, like computational time).

Weaknesses:

1. Experimental setup. It is not clear how many and, for some of the data, the sex of the flies that were analyzed. It appears that for the body data, only one male was analyzed. For the heads, methods say male and female heads, but nothing is annotated in the figures. As such, it remains unclear how robust these data are, given such a limited sample from one sex. As such, the claims of a spatial atlas of the entire fly body and its head ("a rosetta stone") are overstated. Also, the authors should clearly state in the main text and figure legends the sex, the age, how many flies, and how many replicates contributed to the data presented (not just the methods). What also adds to the confusion is the use of "n" in para 2 of the results. " ... we performed coronal sections at different depths in the head (n=13)..." 13 sections in total from 1 head or sections from 13 heads? Based on the body and what is shown in the figure, one assumes 13 sections from one head. Please clarify.

Response: While we agree that sex differences present indeed an interesting opportunity to study with spatial transcriptomics, our goal was not to define male/female differences but rather to establish the technology to go into this detail if wanted in the future. In the revised version, we will provide a more detailed description of the sections, including their sex/genotype/age. We would like to point out that we verified the specificity of our FISH method on all the body sections (Figure 2A, TpnC4 & Act88F) and not only on one. Furthermore, we also would like to state that the idea of “a rosetta stone” was mentioned as a future prospect. We will rewrite the discussion to make this more clear.

1. Probes selected: Information from the methods section should be put into the main text so that it is clear what and why the gene lists were selected. The current main text is confusing. If the authors want others to use their approach, then some testing or, at the very least, some discussion of lower expressed genes should be added. How useful will this approach be if only highly expressed genes can be resolved? In addition, while it is understood that the company has a propriety design algorithm for the probes, the authors should comment on whether the probes for individual genes detect all isoforms or subsets (exons and introns?), given the high level of splicing in tissues such as muscle.

Response: As stated above, while there is a slight bias to higher expressed genes (as expected for marker genes), we have also used very low expressed genes like tinman (body) or sens (head). This shows that our method is more sensitive than single-cell data, as ALL cardiomyocytes can be identified by tinman expression and not only some are positive, as is the case in the FCA data. In fact, the method can’t resolve too highly expressed genes due to optical crowding of the signal leading to a worse quantification. For this reason, ninaE was removed from the analysis (as mentioned in Spatial transcriptomics allows the localization of cell types in the head and brain and in Methods).

As mentioned in the Methods, the probes are designed on gene level targeting all isoforms, but favoring principal isoforms (weighted by APPRIS level). The high level of splicing is indeed interesting and we expect that in the future spatial transcriptomics can help to generate more insight in this.

1. Imaging: it isn't clear from the text whether the repeated rounds of imaging impacted data collection. In many of what appear to be "stitched" images, there are gradients of signal (eg, figure 2F); please comment. Also, since this a new technique, could a before and after comparison of the original images and the segmented images be shown in the supplemental data so that the reader can better appreciate how the authors assessed/chose/thresholded their data? More discussion of the accuracy of spot detection would be helpful.

Response: Any high-resolution imaging (pixel size = 138 nm) of a large field of view (>1mm) uses a stitching method to combine several individual images to reconstruct a large field of view. This does not generate signal gradients, apart from lower signal at the extreme edges of each of the individual images. The spot detection algorithm was written and used by Resolve Biosciences and benchmarked for human (Hela) and mouse (NIH-3T3) cell lines in Groiss et al. 2021 (Highly resolved spatial transcriptomics for detection of rare events in cells, biorxiv). The specificity of the decoded probes was found to lie between 99.45 and 99.9% here, matching the results we found for TpnC4 and Act88F (99.4 and 99.8%). We will add their analysis to our discussion.

1. The authors comment on how many RNAs they detected (first paragraph of results). How do these numbers compare to the total mRNA present as detected by single-cell or single-nuclear sequencing?

Response: The total number of mRNAs detected per spatial transcriptomics experiment is much higher for the body samples compared to single-cell experiments (FCA data). In the head it is slightly lower, but here it is important to note that not all cell types are present in each slice in the head (while they are all present in the head scRNA experiments). A comparison on the cell-type level would be more meaningful, and we will investigate this for the revision.

Author response image 2.

Barplots showing total number of mRNA molecules detected in Molecular Cartography (Resolve, spatial spots) and in snRNA-seq data from the Fly Cell Atlas (10x Genomics, UMIs). Individual black dots show individual experiments, counts are only shown for the chosen gene panel for each sample. Bar shows the mean, with error bars representing the standard error.

1. Using this higher throughput method of spatial transcriptomics, the authors discern different cell types and different localization patterns within a tissue/cell type.

a. The authors should comment on the resolution provided by this approach, in terms of the detection of populations of mRNAs detected by low throughput methods, for example, in glia, motor neuron axons, and trachea that populate muscle tissue. Are these found in the images? Please show.

Response: We did not add any markers for trachea in our gene panel, but we do detect sparse spots of repo (glia) and elav/VGlut in the muscle tissues (Gad1/VAChT are hardly detected in the muscle tissue). This is consistent with the glutamatergic nature of motor neurons in Drosophila as described previously (Schuster CM (2006) Glutamatergic synapses of Drosophila neuromuscular junctions: a high-resolution model for the analysis of experience-dependent potentiation. Cell Tissue Res 326: 287–299.)

Author response image 3.

Molecular Cartography zoomed in on indirect flight muscle. Segmented nuclei are shown in white (based on DAPI), scalebars represent 100 μm).

b. The authors show interesting localization patterns in muscle tissue for different sarcomere protein-coding mRNAs, including enrichment of sls in muscle nuclei located near the muscle-tendon attachment sites. As this high throughput approach is newly being applied to the adult fly, it would increase confidence in these data, if the authors would confirm these data using a low throughput FISH technique. For example, do the authors detect such alternating "stripes" ( Act 88F, TpnC4, and Mhc) or enriched localization (sls) using FISH that doesn't rely on the repeated colorization, imaging, decolorization of the probes?

Response: We thank the reviewer for their interest in the localization patterns in muscle tissue. We could confirm localized mRNA in all the sections analyzed, in flight muscles as well as in leg muscles. We furthermore show that Act 88F, TpnC4 are not detected outside of flight muscle cells (99.4% and 99.8% of the single molecular signal in flight muscles only). Hence, we already show the specificity test in a much more quantitative way compared to traditional FISH, which often includes amplification.

1. The authors developed an unbiased method to identify "new cell types" which relies on co-expression of different transcripts. Are these new cell types or a cell state? While expression is a helpful first step, without any functional data, the significance of what the authors found is diminished. The authors need to soften their statements.

Response: The term “new cell types” only appears in the title. We agree that with the current spatial map we cannot be sure to have found “new cell types”, instead we have shown where unannotated clusters from scRNA-seq map, based on gene expression. Therefore, we will tone down the title in the revised version and thank the reviewer for this valuable suggestion.

Appraisal:

The authors' goal is to map single cell/nuclear RNAseq data described in the 2022 Fly Atlas paper spatially within an organism to achieve a spatial transcriptomic map of the adult fly; no doubt, this is a critical next step in our use of 'omics approaches. While this manuscript does the hard work of trying to take this next step, including developing and testing a new pipeline for high throughput FISH and its analysis, it falls short, in its present form, in achieving this goal. The authors discuss creating a robust spatial map, based on one male fly. Moreover, they do not reveal principles of mRNA localization, as stated in the abstract; they show us patterns, but nothing about the logic or function of these patterns. This same criticism can be said of the identification of "new cell types, just based on RNA colocalization. In both cases (mRNA subcellular localization or cell type identification), further data in the form of validation with traditional low throughput FISH and genetic manipulations to assess the relation to cell function are required for the authors to make such claims.

Response: We have indeed used one male fly for the adult male body data. This is mainly due to the cost of the sample processing. We used 12 individuals for the head samples (from 1 individual we acquired 2 sections, a total of 13 sections). We show that the body samples show a high correlation with each other, while the head samples cover multiple depths of the head. Still, even in the head, we find that sections at similar depths show a high similarity to each other in terms of gene-gene co-expression and expression patterns. Although obtaining more sections would be valuable, we don’t believe it to be necessary for the current goals. Additional replicates beyond the ones we already provide would require significant amounts of extra time and budget, while they would produce similar results as we already show. We are therefore reluctant to repeat the effort again.

The usage of the term “new cell types” is indeed ambiguous and we will tone this down in the revised version. Instead, we meant that unannotated clusters could be mapped to their location. In the text, we further specify that this means that now we only have inferred the location of the nuclei and that for neurons their function/processes are still unknown. As such, our data provides a starting point to identify new cell types since their marker genes and nuclear location are inferred. The next step to identify “new cell types” would indeed be to acquire genetic access to the cell types and characterize them in more detail. This is currently beyond our goals, and therefore we will tone down the title in the revised version and thank the reviewer for this valuable suggestion.

Discussion of likely impact:

If revised, these data, and importantly the approach, would impact those working on Drosophila adults as well as those working in other model systems where single cell/nuclear sequencing is being translated to the spatial localization within the organism. The subcellular localization data - for example, the size of transcripts and how that relates to localization or the patterns of sarcomeric protein localization in muscle - are intriguing, and would likely impact our thinking on RNA localization, transport, etc if confirmed. Lastly, the authors compare their computational approaches to those available in the field; this is valuable as this is a rapidly evolving field and such considerations are critical for those wishing to use this type of approach.

Response: We believe that our manuscript as it stands now is already an “important” paper that will strongly impact the Drosophila community (and beyond the spatial transcriptomics community). As it stands, it provides the groundwork for a full Drosophila adult spatial atlas, similar to how early scRNA-seq datasets provided a framework for the Fly Cell Atlas. In the manuscript we provide both experimental information on how to successfully perform spatial transcriptomics (treating slides for optimal attachment) and the data serves as a benchmark for future experiments to improve upon (similar to how early Drop-seq datasets were compared to later 10x datasets in single-cell transcriptomics). In addition, it also provides proof of principle methods on how to integrate the FCA data with these spatial data and it identifies localized mRNA species in large adult muscle cells, showing the complementarity of spatial techniques with single-cell RNA-seq. To conclude, this is the first spatial adult Drosophila transcriptomics paper, locating 150 mRNA species with easy data access in our user portal (https://spatialfly.aertslab.org/).

Author response:

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

Summary: 

Laura Morano and colleagues have performed a screen to identify compounds that interfere with the formation of TopBP1 condensates. TopBP1 plays a crucial role in the DNA damage response, and specifically the activation of ATR. They found that the GSK-3b inhibitor AZD2858 reduced the formation of TopBP1 condensates and activation of ATR and its downstream target CHK1 in colorectal cancer cell lines treated with the clinically relevant irinotecan active metabolite SN-38. This inhibition of TopBP1 condensates by AZD2858 was independent from its effect on GSK-3b enzymatic activity. Mechanistically, they show that AZD2858 thus can interfere with intra-S-phase checkpoint signaling, resulting in enhanced cytostatic and cytotoxic effects of SN-38 (or SN-38+Fluoracil aka FOLFIRI) in vitro in colorectal carcinoma cell lines. 

Major comments: 

Overall the work is rigorous and the main conclusions are convincing. However, they only show the effects of their combination treatments on colorectal cancer cell lines. I'm worried that blocking the formation of TopB1 condensates will also be detrimental in non-transformed cells. Furthermore it is somewhat disappointing that it remains unclear how AZD2858 blocks selfassembly of TopBP1 condensates, although I understand that unraveling this would be complex and somewhat out-of-reach for now. 

We appreciate your feedback and fully recognize the importance of understanding how AZD2858 blocks the assembly of TopBP1 condensates. While we understand your disappointment, addressing this question remains a key focus for us. Keeping in mind that unravelling such a mechanism in vitro or in vivo is rather challenging, we have consulted an expert who has made efforts to predict the potential docking sites of AZD2858 on TopBP1, which may provide valuable insights for future experimental investigations. Using an AlphaFold model (no crystal or cryo-EM structure available) and looking for suitable pockets or cavities in which AZD2858 could bind, the analyses, though requiring cautious interpretation, suggested that AZD2858 may target the BRCT1 and BRCT8 domains (as shown below, two pockets n°1 and 7 with sufficient volume and surrounded by b-sheets structures like other GSK3 inhibitor) of TopBP1.

However, these are preliminary results that require further exploration and experimental validation to confirm their significance and mechanistic implications.

Author response image 1.

Here are some specific points for improvement: 

(1) The authors conclude that "These data supports [sic] the feasibility of targeting condensates formed in response to DNA damage to improve chemotherapy-based cancer treatments". To support this conclusion the authors need to show that proliferating non-transformed cells (e.g. primary cell cultures or organoids) can tolerate the combination of AZD2858 + SN-38 (or FOLFIRI) better than colorectal cancer cells. 

We would like to thank the reviewer for this vital suggestion to prove that this combination is effective on tumor cells and not very toxic on healthy cells. We therefore used a healthy colon cell line (CCD841) and tested the efficacy of each treatment alone (FOLFIRI and AZD2858) as well as the combination FOLFIRI+AZD2858. We compared the results obtained in the CCD841 cell line with those obtained in the HCT116 colorectal cancer cell line. The results presented below show not only that each treatment alone is much less effective on CCD841 lines, but also that the combination is not synergistic.

Author response image 2.

Page 19 "This suggests that the combination... arrests the cell cycle before mitosis in a DNAPKsc-dependent manner." I find the remark that this arrest would be DNA-PKcs-dependent too speculative. I suppose that the authors base this claim on reference 55 but if they want to support this claim they need to prove this by adding DNA-PKcs inhibitors to their treated cells. 

Thank you for your thoughtful comment. We agree with the reviewer that claiming the G2/M arrest is DNA-PKcs-dependent without direct experimental evidence is speculative. While we initially based this hypothesis on reference 55, we acknowledge that further experiments, such as the use of DNA-PKcs inhibitors, would be necessary to robustly support this claim.

Given that this observation was intended as a potential explanation for the G2/M arrest observed at 6 and 12 hours of treatment with AZD2858 + SN-38 (compared to SN-38 alone), and considering that exploring this pathway is not the primary focus of our study, we have decided to remove this hypothesis from both the figure and the text to avoid any ambiguity.

We appreciate the reviewer’s input and will consider investigating this pathway in future studies.

(2) When discussing Figure S5B the authors claim that SN-38 + AZD2858 progressively increases the fractions of BrdU positive cells, but this is not supported by statistical analysis.

The fractions are still very small, so I would like to see statistics on these data. Alternatively, the authors could take out this conclusion. 

Thank you for your valuable comment. In response, we have conducted a statistical analysis (Mann-Whitney test) on the data, and the results have been added to Figure S5C for the 6-hour time point and Figure S5D for the 12-hour time point, based on three independent biological replicates. We hope this provides the necessary clarification.

Minor comments: 

- Page 5 Materials and methods - Cell culture. Last sentence "Add in what medium you cultured them" looks like an internal review remark and should probably be removed? 

We apologize for this oversight. The medium has now been specified, and the sentence has been removed.

- The numbers in all the synergy matrices (in white font) are extremely small and virtually unreadable, and visually distracting. I recommend taking these out altogether. 

We believe that the reduction in figure quality may be due to the PDF compression, which affected the resolution of the figures. We are happy to provide high-resolution versions of the figures separately for clarity. If the issue persists even with the higher resolution, we will consider removing the numbers, as suggested.

- The legends of the synergy matrices (for example Fig 1D, 4E, 5, 6) are often extremely small, making it difficult to understand them intuitively. Please enlarge them and label them more clearly, and use larger fonts. In the legend of Figure 5D,E a green matrix indicating % live cells is mentioned but I don't see it. Do they mean the grey matrix? 

We have enlarged the figure legends and will provide high-resolution versions of the figures to ensure all details are clearly readable. Regarding Figure 5D,E: we acknowledge that the color may appear differently (more green or gray) depending on the display or printer settings. To avoid any confusion, we have corrected the legend to specify that the color in question is khaki, rather than green. Moreover, following suggestions of the reviewer #2, these figures have been respectively moved to Figure S6B and S6C.

- Figure S2. Perhaps I misunderstand the PML body experiment but the authors seem to use PML body formation to support their idea that AZD2858 blocks TopBP1 condensate formation and not just any condensate formation. However, if this is the case they would need a proper positive control, i.e. an additional experimental condition in which they do see PLM bodies. 

Arsenic is a well-known positive control for experiments involving PML bodies due to its ability to induce specific responses in PML proteins and modify PML nuclear bodies (NBs) structure and function (Jaffray et al., 2023, JCB ; Zhu et al., 1997, PNAS). Thus, we used Arsenic as a positive control and observed a significant increase in PML NBs vs the other conditions (Kruskal-Wallis test) as indicated below. We thus implemented the results in the corresponding figure S2B and text.

Author response image 3.

PML condensates were tested after 2 h of incubation. AZD2858 : 100nM ; SN-38 : 300nM ; Arsenic : 6µM. ****: p<0.0001 (Kruskal-Wallis test).

- The quantification of the flow cytometry data needs to be clarified. I find it strange that in the figures (for example Figure 3A and 3C) representative examples are shown of apparently 3 replicates, and that the percentages shown in these examples are then the given in the text as the overall numbers; for example on page 18 "...BrdU incorporation increased from 16.11% (SN38 alone) to 41.83% (combination)...". This type of description is done in multiple places in the Results section and is confusing. It would be clearer if the authors show proper quantifications (mean +/- sem) of the percentages of (the relevant) gated populations. Besides, I don't think it make a lot of sense to mention in the text the percentages with 2 decimals behind the comma. This suggests a level of precision that does not seem justified in flow cytometry data. Finally, all flow cytometry plots look visually very busy and all the text is crammed in with really small fonts. Cleaning them up and enlarging the fonts of the remaining text/numbers would really improve the readability of the figures. 

Thank you for your helpful comments. We understand your concern regarding the flow cytometry quantification. Indeed, the percentages presented in the figures are derived from representative replicates, and we acknowledge that this presentation could be confusing. To address this, we have included a table summarizing the data from all replicates to improve readability [Table S2 and S3 in the new version]. Second, we specified in the text that the data are representative biological replicates when needed. Third, we have performed statistical analyses on the three replicates when necessary, as shown in Supplementary Figure S5C-F in the new version. The text has been revised to reflect the correct statistical interpretation.

Regarding the use of two decimal, we are unable to remove them due to limitations in the software (Kaluza) used for flow cytometry analysis. However, we agree that this level of precision may not be warranted, and we have revised the text where appropriate to reduce confusion.

- In Figure 5G the authors show that FOLFIRI + AZD2858 are synergistic in two SN-38-resistant cell lines. They conclude that this combination may overcome drug resistance. But tried to figure out the used FOLFIRI concentrations used in these cell lines and they still seem far higher than the SN-38-sensitive HCT116 cell lines, so I would like to see a bit more nuance in their interpretation. I think overcoming drug resistance is an overstatement, and perhaps alleviating would be a better term 

Thank you for highlighting this important point; we have adjusted the text accordingly.

- The legend in Table S2 refers to Figure 5A-B; this should be Figure 4A-B. 

Thank you, this has been corrected and Table S2 is now moved to Table S4 .

Reviewer #1 (Significance (Required)): 

The finding that AZD2858 block TOPbp1 condensate formation via a pleiotropic effect of this compound is interesting and convincing. To my best knowledge it's a novel finding which is interesting to the potential target audience mentioned below. Their findings that inhibition of TOPbp1 condensation and ATR signaling via AZD2858 may synergize with FOLFIRI therapy in colorectal cancer cells are still very preliminary, because the effects on non-cancerous cells are not tested. 

Researchers involved in early cancer drug discovery and cell biologists studying DNA damage responses in cancer cells seem to me typical audience interested and influenced by this paper. 

I'm a cell biologist studying cell cycle fate decisions, and adaptation of cancer cells & stem cells to (drug-induced) stress. My expertise aligns well with the work presented throughout this paper. 

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

The authors have extended their previous research to develop TOPBP1 as a potential drug target for colorectal cancer by inhibiting its condensation. Utilizing an optogenetic approach, they identified the small molecule AZD2858, which inhibits TOPBP1 condensation and works synergistically with first-line chemotherapy to suppress colorectal cancer cell growth. The authors investigated the mechanism and discovered that disrupting TOPBP1 assembly inhibits the ATR/Chk1 signaling pathway, leading to increased DNA damage and apoptosis, even in drug-resistant colorectal cancer cell lines. Addressing the following concerns would enhance clarity and further in vivo work may improve significance: 

(1) How does the optogenetic method for inducing condensates compare to the DNA damage induction mechanism? 

Optogenetics provides a versatile and precise approach for controlling the condensation of scaffold proteins in both space and time. This method enables us to study the role of biomolecular condensates with minute-scale resolution, separating their formation from potentially confounding upstream events, such as DNA damage, and providing valuable insights into their specific function. Importantly, based on our previous publications on TopBP1 or SLX4 optogenetic condensates, we have substantial evidence indicating that light-induced condensates closely mimic those formed in response to DNA damage:

- Functional similarity: Optogenetic condensates recapitulate endogenous condensates formed upon exposure of the cells of DNA damaging agents, and include most known partner proteins involved in the DNA damage response. It was shown for light induced-TopBP1 and SLX4 condensates (1-3).

- Dynamic reversibility: Optogenetic condensates and DNA damage induced condensates are both dynamic and reversible. They dissolve within 15 minutes of light deactivation or after removal of the damaging agent (1,3).

- Chromatin association: Both optogenetic and DNA damage-induced condensates are bound to chromatin or localized at sites of DNA damage (3).

- Regulation: Both types of condensates are regulated similarly, with their formation triggered by the same signaling pathways. ATR basal activity drives the nucleation of opto-TopBP1 condensates and endogenous TopBP1 structures upon light exposure (1). Likewise, sumoylation modifications regulate the formation of opto-SLX4 condensates and endogenous SLX4 condensates (3).

- Structurally: Using super-resolution imaging by stimulation-emission-depletion (STED) microscopy, we observed that endogenous SLX4 nanocondensates formed globular clusters that were indistinguishable from recombinant light induced SLX4 condensates (1,3).  

(1) Frattini C, Promonet A, Alghoul E, Vidal-Eychenie S, Lamarque M, Blanchard MP, et al. TopBP1 assembles nuclear condensates to switch on ATR signaling. Molecular Cell. 18 mars 2021;81(6):1231-1245.e8. 

(2) Alghoul E, Basbous J, Constantinou A. An optogenetic proximity labeling approach to probe the composition of inducible biomolecular condensates in cultured cells. STAR Protocols. 2021;2(3):100677. 

(3) Alghoul E, Basbous J, Constantinou A. Compartmentalization of the DNA damage response: Mechanisms and functions. DNA Repair. août 2023;128:103524.

(2) Why wasn't the initial screen conducted on the HCT116-SN50 resistant cell line? 

Thank you for raising this important question, which we also considered at the outset of the project. After careful consideration, we decided to use the HCT116 WT cells in order to obtain initial data from an unmodified cell line. It is worth mentioning that HCT116-SN50 cells exhibit slower proliferation compared to WT cells, and they also express an efflux pump capable of pumping out SN38. We were concerned that these factors might interfere with the optogenetic assay, which is why we chose to perform the screen using the WT HCT116 cells.

(3) The labels in Fig. 1D are difficult to recognize. 

This issue was also raised by Reviewer #1. We suspect that the PDF conversion may have reduced the resolution of the figures, so we will provide them separately in high resolution. In addition, we have increased the size of some labels to improve their clarity.

The selected cell image in Fig. 2A for SN-38 seems over-representative; unselected cells appear similar to other groups. Why does AZD2858 itself induce TopBP1 condensates in the plot, yet this is not evident in the images? 

Thank you for your comment; we have updated the figure with a more representative image. We indeed observe that AZD2858 alone induces a slight increase in TopBP1 condensates. However, this increase did not lead to the activation of the ATR/Chk1 signaling pathway, as shown by the Western blot data presented in Fig. 2B. In addition, AZD2858 specifically prevents the formation of TopBP1 condensates induced by SN38 treatment, and the level of TopBP1 condensates does not return to the basal levels observed in untreated cells, but rather to those observed with AZD2858 treatment. During the 2-hour AZD2858 treatment, the progression of replication forks was unaffected (Fig. 3A and 3B). However, when AZD2858 was added alone to the Xenopus egg extracts, there was increased recruitment of TopBP1 to the chromatin (Fig. 2E). This result suggests that AZD2858 alone can induce the assembly of TopBP1 on chromatin to initiate DNA replication (a well-established role of TopBP1), but the number and concentration of TopBP1 molecules did not reach levels sufficient to activate the ATR/Chk1 pathway.

(4) In Fig. 3A, despite the drastic change in the FACS plot shape, the quantifications appear quite similar. 

Thank you for this insightful observation. The gates for the S phase were intentionally set wider to avoid biasing the results and inadvertently excluding the population that incorporates BrdU weakly (but still incorporates it) in the SN-38 only condition. As a result, the percentage of cells within this gate remains similar, even though the overall shape of the FACS plot changes, reflecting a shift in the distribution of BrdU incorporation. This point has now been clarified in the legend of the Figure 3A.

This effect can also be attributed to the relatively short treatment time (2 hours), which captures early changes in DNA synthesis. The effect becomes more pronounced at later time points, as shown in Figure 3C. For example, after 6 hours of treatment, the percentage of BrdU-positive cells increases from 15% with SN-38 alone to 41% with the AZD2858 combination, demonstrating a clearer impact on DNA synthesis. A graph summarizing the statistical analysis has been added to Figure S5C for the 6-hour time point and Figure S5D for the 12-hour time point, based on data from three independent biological replicates.

(5) The results section is imbalanced; Figs. 5 and 6 could be combined into one figure. 

We have combined Figures 5 and 6 into a single figure to optimize the presentation of results. To avoid overloading the new figure, some of the data have been moved to supplementary figures, ensuring the main figure remains clear and focused.

(6) An in vivo study is anticipated to assess the drug's efficacy. 

Although AZD2858 was developed a few years ago, there is a limited amount of in vivo data available, which led us to consider potential issues related to the drug's biodistribution or its pharmacokinetics (PK). Despite these concerns, we proceeded with preliminary in vivo studies, testing various diluents and injection routes for AZD2858. However, we observed that the compound was not effective in vivo. Given the strong synergistic effects observed in vitro, we concluded that AZD2858 was likely not being distributed properly in the mice. As a result, we have decided to conduct a more detailed investigation into the pharmacokinetics (PK), pharmacodynamics (PD), and absorption, distribution, metabolism, and excretion (ADME) of AZD2858 to better understand its in vivo behavior and efficacy. Therefore, the in vivo evaluation of AZD2858 will be addressed in a separate study specifically focused on this aspect.

Reviewer #2 (Significance (Required)): 

Addressing the stated concerns would enhance clarity and further in vivo work may improve significance. 

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

Summary 

In 2021 (PMID: 33503405) and 2024 (PMID: 38578830) Constantinou and colleagues published two elegant papers in which they demonstrated that the Topbp1 checkpoint adaptor protein could assemble into mesoscale phase-separated condensates that were essential to amplify activation of the PIKK, ATR, and its downstream effector kinase, Chk1, during DNA damage signalling. A key tool that made these studies possible was the use of a chimeric Topbp1 protein bearing a cryptochrome domain, Cry2, which triggered condensation of the chimeric Topbp1 protein, and thus activation of ATR and Chk1, in response to irradiation with blue light without the myriad complications associated with actually exposing cells to DNA damage. 

In this current report Morano and co-workers utilise the same optogenetic Topbp1 system to investigate a different question, namely whether Topbp1 phase-condensation can be inhibited pharmacologically to manipulate downstream ATR-Chk1 signalling. This is of interest, as the therapeutic potential of the ATR-Chk1 pathway is an area of active investigation, albeit generally using more conventional kinase inhibitor approaches. 

The starting point is a high throughput screen of 4730 existing or candidate small molecule anticancer drugs for compounds capable of inhibiting the condensation of the Topbp1-Cry2mCherry reporter molecule in vivo. A surprisingly large number of putative hits (>300) were recorded, from which 131 of the most potent were selected for secondary screening using activation of Chk1 in response to DNA damage induced by SN-38, a topoisomerase inhibitor, as a surrogate marker for Topbp1 condensation. From this the 10 most potent compounds were tested for interactions with a clinically used combination of SN-38 and 5-FU (FOLFIRI) in terms of cytotoxicity in HCT116 cells. The compound that synergised most potently with FOLFIRI, the GSK3-beta inhibitor drug AZD2858, was selected for all subsequent experiments. 

AZD2858 is shown to suppress the formation of Topbp1 (endogenous) condensates in cells exposed to SN-38, and to inhibit activation of Chk1 without interfering with activation of ATM or other endpoints of damage signalling such as formation of gamma-H2AX or activation of Chk2 (generally considered to be downstream of ATM). AZD2858 therefore seems to selectively inhibit the Topbp1-ATR-Chk1 pathway without interfering with parallel branches of the DNA damage signalling system, consistent with Topbp1 condensation being the primary target. Importantly, neither siRNA depletion of GSK3-beta, or other GSK3-beta inhibitors were able to recapitulate this effect, suggesting it was a specific non-canonical effect of AZD2858 and not a consequence of GSK3-beta inhibition per se. 

To understand the basis for synergism between AZD2858 and SN-38 in terms of cell killing, the effect of AZD2858 on the replication checkpoint was assessed. This is a response, mediated via ATR-Chk1, that modulates replication origin firing and fork progression in S-phase cell under conditions of DNA damage or when replication is impeded. SN-38 treatment of HCT116 cells markedly suppresses DNA replication, however this was partially reversed by co-treatment with AZD2858, consistent with the failure to activate ATR-Chk1 conferring a defect in replication checkpoint function. 

Figures 4 and 5 demonstrate that AZD2858 can markedly enhance the cytotoxic and cytostatic effects of SN-38 and FOLFIRI through a combination of increased apoptosis and growth arrest according to dosage and treatment conditions. Figure 6 extends this analysis to cells cultured as spheroids, sometimes considered to better represent tumor responses compared to single cell cultures. 

Major comments 

Most of the data presented is of good technical quality and supports the conclusions drawn. There are however a small number of instances where this is not true; ie where the data are of insufficient technical quality, or where the description or interpretation of the results is at variance with the data which is presented. Some examples: 

(1) Fig.2E - the claim that "we observed an increase in RPA, Topb1 and Pol-epsilon levels when CPT and AZD2858 were added together" do not seem to be justified by the data provided. It is also unclear what the purpose/ significance of this experiment is. 

Thank you for pointing out the contradiction in Figure 2E. Upon review, we identified an error in the labeling of conditions (CPT and AZD2858 were inadvertently swapped). The corrected figure now clearly shows that, at the 60-minute timepoint after starting replication, the combination of

CPT and AZD2858 results in a greater accumulation of TopBP1, Pol ε, and RPA on chromatin compared to CPT alone. We have revised the sentence to: "Our data demonstrate that combining CPT and AZD2858 earlier enhances the accumulation of replication-related factors (RPA, TopBP1, and Pol ε) on chromatin compared to CPT treatment alone, particularly visible at the 60minute after starting replication."

The significance of this experiment lies in its connection to the earlier observation that AZD2858 restores BrdU incorporation when combined with SN-38, as shown in flow cytometry data (Figure 3A). At a molecular level, this was further supported by DNA fiber assays, which revealed that replication tracks (CldU tracts) were longer in the combination treatment compared to SN-38 alone (Figure 3B).

To strengthen and validate these findings, we chose to employ the Xenopus egg extract system for several reasons. This model provides a highly controlled environment where DNA replication occurs without confounding effects from transcription or translation. Moreover, replication is limited to a single round, offering a unique opportunity to specifically interrogate replication mechanisms. These attributes make the Xenopus model an ideal system to confirm that AZD2858 facilitates replication recovery in the presence of replication stress induced by agents like CPT. This will lead, in longer treatment, to accumulation of DNA damage and apoptosis (Figure 3D-E and Figure 4A-D)

(2) Figs. 3 A and C certainly show that the SN-38-mediated suppression of DNA synthesis is modified and partially alleviated by co-treatment with AZD2858. The statement however that "prolonged co-incubation with AZD2858 for 6 and 12 hours effectively abolished the SN-38 induced S-phase checkpoint" is clearly misleading. If this were true, then the BrdU incorporation profiles of the respective samples would be similar or identical to control, which clearly they are not. Clearly AZD2858 is affecting the imposition of the S-phase checkpoint in some way, but not "abolishing" it. 

We appreciate the reviewer’s detailed observations regarding Figures 3A and 3C and the phrasing in our manuscript. We agree that the term "abolished" is not precise in describing the effects of AZD2858 on the SN-38-induced S-phase checkpoint.

To clarify: our data indicate that co-treatment with AZD2858 modifies and partially alleviates the SN-38-induced suppression of DNA synthesis, as demonstrated by increased BrdU incorporation relative to SN-38 treatment alone. However, as the reviewer correctly points out, the BrdU incorporation profiles of the co-treated samples do not fully return to control non treated cells levels. This suggests that while AZD2858 significantly mitigates the S-phase checkpoint, it does not completely abolish it.

We have revised the statement in the manuscript to better reflect these findings, as follows: "Prolonged co-incubation with AZD2858 for 6 and 12 hours significantly alleviated the SN-38induced S-phase checkpoint, as evidenced by the partially increased BrdU incorporation. However, the population of co-treated cells is heterogeneous: some cells exhibit BrdU incorporation levels similar to those of untreated control cells, while others incorporate BrdU at levels comparable to cells treated with SN-38 alone. This indicates that AZD2858 does not fully restore DNA synthesis to control levels across the entire cell population."

This revised phrasing aligns with the data presented and acknowledges the partial recovery of DNA synthesis observed. Thank you for bringing this to our attention and helping us improve the accuracy of our conclusions.

(3) Fig. 3 E. The western blots of pDNA-PKcs (S2056) and total DNA-PKcs are really not interpretable. It is possible to sympathise that these reagents are probably extremely difficult to work with and obtain clear results, however uninterpretable results are not acceptable. 

We agree that the data presented in the Fig3E are difficult to interpret. As noted by Reviewer 1, we recognize the challenge of obtaining clear and reliable results with these specific reagents. Based on this feedback, and to ensure the robustness of our conclusions, we have decided to exclude these specifics blots from the revised manuscript.

We believe that this adjustment will enhance the clarity and reliability of the manuscript while focusing on the other, more interpretable data presented. Thank you for pointing this out, and we appreciate your understanding.

(4) Fig. 3D. This is a puzzling image. Described as a PFGE assay, it presumably depicts an agarose gel, with intact genomic DNA at the top and a discrete band below representing fragmented genomic DNA. This is a little surprising, as fragmented genomic DNA does not usually appear as a specific band but as a heterogenous population or "smear". Nevertheless, even if one accepts this premise, it is unclear what is meant by "DSBs remained elevated after the combined treatment" when the intensity of this band is equivalent for both SN-38 and SN-38 + AZD2858 treatments. 

We thank the reviewer for his insightful comments regarding the PFGE results in Figure 3D. We agree that the appearance of a discrete band, rather than a heterogeneous smear, is atypical for fragmented genomic DNA in this assay. However, by enhancing the signal intensity (as shown below), the expected smear becomes more appreciable.

Author response image 4.

Regarding the interpretation of the band intensities, we agree that the signals for SN-38 and SN38 + AZD2858 appear similar under these specific conditions. At the relatively high concentration of SN-38 used in this experiment (300 nM), it is indeed challenging to observe a more pronounced effect on DNA breaks. This is why we proposed the "DSBs remained elevated after the combined treatment" because the band intensity of SN-38 single agent treated cells or combined with AZD2858 is comparable. However, we note a slightly more intense γH2AX signal over time when AZD2858 is combined with SN-38 compared to SN-38 alone (Figure 3E). Furthermore, under lower, sub-optimal doses of SN-38 and over extended incubation treatment (48h), we observe a clearer increase in fragmented DNA bands, as demonstrated in Figure 4D.

Minor comments 

(1) Fig. 1. A surprisingly large number of compounds scored positive in the primary screen for inhibition of Topbp1 condensation (>300). Of the 131 of these selected for secondary screening using Chk1 activation (S345 phosphorylation) as a readout approximately 2/3 were negative, implying that a majority of the tested compounds inhibited Topbp1 condensation but not Chk1 activation. What could explain that?

Thank you for this thoughtful comment. The discrepancy between the large number of compounds scoring positive for TopBP1 condensation inhibition and the smaller number inhibiting Chk1 activation (S345 phosphorylation) could be attributed to several factors:

• Different cell lines and induction methods: The initial screen was conducted in HEK293 TrexFlpin cells overexpressing optoTopBP1, while the secondary screen used HCT116 cells. In addition, the methods used to induce the respective pathways were distinct: in the primary screen, we employed a blue light induction of opto-TopBP1 condensates, whereas in the secondary screen, we used an SN-38 treatment to induce DNA replication stress and activate the Chk1 pathway. These differences could account for the varying responses observed in the two screens.

• The compounds that inhibited TopBP1 condensation might not fully block Chk1 activation. While they disrupt TopBP1 condensation, they may still allow for partial activation of Chk1 or Chk1 activation through alternative mechanisms. For instance, Chk1 activation could be mediated by other signaling pathways or molecules, such as ETAA1, a known Chk1 activator (1). Thus, TopBP1 condensation inhibition does not necessarily translate to complete inhibition of Chk1 activation, especially if ETAA1 is employed by cells as a rescue activator.

• Some compounds may affect chromosome dynamics, potentially generating mechanical forces or torsional stress that could activate the ATR/Chk1 pathway independently of TopBP1

(2).

These factors suggest that while the compounds effectively disrupt TopBP1 condensation, they may not always fully inhibit the downstream Chk1 activation, pointing to the complexity of the DNA damage response pathways. 

(1) Bass, T. E. et al. ETAA1 acts at stalled replication forks to maintain genome integrity. Nat Cell Biol 18, 1185–1195 (2016).

(2) Kumar, A. et al. ATR Mediates a Checkpoint at the Nuclear Envelope in Response to Mechanical Stress. Cell 158, 633–646 (2014).

(2) Fig. 2D. The protein-protein interaction assay shown demonstrates that AZD2858 ablates the light-induced auto-interaction between exogenous opto-Topbp1 molecules and ATR plus or minus SN-38, but clearly endogenous Topbp1 molecules do not participate. Why is this? 

The biotin proximity labeling assay was conducted without exposing cells to light, using a TurboID module fused to TopBP1-mCherry-CRY2. Stable cell lines were then generated in HEK293 TrexFlpIn cells, where endogenous TopBP1 is still expressed. Upon adding doxycycline, the recombinant TurboID-TopBP1-mCherry-Cry2 (opto-TopBP1) is induced at levels comparable to endogenous TopBP1 (Fig 2D).

Since the opto-TopBP1 construct exhibits behavior similar to that of endogenous TopBP1 (1), we used it to investigate whether TopBP1 self-assembly and its interaction with ATR are influenced by AZD2858 alone or in combination with SN38. Our results show that treatment with SN38 increases the proximity between opto-TopBP1 and the endogenous TopBP1 (not fused to TurboID). However, AZD2858, either alone or in combination with SN38, disrupts the selfassembly of recombinant TopBP1 with itself as well as its interaction with endogenous TopBP1.

(1) Frattini C, Promonet A, Alghoul E, Vidal-Eychenie S, Lamarque M, Blanchard MP, et al. TopBP1 assembles nuclear condensates to switch on ATR signaling. Molecular Cell. 18 mars 2021;81(6):1231-1245.e8.

Reviewer #3 (Significance (Required)): 

Significance 

Liquid phase separation of protein complexes is increasingly recognised as a fundamental mechanism in signal transduction and other cellular processes. One recent and important example was that of Topbp1, whose condensation in response to DNA damage is required for efficient activation of the ATR-Chk1 pathway. The current study asks a related but distinct question; can protein condensation be targeted by drugs to manipulate signalling pathways which in the main rely on protein kinase cascades? 

Here, the authors identify an inhibitor of GSK3-beta as a novel inhibitor of DNA damage-induced Topbp1 condensation and thus of ATR-Chk1 signalling. 

This work will be of interest to researchers in the fields of DNA damage signalling, biophysics of protein condensation, and cancer chemotherapy.

Author response:

Public Reviews:

Reviewer #1 (Public review):

In this paper by Brickwedde et al., the authors observe an increase in posterior alpha when anticipating auditory as opposed to visual targets. The authors also observe an enhancement in both visual and auditory steady-state sensory evoked potentials in anticipation of auditory targets, in correlation with enhanced occipital alpha. The authors conclude that alpha does not reflect inhibition of early sensory processing, but rather orchestrates signal transmission to later stages of the sensory processing stream. However, there are several major concerns that need to be addressed in order to draw this conclusion.

First, I am not convinced that the frequency tagging method and the associated analyses are adequate for dissociating visual vs auditory steady-state sensory evoked potentials.

Second, if the authors want to propose a general revision for the function of alpha, it would be important to show that alpha effects in the visual cortex for visual perception are analogous to alpha effects in the auditory cortex for auditory perception.

Third, the authors propose an alternative function for alpha - that alpha orchestrates signal transmission to later stages of the sensory processing stream. However, the supporting evidence for this alternative function is lacking. I will elaborate on these major concerns below.

(1) Potential bleed-over across frequencies in the spectral domain is a major concern for all of the results in this paper. The fact that alpha power, 36Hz and 40Hz frequency-tagged amplitude and 4Hz intermodulation frequency power is generally correlated with one another amplifies this concern. The authors are attaching specific meaning to each of these frequencies, but perhaps there is simply a broadband increase in neural activity when anticipating an auditory target compared to a visual target?

We appreciate the reviewer’s insightful comment regarding the potential bleed-over across frequencies in the spectral domain. We fully acknowledge that the trade-off between temporal and frequency resolution is a challenge, particularly given the proximity of the frequencies we are examining.

To address this concern, we performed additional analyses to investigate whether there is indeed a broadband increase in neural activity when anticipating an auditory target as compared to a visual target, as opposed to distinct frequency-specific effects. Our results show that the bleed-over between frequencies is minimal and does not significantly affect our findings. Specifically, we repeated the analyses using the same filter and processing steps for the 44 Hz frequency. At this frequency, we did not observe any significant differences between conditions.

These findings suggest that the effects we report are indeed specific to the 40 Hz frequency band and not due to a general broadband increase in neural activity. We hope this addresses the reviewer’s concern and strengthens the validity of our frequency-specific results.

Author response image 1.

Illustration of bleeding over effects over a span of 4 Hz. A, 40 Hz frequency-tagging data over the significant cluster differing between when expecting an auditory versus a visual target (identical to Fig. 9 in the manuscript). B, 44 Hz signal over the same cluster chosen for A. The analysis was identical with the analysis performed in  A, apart from the frequency for the band-pass filter.

We do, however, not specifically argue against the possibility of a broadband increase when anticipating an auditory compared to a visual target. But even a broadband-increase would directly contradict the alpha inhibition hypothesis, which poses that an increase in alpha completely disengages the whole cortex. We will clarify this point in the revised manuscript.

(2) Moreover, 36Hz visual and 40Hz auditory signals are expected to be filtered in the neocortex. Applying standard filters and Hilbert transform to estimate sensory evoked potentials appears to rely on huge assumptions that are not fully substantiated in this paper. In Figure 4, 36Hz "visual" and 40Hz "auditory" signals seem largely indistinguishable from one another, suggesting that the analysis failed to fully demix these signals.

We appreciate the reviewer’s insightful concern regarding the filtering and demixing of the 36 Hz visual and 40 Hz auditory signals, and we share the same reservations about the reliance on standard filters and the Hilbert transform method.

To address this, we would like to draw attention to Author response image 1, which demonstrates that a 4 Hz difference is sufficient to effectively demix the signals using our chosen filtering and Hilbert transform approach. We believe that the reason the 36 Hz visual and 40 Hz auditory signals show similar topographies lies not in incomplete demixing but rather in the possibility that this condition difference reflects sensory integration, rather than signal contamination.

This interpretation is further supported by our findings with the intermodulation frequency at 4 Hz, which also suggests cross-modal integration. Furthermore, source localization analysis revealed that the strongest condition differences were observed in the precuneus, an area frequently associated with sensory integration processes. We will expand on this in the discussion section to better clarify this point.

(3) The asymmetric results in the visual and auditory modalities preclude a modality-general conclusion about the function of alpha. However, much of the language seems to generalize across sensory modalities (e.g., use of the term 'sensory' rather than 'visual').

We thank the reviewer for pointing this out and agree that in some cases we have not made a good enough distinction between visual and sensory. We will make sure, that when using ‘sensory’, we either describe overall theories, which are not visual-exclusive or refer to the possibility of a broad sensory increase. However, when directly discussing our results and the interpretation thereof, we will now use ‘visual’ in the revised manuscript.

(4) In this vein, some of the conclusions would be far more convincing if there was at least a trend towards symmetry in source-localized analyses of MEG signals. For example, how does alpha power in the primary auditory cortex (A1) compare when anticipating auditory vs visual target? What do the frequency-tagged visual and auditory responses look like when just looking at the primary visual cortex (V1) or A1?

We thank the reviewer for this important suggestion and have added a virtual channel analysis. We were however, not interested in alpha power in primary auditory cortex, as we were specifically interested in the posterior alpha, which is usually increased when expecting an auditory compared to a visual target (and used to be interpreted as a blanket inhibition of the visual cortex). We will improve upon the clarity concerning this point in the manuscript.

We have however, followed the reviewer’s suggestion of a virtual channel analysis, showing that the condition differences are not observable in primary visual cortex for the 36 Hz visual signal and in primary auditory cortex for the 40 Hz auditory signal. Our data clearly shows that there is an alpha condition difference in V1, while there no condition difference for 36 Hz in V1 and for 40 Hz in Heschl’s Gyrus (see Author response image 2).

Author response image 2.

Virtual channels for V1 and Helschl’s gyrus. A, alpha power for the virtual channel created in V1 (Calcerine_L and Calcerine_R from AAL atlas; Tzourio-Mazoyer et al., 2002, NeuroImage). A cluster permutation analysis over time (between -2 and 0) revealed a significant condition difference between ~ -2 and -1.7 s (p = 0.0449). B, 36 Hz frequency-tagging signal for the virtual channel created in V1 (equivalent to the procedure in A). The same cluster permutation as performed in A revealed no significant condition differences. C, 40 Hz frequency-tagging signal for the virtual channel created in Heschl’s gryrus (Heschl_L and Heschl_R from AAL atlas; Tzourio-Mazoyer et al., 2002, NeuroImage). The same cluster permutation as performed in A revealed no significant condition differences.

(5) Blinking would have a huge impact on the subject's ability to ignore the visual distractor. The best thing to do would be to exclude from analysis all trials where the subjects blinked during the cue-to-target interval. The authors mention that in the MEG experiment, "To remove blinks, trials with very large eye-movements (> 10 degrees of visual angle) were removed from the data (See supplement Fig. 5)." This sentence needs to be clarified since eye-movements cannot be measured during blinking. In addition, it seems possible to remove putative blink trials from EEG experiments as well, since blinks can be detected in the EEG signals.

We thank the reviewer for mentioning that we were making this point confusing. From the MEG-data, we removed eyeblinks using ICA. Alone for the supplementary Fig. 5 analysis, we used the eye-tracking data to confirm that participants were in fact fixating the centre of the screen. For this analysis, we removed trials with blinks (which can be seen in the eye-tracker as huge amplitude movements or as large eye-movements in degrees of visual angle; see Author response image 3 below to show a blink in the MEG data and the according eye-tracker data in degrees of visual angle). We will clarify this in the methods section.

As for the concern closed eyes to ignore visual distractors, in both experiments we can observe highly significant distractor cost in accuracy for visual distractors, which we hope will convince the reviewer that our visual distractors were working as intended.

Author response image 3.

Illustration of eye-tracker data for a trial without and a trial with a blink. All data points recorded during this trial are plottet. A, ICA component 1, which reflects blinks and its according data trace in a trial. No blink is visible. B, eye-tracker data transformed into degrees of visual angle for the trial depicted in A. C, ICA component 1, which reflects blinks and its according data trace in a trial. A clear blink is visible. D, eye-tracker data transformed into degrees of visual angle for the trial depicted in C.

(6) It would be interesting to examine the neutral cue trials in this task. For example, comparing auditory vs visual vs neutral cue conditions would be indicative of whether alpha was actively recruited or actively suppressed. In addition, comparing spectral activity during cue-to-target period on neutral-cue auditory correct vs incorrect trials should mimic the comparison of auditory-cue vs visual-cue trials. Likewise, neutral-cue visual correct vs incorrect trials should mimic the attention-related differences in visual-cue vs auditory-cue trials.

We thank the reviewer for this suggestion. We have analysed the neutral cue trials in the EEG dataset (see suppl. Fig. 1) and will expand this figure to show all conditions. There were no significant differences to auditory or visual cues, but descriptively alpha power was higher for neutral cues compared to visual cues and lower for neutral cues compared to auditory cues. While this may suggest that for visual trials alpha is actively suppressed and for auditory trials actively recruited, we do not feel comfortable to make this claim, as the neutral condition may not reflect a completely neutral state. The neutral task can still be difficult, especially because of the uncertainty of the target modality.

As for the analysis of incorrect versus correct trials, we love the idea, but unfortunately the accuracy rate was quite high so that the number of incorrect trials would not be sufficient to perform a reliable analysis.

(7) In the abstract, the authors state that "This implies that alpha modulation does not solely regulate 'gain control' in early sensory areas but rather orchestrates signal transmission to later stages of the processing stream." However, I don't see any supporting evidence for the latter claim, that alpha orchestrates signal transmission to later stages of the processing stream. If the authors are claiming an alternative function to alpha, this claim should be strongly substantiated.

We thank the reviewer for pointing out, that we have not sufficiently explained our case. The first point refers to gain control akin to the alpha inhibition hypothesis, which claims that increases in alpha disengage a whole cortical area. Since we have confirmed the alpha increase in our data to originate from primary visual cortex through source analysis, this should lead to decreased visual processing. The increase in 36 Hz visual processing therefore directly contradicts the alpha inhibition hypothesis. We propose an alternative explanation for the functionality of alpha activity in this task. Through pulsed inhibition, information packages of relevant visual information could be transmitted down the processing stream, thereby enhancing relevant visual signal transmission. We believe the fact that the enhanced visual 36 Hz signal we found correlated with visual alpha power on a trial-by-trial basis, and did not originate from primary visual cortex, but from areas known for sensory integration supports our claim.

We will make this point clearer in our revised manuscript.

Reviewer #2 (Public review):

Brickwedde et al. investigate the role of alpha oscillations in allocating intermodal attention. A first EEG study is followed up with a MEG study that largely replicates the pattern of results (with small to be expected differences). They conclude that a brief increase in the amplitude of auditory and visual stimulus-driven continuous (steady-state) brain responses prior to the presentation of an auditory - but not visual - target speaks to the modulating role of alpha that leads them to revise a prevalent model of gating-by-inhibition.

Overall, this is an interesting study on a timely question, conducted with methods and analysis that are state-of-the-art. I am particularly impressed by the author's decision to replicate the earlier EEG experiment in MEG following the reviewer's comments on the original submission. Evidently, great care was taken to accommodate the reviewer's suggestions.

We thank the reviewer for the positive feedback and expression of interest in the topic of our manuscript.

Nevertheless, I am struggling with the report for two main reasons: It is difficult to follow the rationale of the study, due to structural issues with the narrative and missing information or justifications for design and analysis decisions, and I am not convinced that the evidence is strong, or even relevant enough for revising the mentioned alpha inhibition theory. Both points are detailed further below.

We thank the reviewer for raising this important point. We will revise our introduction and results in line with the reviewer’s suggestions, hoping that our rationale will then be easier to follow and that our evidence will be more convincing.

Strength/relevance of evidence for model revision: The main argument rests on 1) a rather sustained alpha effect following the modality cue, 2) a rather transient effect on steady-state responses just before the expected presentation of a stimulus, and 3) a correlation between those two. Wouldn't the authors expect a sustained effect on sensory processing, as measured by steady-state amplitude irrespective of which of the scenarios described in Figure 1A (original vs revised alpha inhibition theory) applies? Also, doesn't this speak to the role of expectation effects due to consistent stimulus timing? An alternative explanation for the results may look like this: Modality-general increased steady-state responses prior to the expected audio stimulus onset are due to increased attention/vigilance. This effect may be exclusive (or more pronounced) in the attend-audio condition due to higher precision in temporal processing in the auditory sense or, vice versa, too smeared in time due to the inferior temporal resolution of visual processing for the attend-vision condition to be picked up consistently. As expectation effects will build up over the course of the experiment, i.e., while the participant is learning about the consistent stimulus timing, the correlation with alpha power may then be explained by a similar but potentially unrelated increase in alpha power over time.

We thank the reviewer for raising these insightful questions and suggestions.

It is true that our argument rests on a rather sustained alpha effect and a rather transient effect on steady-state responses and a correlation between the two. However, this connection would not be expected under the alpha inhibition hypothesis, which states that alpha activity would inhibit a whole cortical area (when irrelevant to the task), exerting “gain control”. This notion directly contradicts our results of the “irrelevant” visual information a) being transmitted at all and b) increasing.

However, it has been shown on many occasions that alpha activity exerts pulsed inhibition, so we proposed an alternative theory of an involvement in signal transmission. In this case, the cyclic inhibition would serve as an ordering system, which only allows for high-priority information to pass, resulting in higher signa-to-noise. We do not make a claim about how fast or when these signals are transmitted in relation to alpha power. For instance, it could be that alpha power increases as a preparatory state even before signal is actually transmitted.  Zhigalov (2020 Hum. Brain M.) has shown that in V1, frequency-tagging responses were up-and down regulated with attention – independent of alpha activity.

But we do believe that the fact that visual alpha power correlates on a trial-by-trial level with visual 36 Hz frequency-tagging increases and (a relationship which has not been found in V1, see Zhigalov 2020, Hum. Brain Mapp.) suggest a strong connection. Furthermore, the fact that the alpha modulation originates from early visual areas and occurs prior to any frequency-tagging changes, while the increase in frequency-tagging can be observed in areas which are later in the processing stream (such as the precuneus) is strongly indicative for an involvement of alpha power in the transmission of this signal. We cannot fully exclude alternative accounts and mechanisms which effect both alpha power and frequency-tagging responses. 

We do believe that the alternative account described by the reviewer does not contradict our theory, as we do believe that the alpha power modulation may reflect an expectation effect (and the idea that it could be related to the resolution of auditory versus visual processing is very interesting!). It is also possible that this expectation is, as the reviewer suggests, related to attention/vigilance and might result in a modality-general signal increase. And indeed, we can observe an increase in the frequency-tagging response in sensory integration areas. Accordingly, we believe that the alternative explanation provided by the reviewer contradicts the alpha inhibition hypothesis, but not necessarily our alternative theory.

We will revise the discussion, which we hope will make our case stronger and easier to follow. Additionally, we will mention the possibility for alternative explanations as well as the possibility, that alpha networks fulfil different roles in different locations/task environments.

Structural issues with the narrative and missing information: Here, I am mostly concerned with how this makes the research difficult to access for the reader. I list the major points below:

In the introduction the authors pit the original idea about alpha's role in gating against some recent contradictory results. If it's the aim of the study to provide evidence for either/or, predictions for the results from each perspective are missing. Also, it remains unclear how this relates to the distinction between original vs revised alpha inhibition theory (Fig. 1A). Relatedly if this revision is an outcome rather than a postulation for this study, it shouldn't be featured in the first figure.

We agree with the reviewer that we have not sufficiently clarified our goal as well as how different functionalities of alpha oscillations would lead to different outcomes. We will revise the introduction and restructure the results and hope that it will be easier to follow.

The analysis of the intermodulation frequency makes a surprise entrance at the end of the Results section without an introduction as to its relevance for the study. This is provided only in the discussion, but with reference to multisensory integration, whereas the main focus of the study is focussed attention on one sense. (Relatedly, the reference to "theta oscillations" in this sections seems unclear without a reference to the overlapping frequency range, and potentially more explanation.) Overall, if there's no immediate relevance to this analysis, I would suggest removing it.

We thank the reviewer for pointing this out and will add information about this frequency to the introduction part. We believe that the intermodulation frequency analysis is important, as it potentially supports the notion that condition differences in the visual-frequency tagging response are related to downstream processing rather than overall visual information processing in V1. We would therefore prefer to leave this analysis in the manuscript.

Reviewer #3 (Public review):

Brickwedde et al. attempt to clarify the role of alpha in sensory gain modulation by exploring the relationship between attention-related changes in alpha and attention-related changes in sensory-evoked responses, which surprisingly few studies have examined given the prevalence of the alpha inhibition hypothesis. The authors use robust methods and provide novel evidence that alpha likely exhibits inhibitory control over later processing, as opposed to early sensory processing, by providing source-localization data in a cross-modal attention task.

This paper seems very strong, particularly given that the follow-up MEG study both (a) clarifies the task design and separates the effect of distractor stimuli into other experimental blocks, and (b) provides source-localization data to more concretely address whether alpha inhibition is occurring at or after the level of sensory processing, and (c) replicates most of the EEG study's key findings.

We are very grateful to the reviewer for their positive feedback and evaluation of our work.

There are some points that would be helpful to address to bolster the paper. First, the introduction would benefit from a somewhat deeper review of the literature, not just reviewing when the effects of alpha seem to occur, but also addressing how the effect can change depending on task and stimulus design (see review by Morrow, Elias & Samaha (2023).

We thank the reviewer for this suggestion and agree. We will add a paragraph to the introduction which refers to missing correlation studies and the impact of task design.

Additionally, the discussion could benefit from more cautionary language around the revision of the alpha inhibition account. For example, it would be helpful to address some of the possible discrepancies between alpha and SSEP measures in terms of temporal specificity, SNR, etc. (see Peylo, Hilla, & Sauseng, 2021). The authors do a good job speculating as to why they found differing results from previous cross-modal attention studies, but I'm also curious whether the authors think that alpha inhibition/modulation of sensory signals would have been different had the distractors been within the same modality or whether the cues indicated target location, rather than just modality, as has been the case in so much prior work?

We thank the reviewer for suggesting these interesting discussion points and will include a paragraph in our discussion which goes deeper into these topics.

Overall, the analyses and discussion are quite comprehensive, and I believe this paper to be an excellent contribution to the alpha-inhibition literature.

Author Response

Reviewer #1 (Public Review):

The manuscript, "A versatile high-throughput assay based on 3D ring-shaped cardiac tissues generated from human induced pluripotent stem cell-derived cardiomyocytes" developed a unique culture platform with PEG hydrogel that facilitates the in-situ measurement of contractile dynamics of the engineered cardiac rings. The authors optimized the tissue seeding conditions, demonstrated tissue morphology with expressions of cardiac and fibroblast markers, mathematically modeled the equation to derive contractile forces and other parameters based on imaging analysis, and ended by testing several compounds with known cardiac responses.

To strengthen the paper, the following comments should be considered:

1) This paper provided an intriguing platform that creates miniature cardiac rings with merely thousands of CMs per tissue in a 96-well plate format. The shape of the ring and the squeezing motion can recapitulate the contraction of the cardiac chamber to a certain degree. However, Thavandiran et al (PNAS 2013) created a larger version of the cardiac ring and found the electrical propagation revealed spontaneous infinite loop-like cycles of activation propagation traversing the ring. This model was used to mimic a reentrant wave during arrhythmia. Therefore, it presents great concerns if a large number of cardiac tissues experience arrhythmia by geometry-induced re-entry current and cannot be used as a healthy tissue model. It would be interesting to see the impulse propagation/calcium transient on these miniature cardiac rings and evaluate the % of arrhythmia occurrence.

The size is a key factor impacting the electrical propagation within the generated tissues. Our ring-shaped cardiac tissues have a diameter of 360µm, which is largely smaller than other tissues proposed so far, including in Thavandiran et al (PNAS 2013) where circular tissues had a reported size > 1mm. As shown in Figure 4E (and highlighted below in Author response image 1), tissues under basal conditions display regular beating rates without spontaneous arrhythmias. Videos also show that the tissue contraction is homogeneous around the pillar, suggesting that the smaller size favors the electrical propagation and limits the occurrence of spontaneous reentrant waves. Optical mapping measurements will be performed in the future to assess the occurrence of reentrant waves.

**Author response image 1. **

Poincaré plot showing the plots between successive RR intervals (Data from Figure 4E in basal conditions). Linear regression with 95% confidence interval indicates identity.

2) The platform can produce 21 cardiac rings per well in 96-well plates. The throughput has been the highest among competing platforms. The resulting tissues have good sarcomere striation due to the strain from the pillars. Now the emerging questions are culture longevity and reproducibility among tissues. According to Figure 1E, there was uneven ring formation around the pillar, which leads to the tissue thinning and breaking off. There is only 50% survival after 20 days of culture in the optimized seeding group. Is there any way to improve it? The tissues had two compartments, cardiac and fibroblast-rich regions, where fibroblasts are responsible for maintaining the attachment to the glass slides. Do the cardiac rings detach from the glass slides and roll up? The SD of the force measurement is a quarter of the value, which is not ideal with such a high replicate number. As the platform utilizes imaging analysis to derive contractile dynamics, calibration should be done based on the angle and the distance of the camera lens to the individual tissues to reduce the error. On the other hand, how reproducible of the pillars? It is highly recommended to mechanically evaluate the consistency of the hydrogel-based pillars across different wells and within the wells to understand the variance. Figure 2B reports the early results obtained as the system was tested and developed. Since then, we have tested different iPSC lines and confirm that the overall yield is higher (up to 20 tissues at D14 for some cell lines), however dependent of cell lines.

The tissues do not detach from the glass slides. It is very rare to see tissues roll up on the central pillar. As shown in Figure 1B, the pillars have a specific shape to avoid tissues to roll up as they develop and contract.

3) Does the platform allow the observation of non-synchronized beating when testing with compounds? This can be extremely important as the intended applications of this platform are drug testing and cardiac disease modeling. The author should elaborate on the method in the manuscript and explain the obtained results in detail. The arrhythmogenic effect of a drug can be derived from the regularity of the beat-to-beat time. Indeed, we show that dofetilide increases the variability in the beat-to-beat time by plotting for each beat, the beat-to-beat time with the next beat as a function of the beat-to-beat time with the previous beat.

4) The results of drug testing are interesting. Isoproterenol is typically causing positive chronotropic and positive inotropic responses, where inotropic responses are difficult to obtain due to low tissue maturity. It is inconsistent with other reported results that cardiac rings do not exhibit increased beating frequency, but slightly increased forces only. Zhao et al were using electrical pacing at a defined rate during force measurement, whereas the ring constructs are not.

We agree. The difference in the response to isoproterenol with previous papers may be explained by different incubation timing with the drug. In our case, the tissues were incubated for 5 minutes at 37•C before being recorded.

Overall, the manuscript is well written and the designed platform presented the unique advantages of high throughput cardiac tissue culture. Besides the contractile dynamics and IHC images, the paper lacks other cardiac functional evaluations, such as calcium handling, impulse propagation, and/or electrophysiology. The culture reproducibility (high SD) and longevity (<20 days) still remain unsolved.

Since the submission, we have managed to keep some tissues and analyze them up to 32 days. At that time point the tissues are still beating. Nevertheless, a specific study concerning tissue longevity has not been carried out as the tissues were usually fixed after 14 days to be stained and analyze their structure.

Reviewer #2 (Public Review):

The authors should be commended for developing a high throughput platform for the formation and study of human cardiac tissues, and for discussing its potential, advantages and limitations. The study is addressing some of the key needs in the use of engineered cardiac tissues for pharmacological studies: ease of use, reproducible preparation of tissues, and high throughput.

There are also some areas where the manuscript should be improved. The design of the platform and the experimental design should be described in more detail.

It would be of interest to comprehensively document the progression of tissue formation. To this end, it would be helpful to show the changes in tissue structure through a series of images that would correspond to the progression of contractile properties shown in Figure 3.

Our results indicate that the fibroblasts/cardiomyocytes segregation likely happens as soon as the tissue is formed, as the fibroblasts are critical for tissue generation. The change with time in the shape of the contractile ring is reported in Figure 1E, with a series of images which correspond to the timepoints of Figure 3.

The very interesting tissue morphology (separation into the two regions) that was observed in this study is inviting more discussion.

Finally, the reader would benefit from more specific comparisons of the contractile function of cardiac tissues measured in this study with data reported for other cardiac tissue models.

Author Response

We thank the reviewers for truly valuable advice and comments. We have made multiple corrections and revisions to the original pre-print accordingly. Here we address 2 major points.

1) Regarding the genetic association of the common COL11A1 variant rs3753841 (p.(Pro1335Leu)), we do not propose that it is the sole risk variant contributing to the association signal we detected and have clarified this in the manuscript. We concluded that it was worthy of functional testing for reasons described here. Although there were several common variants in the discovery GWAS within and around COL11A1, none were significantly associated with AIS and none were in linkage disequilibrium (R2>0.6) with the top SNP rs3753841. We next reviewed rare (MAF<=0.01) coding variants within the COL11A1 LD region of the associated SNP (rs3753841) in 625 available exomes representing 46% of the 1,358 cases from the discovery cohort. The LD block was defined using Haploview based on the 1KG_CEU population. Within the ~41 KB LD region (chr1:103365089- 103406616, GRCh37) we found three rare missense mutations in 6 unrelated individuals, Author response table 1. Two of them (NM_080629.2: c.G4093A:p.A1365T; NM_080629.2:c.G3394A:p.G1132S), from two individuals, are predicted to be deleterious based on CADD and GERP scores and are plausible AIS risk candidates. At this rate we could expect to find only 4-5 individuals with linked rare coding variants in the total cohort of 1,358 which collectively are unlikely to explain the overall association signal we detected. Of course, there also could be deep intronic variants contributing to the association that we would not detect by our methods. However, given this scenario, the relatively high predicted deleteriousness of rs3753841 (CADD= 25.7; GERP=5.75), and its occurrence in a Gly-X-Y triplet repeat, we hypothesized that this variant itself could be a risk allele worthy of further investigation.

Author response table 1.

We also appreciate the reviewer’s suggestion to perform a rare variant burden analysis of COL11A1. We conducted pilot gene-based analysis in 4534 European ancestry exomes including 797 of our own AIS cases and 3737 controls and tested the burden of rare variants in COL11A1. SKATO P value was not significant (COL11A1_P=0.18) but this could due to lack of power and/or background from rare benign variants that could be screened out using the functional testing we have developed.

2) Regarding functional testing, by knockdown/knockout cell culture experiments, we showed for the first time that Col11a1 negatively regulates Mmp3 expression in cartilage chondrocytes, an AIS-relevant tissue. We then tested the effect of overexpressing the human wt or variant COL11A1 by lentiviral transduction in SV40-transformed chondrocyte cultures. We deleted endogenous mouse Col11a1 by Cre recombination to remove the background of its strong suppressive effects on Mmp3 expression. We acknowledge that Col11a1 missense mutations could confer gain of function or dominant negative effects that would not be revealed in this assay. However as indicated in our original manuscript we have noted that spinal deformity is described in the cho/cho mouse, a Col11a1 loss of function mutant. We also note the recent publication by Rebello et al. showing that missense mutations in Col11a2 associated with congenital scoliosis fail to rescue a vertebral malformation phenotype in a zebrafish col11a2 KO line. Although the connection between AIS and vertebral malformations is not altogether clear, we surmise that loss of the components of collagen type XI disrupt spinal development. in vivo experiments in vertebrate model systems are needed to fully establish the consequences and genetic mechanisms by which COL11A1 variants contribute to an AIS phenotype.

Author response:

We thank the reviewers for their thoughtful criticisms.  This provisional response addresses what we consider the central critiques, with a full, point-by-point reply to follow with the revised manuscript.  Central critiques concern 1) providing further clarity about the apportionment cost of time, 2) generality & scope, and 3) clarifying the meaning of key equations.

(1) Apportionment cost

Reviewers commonly identified a need to provide a concise and intuitive definition of apportionment cost, and to explicitly solve and provide for its mathematical expression. 

We will add the following definition of apportionment cost to the manuscript: “Apportionment cost is the difference in reward that can be expected, on average, between a policy of taking versus a policy of not taking the considered pursuit, over a time equal to its duration.”  While this difference is the apportionment cost of time, the amount that would be expected over a time equal to the considered pursuit under a policy of not taking the considered pursuit is the opportunity cost of time.  Together, they sum to Time’s Cost.  The above definition of apportionment cost adds to other stated relationships of apportionment cost found throughout the paper (Lines 434,435,447,450). 

As suggested, we will also add equations of apportionment cost, as below.

(2) Generality & Scope

Generality. We will add further examples in support of the generality of these equations for assessing and thinking about the value of initiating a pursuit.  Specifically, this will include 1) illustrating forgo decision making in a world composed of multiple pursuits, as in prey selection, 2) demonstrating and examining worlds in which a sequence of pursuits compose a considered pursuit’s ‘outside’, and 3) clarifying how our framework does contend with variance and uncertainty in reward magnitude and occurrence.

Scope. In this manuscript, we consider the worth of initiating one or another pursuit having completed a prior one, and not the issue of continuing within a pursuit having already engaged in it.  The worth of continuing a pursuit, as in patch-foraging/give-up tasks, constitutes a third fundamental time decision-making topology which is outside the scope of the current work.  It engages a large and important literature, encompassing evidence accumulation, and requires a paper in its own right that can use the concepts and framework developed here.  We will further consider applying this framework to extant datasets.

(3) Correction of typographical errors and further explanation of equations.   

We would like to redress the two typographical errors identified by the reviewers that appeared in the equations on line 277 and on line 306, and provide further explanation to equations that gave pause to the reviewers.

Typographical errors: 

The first typographical error in the main text regards equation 2 and will be corrected so that equation 2 appears correctly as…

Line 277:  

The second typo regards the definition of the considered pursuit’s reward rate, and will be corrected to appear as…

Line 306:   

Regarding equations:

Cross-reference to equations in the main text refer to equations as they appear in the main text.  Where needed, the appendix in which they are derived is also given.   Equation numbering within the appendices refer to equations as they appear in the appendices.  In the revision, we will refer to all equations that appear in the appendices as Ap.#.#. so as to avoid confusion between referencing equations as they appear in the main text and equations as they appear in the appendices.  

We would also like to clarify that equation 8, , as we derive, is not new, as it is similarly derived and expressed in prior foundational work by McNamara (1982), which is now so properly attributed. 

Equation 1 and Appendix 1

Equation 1 is formulated to calculate the average reward received and average time spent per unit time spent in the default pursuit. So, fi is the encounter rate of pursuit  for one unit of time spent in the default pursuit (lines 259-262). Added to the summation in the numerator, we have the average reward obtained in the default pursuit per unit time and in the denominator we have the time spent in the default pursuit per unit time (1).

Equation 2 and Appendix 2

Eq. 2.4 in Appendix 2 calculates the average time spent outside of the considered pursuit, per encounter with the considered pursuit. Breaking down eq. 2.4, the first term in the numerator,

gives the expected time spent in other pursuits, per unit time spent in the default pursuit, where fi is the encounter rate of pursuit  per unit time spent in the default pursuit, and  is the time required by pursuit i. The second term in the numerator, (1, added outside the summation) simply represents the unit of time spent in the default pursuit, over which the encounter rate of each pursuit is calculated. Together, these represent the total time spent outside the considered pursuit, per unit time spent in the default pursuit. The denominator,

is the frequency with which the considered pursuit is encountered per unit time spent in the default pursuit, so

is the average time spent within the default pursuit, per encounter with the considered pursuit. By multiplying the average time spent outside of the considered pursuit per unit time spent in the default pursuit by the average time spent within the default pursuit per encounter with the considered pursuit, we get eq. 2.4, the average time spent outside of the considered pursuit, per encounter with the considered pursuit, which is equal to tout.

                       (eq. 2.4)

Author response:

To Reviewer #1:

Thank you for your thorough review and comments on our work, which you described as “the role of neuritin in T cell biology studied here is new and interesting.”.  We have summarized your comments into two categories: biology and investigation approach, experimental rigor, and data presentation.

Biology and Investigation approach comments:

(1) Questions regarding the T cell anergy model:

Major point “(4) Figure 1E-H. The authors assume that this immunization protocol induces anergic cells, but they provide no experimental evidence for this. It would be useful to show that T cells are indeed anergic in this model, especially those that are OVA-specific. The lack of IL-2 production by Cltr cells could be explained by the presence of fewer OVA-specific cells, rather than by an anergic status.”

T cell anergy is a well-established concept first described by Schwartz’s group. It refers to the hyporesponsive T cell functional state in antigen-experienced CD4 T cells (Chappert and Schwartz, 2010; Fathman and Lineberry, 2007; Jenkins and Schwartz, 1987; Quill and Schwartz, 1987).  Anergic T cells are characterized by their inability to expand and to produce IL2 upon subsequent antigen re-challenge. In this paper, we have borrowed the existing in vivo T cell anergy induction model used by Mueller’s group for T cell anergy induction (Vanasek et al., 2006).  Specifically, Thy1.1+ Ctrl or Nrn1-/- TCR transgenic OTII cells were co-transferred with the congenically marked Thy1.2+ WT polyclonal Treg cells into TCR-/- mice.  After anergy induction, the congenically marked TCR transgenic T cells were recovered by sorting based on Thy1.1+ congenic marker, and subsequently re-stimulation ex vivo with OVA323-339 peptide. We evaluated the T cell anergic state based on OTII cell expansion in vivo and IL2 production upon OVA323-339 restimulation ex vivo.  

“The authors assume that this immunization protocol induces anergic cells, but they provide no experimental evidence for this.”

Because the anergy model by Mueller's group is well established (Vanasek et al., 2006), we did not feel that additional effort was required to validate this model as the reviewer suggested. Moreover, the limited IL2 production among the control cells upon restimulation confirms the validity of this model.

“The lack of IL-2 production by Cltr cells could be explained by the presence of fewer OVAspecific cells, rather than by an anergic status”.

Cells from Ctrl and Nrn1-/- mice on a homogeneous TCR transgenic (OTII) background were used in these experiments. The possibility that substantial variability of TCR expression or different expression levels of the transgenic TCR could have impacted IL2 production rather than anergy induction is unlikely.

Overall, we used this in vivo anergy model to evaluate the Nrn1-/- T cell functional state in comparison to Ctrl cells under the anergy induction condition following the evaluation of Nrn1 expression, particularly in anergic T cells.  Through studies using this anergy model, we observed a significant change in Treg induction among OTII cells. We decided to pursue the role of Nrn1 in Treg cell development and function rather than the biology of T cell anergy as evidenced by subsequent experiments.

Minor points “(6) On which markers are anergic cells sorted for RNAseq analysis?”

Cells were sorted out based on their congenic marker marking Ctrl or Nrn1-/- OTII cells transferred into the host mice.  We did not specifically isolate anergic cells for sequencing.

(2) Question regarding the validity of iTreg differentiation model.

Major point: “(5) Figure 2A-C and Figure 3. The use of iTregs to try to understand what is happening in vivo is problematic. iTregs are cells that have probably no equivalent in vivo, and so may have no physiological relevance. In any case, they are different from pTreg cells generated in vivo. Working with pTreg may be challenging, that is why I would suggest generating data with purified nTreg. Moreover, it was shown in the article of Gonzalez-Figueroa 2021 that Nrn1-/- nTreg retained a normal suppressive function, which would not be what is concluded by the authors of this manuscript. Moreover, we do not even know what the % of Foxp3 cells is in the iTreg used (after differentiation and 20h of re-stimulation) and whether this % is the same between Ctlr and Nrn1 KO cells.”.

We thank Reviewer #1 for their feedback. While it is true that iTregs made in vitro and in vivo generated pTregs display several distinctions (e. g., differences in Foxp3 expression stability, for example), we strongly disagree with this statement by Revieweer#1 “The use of iTregs to try to understand what is happening in vivo is problematic. iTregs are cells that have probably no equivalent in vivo, and so may have no physiological relevance.” The induced Treg cell (iTreg) model was established over 20 years ago (Chen et al., 2003; Zheng et al., 2002), and the model is widely adopted with over 2000 citations. Further, it has been instrumental in understanding different aspects of regulatory T cell biology (Hurrell et al., 2022; John et al., 2022; Schmitt and Williams, 2013; Sugiura et al., 2022).   

Because we have observed reduced pTreg generation in vivo, we choose to use the in vitro iTreg model system to understand the mechanistic changes involved in Treg cell differentiation and function, specifically, neuritin’s role in this process. We have made no claim that iTreg cell biology is identical to pTreg generated in vivo or nTreg cells. However, the iTreg culture system has proved to be a good in vitro system for deciphering molecular events involved in complex processes. As such, it remains a commonly used approach by many research groups in the Treg cell field (Hurrell et al., 2022; John et al., 2022; Sugiura et al., 2022). Moreover, applying the iTreg in vitro culture system has been instrumental in helping us identify the cell electrical state change in Nrn1-/- CD4 cells and revealed the biological link between Nrn1 and the ionotropic AMPA receptor (AMPAR), which we will discuss in the subsequent discussion. It is technically challenging to use nTreg cells for T cell electrical state studies due to their heterogeneous nature from development in an in vivo environment and the effect of manipulation during the nTreg cell isolation process, which can both affect the T cell electrical state.   

“Moreover, it was shown in the article of Gonzalez-Figueroa 2021 that Nrn1-/- nTreg retained a normal suppressive function, which would not be what is concluded by the authors of this manuscript.” 

We have also carried out nTreg studies in vitro in addition to iTreg cells. Similar to Gonzalez-Figueroa et al.'s findings, we did not observe differences in suppression function between Nrn1-/- and WT nTreg using the in vitro suppression assay. However, Nrn1-/- nTreg cells revealed reduced suppression function in vivo (Fig. 2D-L). In fact, Gonzalez-Figueroa et al. observed reduced plasma cell formation after OVA immunization in Treg-specific Nrn1-/- mice, implicating reduced suppression from Nrn1-/- follicular regulatory T (Tfr) cells. Thus, our observation of the reduced suppression function of Nrn1-/- nTreg toward effector T cell expansion, as presented in Fig. 2D-L, does not contradict the results from Gonzalez-Figueroa et al. Rather, the conclusions of these two studies agree that Nrn1 can play important roles in immune suppression observable in vivo that are not captured readily by the in vitro suppression assay.

“Moreover, we do not even know what the % of Foxp3 cells is in the iTreg used (after differentiation and 20h of re-stimulation) and whether this % is the same between Ctlr and Nrn1 KO cells.”

We have stated in the manuscript on page 7 line 208 that “Similar proportions of Foxp3+ cells were observed in Nrn1-/- and Ctrl cells under the iTreg culture condition, suggesting that Nrn1 deficiency does not significantly impact Foxp3+ cell differentiation”. In the revised manuscript, we will include the data on the proportion of Foxp3+ cells before iTreg restimulation.

(3) Confirmation of transcriptomic data regarding amino acids or electrolytes transport change

Minor point“(3) Would not it be possible to perform experiments showing the ability of cells to transport amino acids or electrolytes across the plasma membrane? This would be a more interesting demonstration than transcriptomic data.”

We appreciate Review# 1’s suggestion regarding “perform experiments showing the ability of cells to transport amino acids or electrolytes across the plasma membrane”.  We have indeed already performed such experiments corroborating the transcriptomics data on differential amino acid and nutrient transporter expression. Specifically, we loaded either iTreg or Th0 cells with membrane potential (MP) dye and measured MP level change after adding the complete set of amino acids (complete AA).  Upon entry, the charge carried by AAs may transiently affect cell membrane potential. Different AA transporter expression patterns may show different MP change patterns upon AA entry, as we showed in Author response image 1. We observed reduced MP change in Nrn1-/- iTreg compared to the Ctrl, whereas in the context of Th0 cells, Nrn1-/- showed enhanced MP change than the Ctrl. We can certainly include these data in the revised manuscript.

Author response image 1.

Membrane potential change induced by amino acids entry. a. Nrn1-/- or WT iTreg cells loaded with MP dye and MP change was measured upon the addition of a complete set of AAs. b. Nrn1-/- or WT Th0 cells loaded with MP dye and MP change was measured upon the addition of a complete set of AAs.

(4) EAE experiment data assessment

Minor point ”(5) Figure 5F. How are cells re-stimulated? If polyclonal stimulation is used, the experiment is not interesting because the analysis is done with lymph node cells. This analysis should either be performed with cells from the CNS or with MOG restimulation with lymph node cells.”

In the EAE study, the Nrn1-/- mice exhibit similar disease onset but a protracted non-resolving disease phenotype compared to the WT control mice.  Several reasons may contribute to this phenotype: 1. Enhanced T effector cell infiltration/persistence in the central nervous system (CNS); 2. Reduced Treg cell-mediated suppression to the T effector cells in the CNS; 3. Protracted non-resolving inflammation at the immunization site has the potential to continue sending T effector cells into CNS, contributing to persistent inflammation. Based on this reasoning, we examined the infiltrating T effector cell number and Treg cell proportion in the CNS.  We also restimulated cells from draining lymph nodes close to the inflammation site, looking for evidence of persistent inflammation.  When mice were harvested around day 16 after immunization, the inflammation at the local draining lymph node should be at the contraction stage.  We stimulated cells with PMA and ionomycin intended to observe all potential T effector cells involved in the draining lymph node rather than only MOG antigen-specific cells.  We disagree with Reviewer #1’s assumption that “This analysis should either be performed with cells from the CNS or with MOG restimulation with lymph node cells.”. We think the experimental approach we have taken has been appropriately tailored to the biological questions we intended to answer.

Experimental rigor and data presentation.

(1) Data labeling and additional supporting data

Major points (2) The authors use Nrn1+/+ and Nrn1+/- cells indiscriminately as control cells on the basis of similar biology between Nrn1+/+ and Nrn1+/- cells at homeostasis. However, it is quite possible that the Nrn1+/- cells have a phenotype in situations of in vitro activation or in vivo inflammation (cancer, EAE). It would be important to discriminate Nrn1+/- and Nrn1+/+ cells in the data or to show that both cell types have the same phenotype in these conditions too.

(3) Figure 1A-D. Since the authors are using the Nrp1 KO mice, it would be important to confirm the specificity of the anti-Nrn1 mAb by FACS. Once verified, it would be important to add FACS results with this mAb in Figures 1A-C to have single-cell and quantitative data as well.

Minor points  

(1) Line 119, 120 of the text. It is said that one of the most up-regulated genes in anergic cells is Nrn1 but the data is not shown.

(2) For all figures showing %, the titles of the Y axes are written in an odd way. For example, it is written "Foxp3% CD4". It would be more conventional and clearer to write "% Foxp3+ / CD4+" or "% Foxp3+ among CD4+".

(4) For certain staining (Figure 3E, H) it would be important to show the raw data, in addition to MFI or % values.

We can adapt the labeling and provide additional data, including Nrn1 staining on Treg cells and flow graphs for pmTOR and pS6 staining (Fig. 3H), as requested by Reviewer #1.

(2) Experimental rigor:

General comments:

“However, it is disappointing that reading this manuscript leaves an impression of incomplete work done too quickly.”

We were discouraged to receive the comment, “this manuscript leaves an impression of incomplete work done too quickly.” Our study of this novel molecule began without any existing biological tools such as antibodies, knockout mice, etc.  Over the past several years, we have established our own antibodies for Nrn1 detection, obtained and characterized Nrn1 knockout mice, and utilized multiple approaches to identify the molecular mechanism of Nrn1 function. Through the use of the in vitro iTreg system described in this manuscript, we identified the association of Nrn1 deficiency with cell electrical state change, potentially connected to AMPAR function. We have further corroborated our findings by generating Nrn1 and AMPAR T cell specific double knockout mice and confirmed that T cell specific AMPAR deletion could abrogate the phenotype caused by the Nrn1 deficiency (see Author response image 2).  We did not include the double knockout data in the current manuscript because AMPAR function has not yet been studied thoroughly in T cell biology, and we feel this topic warrants examination in its own right.  However, the unpublished data support the finding that Nrn1 modulates the T cell electrical state and, consequently, metabolism, ultimately influencing tolerance and immunity.  In its current form, the manuscript represents the first characterization of the novel molecule Nrn1 in anergic cells, Tregs, and effector T cells. While this work has led to several exciting additional questions, we disagree that the novel characterization we have presented Is incomplete. We feel that our present data set, which squarely highlights Nrn1’s role as an important immune regulator while shedding unprecedented light on the molecular events involved, will be of considerable interest to a broad field of researchers.

“Multiple models have been used, but none has been studied thoroughly enough to provide really conclusive and unambiguous data. For example, 5 different models were used to study T cells in vivo. It would have been preferable to use fewer, but to go further in the study of mechanisms.”

We have indeed used multiple in vivo models to reveal Nrn1's function in Treg differentiation, Treg suppression function, T effector cell differentiation and function, and the overall impact on autoimmune disease. Because the impact of ion channel function is often context-dependent, we examined the biological outcome of Nrn1 deficiency in several in vivo contexts.  We would appreciate it if Reviewer#1 would provide a specific example, given the Nrn1 phenotype, of how to proceed deeper to investigate the electrical change in the in vivo models.

“Major points (1) A real weakness of this work is the fact that in most of the results shown, there are few biological replicates with differences that are often small between Ctrl and Nrn1 -/-. The systematic use of student's t-test may lead to thinking that the differences are significant, which is often misleading given the small number of samples, which makes it impossible to know whether the distributions are Gaussian and whether a parametric test can be used. RNAseq bulk data are based on biological duplicates, which is open to criticism.”

We respectfully disagree with Reviewer #1 on the question of statistical power and significance to our work. We have used 5-8 mice/group for each in vivo model and 3-4 technical replicates for the in vitro studies, with a minimum of 2-3 replicate experiments. These group sizes and replication numbers are in line with those seen in high-impact publications. While some differences between Ctrl and Nrn1-/- appear small, they have significant biological consequences, as evidenced by the various Nrn1-/- in vivo phenotypes. Furthermore, we believe we have subjected our data to the appropriate statistical tests to ensure rigorous analysis and representation of our findings.

To Reviewer #2.

We thank Reviewer #2 for the careful review of the manuscript. We especially appreciate the comments that “The characterizations of T cell Nrn1 expression both in vitro and in vivo are comprehensive and convincing. The in vivo functional studies of anergy development, Treg suppression, and EAE development are also well done to strengthen the notion that Nrn1 is an important regulator of CD4 responsiveness.”

“The major weakness of this study stems from a lack of a clear molecular mechanism involving Nrn1. “  

We fully understand this comment from Reviewer #2. The main mechanism we identified contributing to the functional defect of Nrn1-/- T cells involves novel effects on the electric and metabolic state of the cells. Although we referenced neuronal studies that indicate Nrn1 is the auxiliary protein for the ionotropic AMPA-type glutamate receptor (AMPAR) and may affect AMPAR function, we did not provide any evidence in this manuscript as the topic requires further in-depth study.   

For the benefit of this discussion, we include our preliminary Nrn1 and AMPAR double knockout data (Author response image 2), which indicates that abrogating AMPAR expression can compensate for the defect caused by Nrn1 deficiency in vitro and in vivo. This preliminary data supports the notion that Nrn1 modulates AMPAR function, which causes changes in T cell electric and metabolic state, influencing T cell differentiation and function.  

Author response image 2.

Deletion of AMPAR expression in T cells compensates for the defect caused by Nrn1 deficiency. Nrn1-/- mice were crossed with T cell-specific AMPAR knockout mice (AMPARfl/flCD4Cre+) mice. The following mice were generated and used in the experiment: T cell specific AMPAR-knockout and Nrn1 knockout mice (AKONKO), Nrn1 knockout mice (AWTNKO), Ctrl mice (AWTNWT). a. Deletion of AMPAR compensates for the iTreg cell defect observed in Nrn1-/- CD4 cells. iTreg live cell proportion, cell number, and Ki67 expression among Foxp3+ cells 3 days after aCD3 restimulation. b. Deletion of AMPAR in T cells abrogates the enhanced autoimmune response in Nrn1-/- Mouse in the EAE disease model. Mouse relative weight change and disease score progression after EAE disease induction.  

Ion channels can influence cell metabolism through multiple means (Vaeth and Feske, 2018; Wang et al., 2020). First, ion channels are involved in maintaining cell resting membrane potential. This electrical potential difference across the cell membrane is essential for various cellular processes, including metabolism (Abdul Kadir et al., 2018; Blackiston et al., 2009; Nagy et al., 2018; Yu et al., 2022). Second, ion channels facilitate the movement of ions across cell membranes. These ions are essential for various metabolic processes. For example, ions like calcium (Ca2+), potassium (K+), and sodium (Na+) play crucial roles in signaling pathways that regulate metabolism (Kahlfuss et al., 2020). Third, ion channel activity can influence cellular energy balance due to ATP consumption associated with ion transport to maintain ion balances (Erecińska and Dagani, 1990; Gerkau et al., 2019). This, in turn, can impact processes like ATP production, which is central to cellular metabolism. Thus, ion channel expression and function determine the cell’s bioelectric state and contribute to cell metabolism (Levin, 2021).

Because the AMPAR function has not been thoroughly studied using a genetic approach in T cells, we do not intend to include the double knockout data in this manuscript before fully characterizing the T cell-specific AMPAR knockout mice.  

“Although the biochemical and informatics studies are well-performed, it is my opinion that these results are inconclusive in part due to the absence of key "naive" control groups. This limits my ability to understand the significance of these data.

Specifically, studies of the electrical and metabolic state of Nrn1-/- inducible Treg cells (iTregs) would benefit from similar data collected from wild-type and Nrn1-/- naive CD4 T cells.”

We appreciate the reviewer’s comments. This comment reflects two concerns in data interpretation:

(1) Are Nrn1-/- naïve T cells fundamentally different from WT cells? Does this fundamental difference contribute to the observed electrical and metabolic phenotype in iTreg or Th0 cells? This is a very good question we will perform the experiments as the reviewer suggested. While Nrn1 is expressed at a basal (low) level in naïve T cells, deletion of Nrn1 may cause changes in naïve T cell phenotype.   

(2) Is the Nrn1-/- phenotype caused by Nrn1 functional deficiency or due to the secondary effect of Nrn1 deletion, such as non-physiological cell membrane structure changes?

We have done the following experiment to address this concern.  We have cultured WT T cells in the presence of Nrn1 antibody and compared the outcome with Nrn1-/- iTreg cells (Author response image 3). WT iTreg cells under antibody blockade exhibited similar changes as Nrn1-/- iTreg cells, confirming the physiological relevance of the Nrn1-/- phenotype.

Author response image 3.

Nrn1 antibody blockade in WT iTreg cell culture caused similar phenotypic change as in Nrn1-/- iTreg cells. Nrn1-/- and WT CD4 cells were differentiated under iTreg condition in the presence of anti-Nrn1 (aNrn1) antibody or isotype control for 3 days. Cells were restimulated with anti-CD3 and in the presence of aNrn1 or isotype. a. MP measured 18hr after anti-CD3 restimulation. b. live CD4 cell number and proportion of Ki67 expression among live cells three days after restimulation. c. The proportion of Foxp3+ cells among live cells three days after restimulation.  

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Author response:

Reviewer #1 (Public review):

Summary:

Loh and colleagues investigate valence encoding in the mesolimbic dopamine system. Using an elegant approach, they show that sucrose, which normally evokes strong dopamine neuron activity and release in the nucleus accumbens, is made aversive via conditioned taste aversion, the same sucrose stimulus later evokes much less dopamine neuron activity and release. Thus, dopamine activity can dynamically track the changing valence of an unconditioned stimulus. These results are important for helping clarify valence and value related questions that are the matter of ongoing debate regarding dopamine functions in the field.

Strengths:

This is an elegant way to ask this question, the within subject's design and the continuity of the stimulus is a strong way to remove a lot of the common confounds that make it difficult to interpret valence-related questions. I think these are valuable studies that help tie up questions in the field while also setting up a number of interesting future directions. There are number of control experiments and tweaks to the design that help eliminate a number of competing hypotheses regarding the results. The data are clearly presented and contextualized.

Weaknesses for consideration:

The focus on one relatively understudied region of the rat striatum for dopamine recordings could potentially limit generalization of the findings. While this can be determined in future studies, the implications should be further discussed in the current manuscript.

We agree that the manuscript would benefit from providing a stronger rationale for our recording sites and acknowledging the potential for regional differences in dopamine signaling. We have made the following additions to the manuscript:

Added to the Discussion: “Recordings were targeted to the lateral VTA and the corresponding approximate terminal site in the NAc lateral shell (Lammel et al., 2008). Subregional differences in dopamine activity likely contribute to mixed findings on dopamine and affect. For example, dopamine in the NAc lateral shell differentially encodes cues predictive of rewarding sucrose and aversive footshock, which is distinct from NAc medial shell dopamine responses (de Jong et al., 2019). Our findings are similar to prior work from our group targeting recordings to the NAc dorsomedial shell (Hsu et al., 2020; McCutcheon et al., 2012; Roitman et al., 2008): there, intraoral sucrose increased NAc dopamine release while the response in the same rats to quinine was significantly lower.”

Reviewer #2 (Public review):

Summary:

Koh et al. report an interesting manuscript studying dopamine binding in the lateral accumbens shell of rats across the course of conditioned taste aversion. The question being asked here is how does the dopamine system respond to aversion? The authors take advantage of unique properties of taste aversion learning (notably, within-subjects remapping of valence to the same physical stimulus) to address this.

They combine a well controlled behavioural design (including key, unpaired controls) with fibre photometry of dopamine binding via GrabDA and of dopamine neuron activity by gCaMP, careful analyses of behaviour (e.g., head movements; home cage ingestion), the authors show that, 1) conditioned taste aversion of sucrose suppresses the activity of VTA dopamine neurons and lateral shell dopamine binding to subsequent presentations of the sucrose tastant; 2) this pattern of activity was similar to the innately aversive tastant quinine; 3) dopamine responses were negatively correlated with behavioural (inferred taste reactivity) reactivity; and 4) dopamine responses tracked the contingency of between sucrose and illness because these responses recovered across extinction of the conditioned taste aversion.

Strengths:

There are important strengths here. The use of a well-controlled design, the measurement of both dopamine binding and VTA dopamine neuron activity, the inclusion of an extinction manipulation; and the thorough reporting of the data. I was not especially surprised by these results, but these data are a potentially important piece of the dopamine puzzle (e.g., as the authors note, salience-based argument struggles to explain these data).

Weaknesses for consideration:

(1) The focus here is on the lateral shell. This is a poorly investigated region in the context of the questions being asked here. Indeed, I suspect many readers might expect a focus on the medial shell. So, I think this focus is important. But, I think it does warrant greater attention in both the introduction and discussion. We do know from past work that there can be extensive compartmentalisation of dopamine responses to appetitive and aversive events and many of the inconsistent findings in the literature can be reconciled by careful examination of where dopamine is assessed. I do think readers would benefit from acknowledgement this - for example it is entirely reasonable to suppose that the findings here may be specific to the lateral shell.

As with our response to Reviewer 1, we agree that we should provide further rationale for focusing our recordings on the lateral shell and acknowledge potential differences in dopamine dynamics across NAc subregions. In addition to the changes in the Discussion detailed in our response to Reviewer 1, we have made the following additions to the Introduction:

Added to the Introduction: “NAc lateral shell dopamine differentially encodes cues predictive of rewarding (i.e., sipper spout with sucrose) and aversive stimuli (i.e., footshock), which is distinct from other subregions (de Jong et al., 2019). It is important to note that other regions of the NAc may serve as hedonic hotspots (e.g. dorsomedial shell; or may more closely align with the signaling of salience (e.g. ventromedial shell; (Yuan et al., 2021)).”

(2) Relatedly, I think readers would benefit from an explicit rationale for studying the lateral shell as well as consideration of this in the discussion. We know that there are anatomical (PMID: 17574681), functional (PMID: 10357457), and cellular (PMID: 7906426) differences between the lateral shell and the rest of the ventral striatum. Critically, we know that profiles of dopamine binding during ingestive behaviours there can be highly dissimilar to the rest of ventral striatum (PMID: 32669355). I do think these points are worth considering.

There are several reasons why dopamine dynamics were recorded in the NAc lateral shell:

(1) Dopamine neurons in more medial aspects of the VTA preferentially target the NAc medial shell and core whereas dopamine neurons in the lateral VTA – our target for VTA DA recordings – project to the lateral shell of the NAc (Lammel et al., 2008). Thus, our goal was to sample NAc release dynamics in areas that receive projections from our cell body recording sites.

(2) Cues predictive of reward availability (i.e., sipper spout with sucrose) and aversive stimuli (i.e., footshock) are differentially encoded by NAc lateral shell dopamine, which is distinct from NAc ventromedial shell dopamine responses (de Jong et al., 2019). These findings suggest a role for NAc lateral shell dopamine in the encoding of a stimulus’s valence, which made the subregion an area of interest for further examination.

(3) With respect to the medial NAc shell specifically, extensive literature had already shown it to be a ‘hedonic hotspot’ (Morales and Berridge, 2020; Yuan et al., 2021) whereas the ventral portion is more mixed with respect to valence (Yuan et al., 2021). We had previously shown that intraoral infusions of primary taste stimuli of opposing valence (i.e., sucrose and quinine) evoke differential responses in dopamine release within the NAc dorsomedial shell (Roitman et al., 2008). We more recently replicated differential dopamine responses from dopamine cell bodies in the lateral VTA (Hsu et al., 2020) and thus endeavored to the possibility of changing dopamine responses in the lateral VTA to the same stimulus as its valence changes. As a result of these choices, measuring dopamine release in the lateral shell was a logical choice. The field would greatly benefit from continued future work surveying the entirety of the VTA DA projection terminus. 

We have included these points of justification in the Introduction and Discussion sections.

(3) I found the data to be very thoughtfully analysed. But in places I was somewhat unsure:

(a) Please indicate clearly in the text when photometry data show averages across trials versus when they show averages across animals.

We have now explicitly indicated in the figure legends of Figures 1, 3, 5, 7, and 8:

(1) In heat maps, each row represents the averaged (across rats) response on that trial.

(2) Traces below heat maps represent the response to infusion averaged first across trials for each rat and then across all rats.

(3) Insets represent the average z-score across the infusion period averaged first across all trials for each rat and then across all rats.

(b) I did struggle with the correlation analyses, for two reasons.

(i) First, the key finding here is that the dopamine response to intraoral sucrose is suppressed by taste aversion. So, this will significantly restrict the range of dopamine transients, making interpretation of the correlations difficult.

The overall hypothesis is that the dopamine response would correlate with the valence of a taste stimulus – even and especially when the stimulus remained constant but its valence changed. We inferred valence from the behavioral reactivity to the stimulus – reasoning that an appetitive taste will evoke minimal movement of the nose and paws (presumably because the animals are primarily engaging in small mouth movements associated with ingestion as shown by the seminal work of Grill and Norgren (1978) and the many studies published by the K.C. Berridge group) whereas an aversive taste will evoke significantly more movement as the rats engage in rejection responses (e.g. forelimb flails, chin rubs, etc.). When we conducted our regression analyses we endeavored to be as transparent as possible and labeled each symbol based on group (Unpaired vs Paired) and day (Conditioning vs Test). Both behavioral reactivity and dopamine responses change – but only for the Paired rats across days. In this sense, we believe the interpretation is clear. However, the Reviewer raises an important criticism that there would essentially be a floor effect with dopamine responses. We believe this is mitigated by data acquired across extinction and especially in Figure 9B. Here, the observations that dopamine responses fall to near zero but return to pre-conditioning levels in the Paired group with strong correlation between dopamine and behavioral reactivity throughout would hopefully partially allay the Reviewer’s concerns. See Part ii below for further support.

(ii) Second, the authors report correlations by combining data across groups/conditions. I understand why the authors have done this, but it does risk obscuring differences between the groups. So, my question is: what happens to this trend when the correlations are computed separately for each group? I suspect other readers will share the same question. I think reporting these separate correlations would be very helpful for the field -

regardless of the outcome.

To address this concern, we performed separate regression analyses for Paired and Unpaired rats and provide the table below to detail results where data were combined across groups or separated. Expectedly, all analyses in Paired rats indicated a significant inverse relationship between dopamine and behavioral reactivity. Afterall, it is only in this group where behavioral reactivity to the taste stimulus changes as function of conditioning. Perhaps even more striking is that in almost all comparisons, even when restricting the regression analysis to Unpaired rats, we still observed a significant inverse relationship between dopamine and behavioral reactivity in most experiments. We have outlined the separated correlations below (asterisks denote slopes significantly different from 0; * p<0.05; ** p<0.01; *** p<0.005; **** p<0.001):

Author response table 1.

(4) Figure 1A is not as helpful as it might be. I do think readers would expect a more precise reporting of GCaMP expression in TH+ and TH- neurons. I also note that many of the nuances in terms of compartmentalisation of dopamine signalling discussed above apply to ventral tegmental area dopamine neurons (e.g. medial v lateral) and this is worth acknowledging when interpreting t

Others have reported (Choi et al., 2020) and quantified (Hsu et al., 2020) GCaMP6f expression in TH+ neurons. While we didn’t report these quantifications, our observations were very much in line with previous quantifications from our laboratory (Hsu et al. 2020).

We agree that we should elaborate on VTA subregional differences and have answered this response above (See responses to Reviewer 1 Weakness #1 and Reviewer 2 Weakness #2).

Reviewer #3 (Public review):

Summary:

This study helps to clarify the mixed literature on dopamine responses to aversive stimuli. While it is well accepted that dopamine in the ventral striatum increases in response to various rewarding and appetitive stimuli, aversive stimuli have been shown to evoke phasic increases or decreasing depending on the exact aversive stimuli, behavioral paradigm, and/or dopamine recording method and location examined. Here the authors use a well-designed set of experiments to show differential responses to an appetitive primary reward (sucrose) that later becomes a conditioned aversive stimulus (sucrose previously paired with lithium chloride in a conditioned taste aversion paradigm). The results are interesting and add valuable data to the question of how the mesolimbic dopamine system encodes aversive stimuli, however, the conclusions are strongly stated given that the current data do not necessarily align with prior conflicting data in terms of recording location, and it is not clear exactly how to interpret the generally biphasic dopamine response to the CTA-sucrose which also evolves over exposures within a single session.

Strengths:

• The authors nicely demonstrate that their two aversive stimuli examined, quinine and sucrose following CTA, evoked aversive facial expressions and paw movements that differed from those following rewarding sucrose to support that the stimuli experienced by the rats differ in valence.

• Examined dopamine responses to the exact same sensory stimuli conditioned to have opposing valences, avoiding standard confounds of appetitive and aversive stimuli being sensed by different sensory modalities (i.e., sweet taste vs. electric shock)

• The authors examined multiple measurements of dopamine activity - cell body calcium (GCaMP6f) in midbrain and release in NAc (Grab-DA2h), which is useful as the prior mixed literature on aversive dopamine responses comes from a variety of recording methods.

• Correlations between sucrose preference and dopamine signals demonstrate behavioral relevance of the differential dopamine signals.

• The delayed testing experiment in Figure 7 nicely controls for the effect of time to demonstrate that the "rewarding" dopamine response to sucrose only recovers after multiple extinction sucrose exposures to extinguish the CTA.

Weaknesses for consideration:

(1) Regional differences in dopamine signaling to aversive stimuli are mentioned in the introduction and discussion. For instance, the idea that dopamine encodes salience is strongly argued against in the discussion, but the paper cited as arguing for that (Kutlu et al. 2021) is recording from the medial core in mice. Given other papers cited in the text about the regional differences in dopamine signaling in the NAc and from different populations of dopamine neurons in midbrain, it's important to mention this distinction wrt to salience signaling. Relatedly, the text says that the lateral NAc shell was targeted for accumbens recordings, but the histology figure looks like the majority of fibers were in the anterior lateral core of NAc. For the current paper to be a convincing last word on the issue, it would be extremely helpful to have similar recordings done in other parts of the NAc to do a more thorough comparison against other studies.

As the Reviewer notes, NAc dopamine recordings were aimed at the lateral NAc shell. It is possible that some dopamine neurons lying within the anterior lateral core were recorded. Fiber photometry and the size of the fiber optics cannot definitively identify the precise location and number of dopamine neurons from which we recorded. Still, recording sites did not systematically differ between groups. Further, the within-subjects design helps to mitigate any potential biases for one subregion over another. The results presented in the manuscript strongly support a valence code. It is difficult to be the ‘last word’ on this topic and we suspect debate will continue. We used taste stimuli for appetitive and aversive stimuli – whereas many in the field will continue to use other noxious stimuli (e.g. foot shock) that likely recruit different circuits en route to the VTA. And there may very well be a different regional profile for dopamine signaling with different noxious stimuli. Moreover, we used intraoral infusion to avoid confounds of stimulus avoidance and competing motivations (e.g. food or fluid deprivation). We believe that this is one of the most important and unique features of our report. Recent work supports a role for phasic increases in dopamine in avoidance of noxious stimuli (Jung et al., 2024) and it will be critical for the field to reflect on the differences between avoidance and aversion. Moreover, in ongoing studies we aspire to fully survey dopamine signaling in conditioned taste aversion across the medial-lateral and dorsal-ventral axes of the VTA and NAc.

(2) Dopamine release in the NAc never dips below baseline for the conditioned sucrose. Is it possible to really consider this as a signal for valence per se, as opposed to it being a weaker response relative to the original sucrose response?

Indeed, NAc dopamine release to intraoral quinine nor aversive sucrose doesn’t dip below baseline but rather dopamine binding doesn’t change from pre-infusion baseline levels. It should be noted that VTA dopamine cell body activity does indeed dip below baseline in response to aversive sucrose. Moreover, using fast-scan cyclic voltammetry, we showed that dopamine release dips below baseline in the NAc dorsomedial shell in response to intraoral quinine (Roitman et al., 2008). The differences across recording sites may reflect regional differences but they may also reflect differences in recording approaches. GrabDA2h, used here, has relatively slow kinetics that may obscure dips below baseline (see response Weakness# 8 below).

(3) Related to this, the main measure of the dopamine signal here, "mean z-score," obscures the temporal dynamics of the aversive dopamine response across a trial. This measure is used to claim that sucrose after CTA is "suppressing" dopamine neuron activity and release, which is true relative to the positive valence sucrose response. However, both GRAB-DA and cell-body GCaMP measurements show clear increases after onset of sucrose infusion before dipping back to baseline or slightly below in the average of all example experiments displayed. One could point to these data to argue either that aversive stimuli cause phasic increases in dopamine (due to the initial increase) or decreases (due to the delayed dip below baseline) depending on the measurement window. Some discussion of the dynamics of the response and how it relates to the prior literature would be useful.

We have used mean z-score to do much of our quantitative analyses but the Reviewer raises the intriguing possibility that we are masking an initial increase in dopamine release and VTA DA activity evoked by aversive taste by doing so. We included the heat maps in the manuscript to be as transparent as possible about the time course of dopamine responses – both within a trial and across trials. The Reviewer’s point prompted us to reflect further on the heat maps and recognize that trials early in the session often showed a brief increase in dopamine for aversive sucrose but this response dissipated (NAc dopamine release) or flipped (VTA DA cell body activity) over trials. We now quantitatively characterize this feature by looking at the timecourse of dopamine responses in each third of the trials (1-10, 11-20, 21-30; see Author response images 1,2 and 3). As we infer the valence of the stimulus from nose and paw movements (behavioral reactivity), it is especially striking that we a similar timecourse for changes in behavior. Collectively, the data may reflect an updating process that is relatively slow and requires experience of the stimulus in a new (aversive) state – that is, a model-free process. While our experiments were not designed to test the updating of dopamine responses and discern their participation in model-based versus model-free learning processes – another debate in the dopamine field (Cone et al., 2016; Deserno et al., 2021)– the data reflect a model-free process. This is further supported in the experiment involving multiple conditioning sessions, where dopamine ‘dips’ are observed in trials 1-10 on Conditioning Day 3 and Extinction Day 1 when the new value of sucrose has been established. Finally, the relatively slow updating of the value of sucrose is reflected in older literature using a continuous intraoral infusion. Using this approach, rats began rejecting the saccharin infusion only after ~2min rather than immediately (Schafe et al., 1998; Schafe and Bernstein, 1996; Wilkins and Bernstein, 2006).   

Author response image 1.

Author response image 2.

Author response image 3.

(4) Would this delayed below-baseline dip be visible with a shorter infusion time?

While our experiments did not explore this parameter, it would be interesting to parametrically vary infusion duration times and examine differences in dopamine responses. However, we believe the most parsimonious explanation is that the ‘dip’ in VTA cell body activity develops as a function of the slow updating of the value of sucrose reflective of a model-free process. We recognize that this is mere speculation.

(5) Does the max of the increase or the dip of the decrease better correlate with the behavioral measures of aversion (orofacial, paw movements) or sucrose preference than "mean z-score" measure used here?

It seems plausible that finding the most extreme value from baseline could better correlate to behavioral measures. Time courses to max increase and max decrease are different. Moreover, with appetitive sucrose, there are often multiple transients that occur throughout a single intraoral infusion. Coupled with a noisy time course for individual components of behavioral reactivity, we determined that averaging data across the whole infusion period (i.e. mean z-score) was the most objective way we could analyze the dopamine and behavioral responses to taste stimuli.

(6) The authors argue strongly in the discussion against the idea that dopamine is encoding "salience." Could this initial peak (also seen in the first few trials of quinine delivery, fig 1c color plot) be a "salience" response?

Our response above to the potential for ‘mixed’ dopamine responses to aversive sucrose led to additional analyses that support a slow updating of both behavior and dopamine to the new, aversive value of sucrose. Quinine is innately aversive and thus the Reviewer rightly points out that even here we observe an increase in dopamine release evoked by quinine on the first few trials (as observed in the heat map). We’d like to note, though, that the order of stimulus exposure was counterbalanced across rats. In those rats first receiving a sucrose session, quinine initially caused a modest increase in dopamine release during the first 10 trials (which is more pronounced in the first 2 trials). In the subsequent 2 blocks of 10 trials, no such increase was observed. Interestingly, in rats for which quinine was their first stimulus, we did not see an increase in dopamine release on the first few trials (see Author response image 4). We speculate that the initial sucrose session required the value of intraoral infusions to be updated when quinine was delivered to these rats and that, once more, the updating process may be slow and akin to a model-free process. This analysis, at present, is underpowered but will direct future attention in follow-up work.

Author response image 4.

(7) Related to this, the color plots showing individual trials show a reduction in the increases to positive valence sucrose across conditioning day trials and a flip from infusion-onset increase to delayed increases across test day trials. This evolution across days makes it appear that the last few conditioning day trials would be impossible to discriminate from the first few test day trials in the CTA-paired. Presumably, from strength of CTA as a paradigm, the sucrose is already aversive to the animals at the first trial of test day. Why do the authors think the response evolves across this session?

As the Reviewer noted, Points 3-7 are related. We have speculated that the evolving dopamine response in Paired rats across test day trials reflects a model-free process. Importantly, as in the manuscript, our additional analyses once again show a tight relationship between behavioral reactivity and the dopamine response across the test session trials. It is important to note, though, that these experiments were not designed to test if responses reflect model-free or model-based processes.

(8) Given that most of the work is using a conditioned aversive stimulus, the comparison to a primary aversive tastant quinine is useful. However, the authors saw basically no dopamine response to a primary aversive tastant quinine (measured only with GRAB-DA) and saw less noticeable decreases following CTA for NAc recordings with GRAB-DA2h than with cell body GCaMP. Given that they are using the high-affinity version of the GRAB sensor, this calls into question whether this is a true difference in release vs. soma activity or issue of high affinity release sensor making decreases in dopamine levels more difficult to observe.

We share the same speculation as the Reviewer. Using fast-scan cyclic voltammetry, albeit measuring dopamine concentration in the dorsomedial shell, we observed a clear decrease from baseline with intraoral infusions of quinine (Roitman et al., 2008). Using fiber photometry here, the Reviewer and we note that GRAB_DA2h is a high-affinity (i.e., EC50: 7nM) dopamine sensor with relatively long off-kinetics (i.e., t1/2 decay time: 7300ms) (Labouesse et al., 2020). It may therefore be much more difficult to observe decreases (below baseline) using this sensor. The publication of new dopamine sensors - with lower affinity, faster kinetics, and greater dynamic range (Zhuo et al., 2024) – introduces opportunities for comparison and the greater potential for capturing decreases below baseline. Due to the poorer kinetics associated with GRAB_DA2h, we would not assert that direct comparisons between the GCaMP- and GRAB-based signals observed here represent true differences between somatic and terminal activity.

References

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Author Response:

We greatly appreciate invaluable and constructive comments from Editors and Reviewers. We also thank for their time and patience. We are pleased for our manuscript to have been assessed valuable and solid.

One of most critical concerns was a possible involvement of Ca2+ channel inactivation in the strong paired pulse depression (PPD). Meanwhile, we have already measured total (free plus buffered) calcium increments induced by each of first four APs in a 40 Hz train at axonal boutons of prelimbic layer 2/3 pyramidal cells. We found that first four Ca2+ increments were not different each other, arguing against possible contribution of Ca2+ channel inactivation to PPD. Please see our reply to the 2nd issue in the Weakness section of Reviewer #3.

The second critical issue was on the definition of ‘vesicular probability’. Previously, vesicular probability (pv) has been used with reference to the releasable vesicle pool which includes not only tightly docked vesicles but also reluctant vesicles. On the other hand, the meaning of pv in the present study was release probability of tightly docked vesicles. We clarified this point in our replies to the 1st issues in the Weakness sections of Reviewer #2 and Reviewer #3.

To other Reviews’ comments, we below described our point-by-point replies.

Reviewer #2 (Public review):

Summary:

Shin et al aim to identify in a very extensive piece of work a mechanism that contributes to dynamic regulation of synaptic output in the rat cortex at the second time scale. This mechanism is related to a new powerful model is well versed to test if the pool of SV ready for fusion is dynamically scaled to adjust supply demand aspects. The methods applied are state-of-the-art and both address quantitative aspects with high signal to noise. In addition, the authors examine both excitatory output onto glutamatergic and GABAergic neurons, which provides important information on how general the observed signals are in neural networks, The results are compellingly clear and show that pool regulation may be predominantly responsible. Their results suggests that a regulation of release probability, the alternative contender for regulation, is unlikely to be involved in the observed short term plasticity behavior (but see below). Besides providing a clear analysis pof the underlying physiology, they test two molecular contenders for the observed mechanism by showing that loss of Synaptotagmin7 function and the role of the Ca dependent phospholipase activity seems critical for the short term plasticity behavior. The authors go on to test the in vivo role of the mechanism by modulating Syt7 function and examining working memory tasks as well as overall changes in network activity using immediate early gene activity. Finally, they model their data, providing strong support for their interpretation of TS pool occupancy regulation.

Strengths:

This is a very thorough study, addressing the research question from many different angles and the experimental execution is superb. The impact of the work is high, as it applies recent models of short term plasticity behavior to in vivo circuits further providing insights how synapses provide dynamic control to enable working memory related behavior through nonpermanent changes in synaptic output.

Weaknesses:

While this work is carefully examined and the results are presented and discussed in a detailed manner, the reviewer is still not fully convinced that regulation of release provability is not a putative contributor to the observed behavior. No additional work is needed but in the moment I am not convinced that changes in release probability are not in play. One solution may be to extend the discussion of changes in rules probability as an alternative.

Quantal content (m) depends on n * pv, where n = RRP size and pv =vesicular release probability. The value for pv critically depends on the definition of RRP size. Recent studies revealed that docked vesicles have differential priming states: loosely or tightly docked state (LS or TS, respectively). Because the RRP size estimated by hypertonic solution or long presynaptic depolarization is larger than that by back extrapolation of a cumulative EPSC plot (Moulder & Mennerick, 2005; Sakaba, 2006) in glutamatergic synapses, the former RRP (denoted as RRPhyper) may encompass not only AP-evoked fast-releasing vesicles (TS vesicle) but also reluctant vesicles (LS vesicles). Because we measured pv based on AP-evoked EPSCs such as strong paired pulse depression (PPD) and associated failure rates, pv in the present study denotes vesicular fusion probability of TS vesicles not that of LS plus TS vesicles.

Recent studies suggest that release sites are not fully occupied by TS vesicles in the baseline (Miki et al., 2016; Pulido and Marty, 2018; Malagon et al., 2020; Lin et al., 2022). Instead the occupancy (pocc) by TS vesicles is subject to dynamic regulation by reversible rate constants (denoted by k1 and b1, respectively). The number of TS vesicles (n) can be factored into the number of release sites (N) and pocc, among which N is a fixed parameter but pocc depends on k1/(k1+b1) under the framework of the simple refilling model (see Methods). Because these refilling rate constants are regulated by Ca2+ (Hosoi, et al., 2008), pocc is not a fixed parameter. Therefore, release probability should be re-defined as pocc x pv. In this regard, the increase in release probability is a major player in STF. Our study asserts that STF by 2.3 times can be attributed to an increase in pocc rather than pv, because pv is close to unity (Fig. S8). Moreover, strong PPD was observed not only in the baseline but also at the early and in the middle of a train (Fig. 2 and 7) and during the recovery phase (Fig. 3), arguing against a gradual increase in pv of reluctant vesicles.

If the Reviewer meant vesicular release or fusion probability (pv) by ‘release provability’, pv (of TS vesicles) is not a major player in STF, because the baseline pv is already higher than 0.8 even if it is most parsimoniously estimated (Fig. 2). Moreover, considering very high refilling rate (23/s), the high double failure rate cannot be explained without assuming that pv is close to unity (Fig. S8).

Conventional models for facilitation assume a post-AP residual Ca2+-dependent step increase in pv of RRP (Dittman et al., 2000) or reluctant vesicles (Turecek et al., 2016). Given that pv of TS vesicles is close to one, an increase in pv of TS vesicles cannot account for facilitation. The possibility for activity-dependent increase in fusion probability of LS vesicles (denoted as pv,LS) should be considered in two ways depending on whether LS and TS vesicles reside in distinct pools or in the same pool. Notably, strong PPD at short ISI implies that pv,LS is near zero at the resting state. Whereas LS vesicles do not contribute to baseline transmission, short-term facilitation (STF) may be mediated by cumulative increase in pv, LS that reside in a distinct pool. Because the increase in pv,LS during facilitation recruits new release sites (increase in N), the variance of EPSCs should become larger as stimulation frequency increases, resulting in upward deviation from a parabola in the V-M plane, as shown in recent studies (Valera et al., 2012; Kobbersmed et al., 2020). This prediction is not compatible with our results of V-M analysis (Fig. 3), showing that EPSCs during STF fell on the same parabola regardless of stimulation frequencies. Therefore, it is unlikely that an increase in fusion probability of reluctant vesicles residing in a distinct release pool mediates STF in the present study.

For the latter case, in which LS and TS vesicles occupy in the same release sites, it is hard to distinguish a step increase in fusion probability of LS vesicles from a conversion of LS vesicles to TS. Nevertheless, our results do not support the possibility for gradual increase in pv,LS that occurs in parallel with STF. Strong PPD, indicative of high pv, was consistently found not only in the baseline (Fig. 2 and Fig. S6) but also during post-tetanic augmentation phase (Fig. 3D) and even during the early development of facilitation (Fig. 2D-E and Fig. 7), arguing against gradual increase in pv,LS. One may argue that STF may be mediated by a drastic step increase of pv,LS from zero to one, but it is not distinguishable from conversion of LS to TS vesicles.

To address the reviewer’s concern, we will incorporate these perspectives into the discussion and further clarify the reasoning behind our conclusions.

<References>

Moulder KL, Mennerick S (2005) Reluctant vesicles contribute to the total readily releasable pool in glutamatergic hippocampal neurons. J Neurosci 25:3842–3850.

Sakaba, T (2006) Roles of the fast-releasing and the slowly releasing vesicles in synaptic transmission at the calyx of Held. J Neurosci 26(22): 5863-5871.

Fig 3 I am confused about the interpretation of the Mean Variance analysis outcome. Since the data points follow the curve during induction of short term plasticity, aren't these suggesting that release probability and not the pool size increases? Related, to measure the absolute release probability and failure rate using the optogenetic stimulation technique is not trivial as the experimental paradigm bias the experiment to a given output strength, and therefore a change in release probability cannot be excluded.

Under the recent definition of release probability, it can be factored into pv and pocc, which are fusion probability of TS vesicles and the occupancy of release sites by TS vesicles, respectively. With this regard, our interpretation of the Variance-Mean results is consistent with conventional one: different data points along a parabola represent a change in release probability (= pocc x pv). Our novel finding is that the increase in release probability should be attributed to an increase in pocc, not to that in pv.

Fig4B interprets the phorbol ester stimulation to be the result of pool overfilling, however, phorbol ester stimulation has also been shown to increase release probability without changing the size of the readily releasable pool. The high frequency of stimulation may occlude an increased paired pulse depression in presence of OAG, which others have interpreted in mammalian synapses as an increase in release probability.

To our experience in the calyx of Held synapses, OAG, a DAG analogue, increased the fast releasing vesicle pool (FRP) size (Lee JS et al., 2013), consistent with our interpretation (pool overfilling). Once the release sites are overfilled in the presence of OAG, it is expected that the maximal STF (ratio of facilitated to baseline EPSCs) becomes lower as long as the number of release sites (N) are limited. As aforementioned, the baseline pv is already close to one, and thus it cannot be further increased by OAG. Instead, the baseline pocc seems to be increased by OAG.

<Reference>

Lee JS, et al., Superpriming of synaptic vesicles after their recruitment to the readily releasable pool. Proc Natl Acad Sci U S A, 2013. 110(37): 15079-84.

The literature on Syt7 function is still quite controversial. An observation in the literature that loss of Syt7 function in the fly synapse leads to an increase of release probability. Thus the observed changes in short term plasticity characteristics in the Syt7 KD experiments may contain a release probability component. Can the authors really exclude this possibility? Figure 5 shows for the Syt7 KD group a very prominent depression of the EPSC/IPSC with the second stimulus, particularly for the short interpulse intervals, usually a strong sign of increased release probability, as lack of pool refilling can unlikely explain the strong drop in synaptic output.

The reviewer raises an interesting point regarding the potential link between Syt7 KD and increased initial pv, particularly in light of observations in Drosophila synapses (Guan et al., 2020; Fujii et al., 2021), in which Syt7 mutants exhibited elevated initial pv. However, it is important to note that these findings markedly differ from those in mammalian systems, where the role of Syt7 in regulating initial pv has been extensively studied. In rodents, consistent evidence indicates that Syt7 does not significantly affect initial pv, as demonstrated in several studies (Jackman et al., 2016; Chen et al., 2017; Turecek and Regehr, 2018). Furthermore, in our study of excitatory synapses in the mPFC layer 2/3, we observed an initial pv already near its maximal level, approaching a value of 1. Consequently, it is unlikely that the loss of Syt7 could further elevate the initial pv. Instead, such effects are more plausibly explained by alternative mechanisms, such as alterations in vesicle replenishment dynamics, rather than a direct influence on pv.

<References>

Chen, C., et al., Triple Function of Synaptotagmin 7 Ensures Efficiency of High-Frequency Transmission at Central GABAergic Synapses. Cell Rep, 2017. 21(8): 2082-2089.

Fujii, T., et al., Synaptotagmin 7 switches short-term synaptic plasticity from depression to facilitation by suppressing synaptic transmission. Scientific reports, 2021. 11(1): 4059.

Guan, Z., et al., Drosophila Synaptotagmin 7 negatively regulates synaptic vesicle release and replenishment in a dosage-dependent manner. Elife, 2020. 9: e55443.

Jackman, S.L., et al., The calcium sensor synaptotagmin 7 is required for synaptic facilitation. Nature, 2016. 529(7584): 88-91.

Turecek, J. and W.G. Regehr, Synaptotagmin 7 mediates both facilitation and asynchronous release at granule cell synapses. Journal of Neuroscience, 2018. 38(13): 3240-3251.

Reviewer #3 (Public review):

Summary:

The report by Shin, Lee, Kim, and Lee entitled "Progressive overfilling of readily releasable pool underlies short-term facilitation at recurrent excitatory synapses in layer 2/3 of the rat prefrontal cortex" describes electrophysiological experiments of short-term synaptic plasticity during repetitive presynaptic stimulation at synapses between layer 2/3 pyramidal neurons and nearby target neurons. Manipulations include pharmacological inhibition of PLC and actin polymerization, activation of DAG receptors, and shRNA knockdown of Syt7. The results are interpreted as support for the hypothesis that synaptic vesicle release sites are vacant most of the time at resting synapses (i.e., p_occ is low) and that facilitation (and augmentation) components of short-term enhancement are caused by an increase in occupancy, presumably because of acceleration of the transition from not-occupied to occupied. The report additionally describes behavioural experiments where trace fear conditioning is degraded by knocking down syt7 in the same synapses.

Strengths:

The strength of the study is in the new information about short-term plasticity at local synapses in layer 2/3, and the major disruption of a memory task after eliminating short-term enhancement at only 15% of excitatory synapses in a single layer of a small brain region. The local synapses in layer 2/3 were previously difficult to study, but the authors have overcome a number of challenges by combining channel rhodopsins with in vitro electroporation, which is an impressive technical advance.

Weaknesses:

The question of whether or not short-term enhancement causes an increase in p_occ (i.e., "readily releasable pool overfilling") is important because it cuts to the heart of the ongoing debate about how to model short term synaptic plasticity in general. However, my opinion is that, in their current form, the results do not constitute strong support for an increase in p_occ, even though this is presented as the main conclusion. Instead, there are at least two alternative explanations for the results that both seem more likely. Neither alternative is acknowledged in the present version of the report.

The evidence presented to support overfilling is essentially two-fold. The first is strong paired pulse depression of synaptic strength when the interval between action potentials is 20 or 25 ms, but not when the interval is 50 ms. Subsequent stimuli at frequencies between 5 and 40 Hz then drive enhancement. The second is the observation that a slow component of recovery from depression after trains of action potentials is unveiled after eliminating enhancement by knocking down syt7. Of the two, the second is predicted by essentially all models where enhancement mechanisms operate independently of release site depletion - i.e., transient increases in p_occ, p_v, or even N - so isn't the sort of support that would distinguish the hypothesis from alternatives (Garcia-Perez and Wesseling, 2008, https://doi.org/10.1152/jn.01348.2007).

The apparent discrepancy in interpretation of post-tetanic augmentation between the present and previous papers [Sevens Wesseling (1999), Garcia-Perez and Wesseling (2008)] is an important issue that should be clarified. We noted that different meanings of ‘vesicular release probability’ in these papers are responsible for the discrepancy. We will add an explanation to Discussion on the difference in the meaning of ‘vesicular release probability’ between the present study and previous studies [Sevens Wesseling (1999), Garcia-Perez and Wesseling (2008)]. In summary, the pv in the present study was used for vesicular release probability of TS vesicles, while previous studies used it as vesicular release probability of vesicles in the RRP, which include LS and TS vesicles. Accordingly, pocc in the present study is occupancy of release sites by TS vesicles.

Not only double failure rate but also other failure rates upon paired pulse stimulation were best fitted at pv close to 1 (Fig. S8 and associated text). Moreover, strong PPD, indicating release of vesicles with high pv, was observed not only at the beginning of a train but also in the middle of a 5 Hz train (Fig. 2D), during the augmentation phase after a 40 Hz train (Fig 3D), and in the recovery phase after three pulse bursts (Fig. 7). Given that pv is close to 1 throughout the EPSC trains and that N does not increase during a train (Fig. 3), synaptic facilitation can be attained only by the increase in pocc (occupancy of release sites by TS vesicles). In addition, it should be noted that Fig. 7 demonstrates strong PPD during the recovery phase after depletion of TS vesicles by three pulse bursts, indicating that recovered vesicles after depletion display high pv too. Knock-down of Syt7 slowed the recovery of TS vesicles after depletion of TS vesicles, highlighting that Syt7 accelerates the recovery of TS vesicles following their depletion.

As addressed in our reply to the first issue raised by Reviewer #2 and the third issue raised by Reviewer #3, our results do not support possibilities for recruitment of new release sites (increase in N) having low pv or for a gradual increase in pv of reluctant vesicles during short-term facilitation.  

<Following statement will be added to _Discussion_ in the revised manuscript>

Previous studies suggested that an increase in pv is responsible for post-tetanic augmentation (Stevens and Wesseling, 1999; Garcia-Perez and Wesseling, 2008) by observing invariance of the RRP size after tetanic stimulation. In these studies, the RRP size was estimated by hypertonic sucrose solution or as the sum of EPSCs evoked 20 Hz/60 pulses train (denoted as ‘RRPhyper’). Because reluctant vesicles (called LS vesicles) can be quickly converted to TS vesicles (16/s) and are released during a train (Lee et al., 2012), it is likely that the RRP size measured by these methods encompasses both LS and TS vesicles. In contrast, we assert high pv based on the observation of strong PPD and failure rates upon paired stimulations at ISI of 20 ms (Fig. 2 and Fig. S8). Given that single AP-induced vesicular release occurs from TS vesicles but not from LS vesicles, pv in the present study indicates the fusion probability of TS vesicles. From the same reasons, pocc denotes the occupancy of release sites by TS vesicles. Note that our study does not provide direct clue whether release sites are occupied by LS vesicles that are not tapped by a single AP, although an increase in the LS vesicle number may accelerate the recovery of TS vesicles. As suggested in Neher (2024), even if the number of LS plus TS vesicles are kept constant, an increase in pocc (occupancy by TS vesicles) would be interpreted as an increase in ‘vesicular release probability’ as in the previous studies (Stevens and Wesseling (1999); Garcia-Perez and Wesseling (2008)) as long as it was measured based on RRPhyper.

Regarding the paired pulse depression: The authors ascribe this to depletion of a homogeneous population of release sites, all with similar p_v. However, the details fit better with the alternative hypothesis that the depression is instead caused by quickly reversing inactivation of Ca2+ channels near release sites, as proposed by Dobrunz and Stevens to explain a similar phenomenon at a different type of synapse (1997, PNAS,<br /> https://doi.org/10.1073/pnas.94.26.14843). The details that fit better with Ca2+ channel inactivation include the combination of the sigmoid time course of the recovery from depression (plotted backwards in Fig1G,I) and observations that EGTA (Fig2B) increases the paired-pulse depression seen after 25 ms intervals. That is, the authors ascribe the sigmoid recovery to a delay in the activation of the facilitation mechanism, but the increased paired pulse depression after loading EGTA indicates, instead, that the facilitation mechanism has already caused p_r to double within the first 25 ms (relative to the value if the facilitation mechanism was not active). Meanwhile, Ca2+ channel inactivation would be expected to cause a sigmoidal recovery of synaptic strength because of the sigmoidal relationship between Ca2+-influx and exocytosis (Dodge and Rahamimoff, 1967, https://doi.org/10.1113/jphysiol.1967.sp008367).

The Ca2+-channel inactivation hypothesis could probably be ruled in or out with experiments analogous to the 1997 Dobrunz study, except after lowering extracellular Ca2+ to the point where synaptic transmission failures are frequent. However, a possible complication might be a large increase in facilitation in low Ca2+ (Fig2B of Stevens and Wesseling, 1999, https://doi.org/10.1016/s0896-6273(00)80685-6).

We appreciate the reviewer's thoughtful comment regarding the potential role of Ca2+ channel inactivation in the observed paired-pulse depression (PPD). As noted by the Reviewer, the Dobrunz and Stevens (1997) suggested that the high double failure rate at short ISIs in synapses exhibiting PPD can be attributed to Ca2+ channel inactivation. This interpretation seems to be based on a premise that the number of RRP vesicles are not varied trial-by-trial. The number of TS vesicles, however, can be dynamically regulated depending on the parameters k1 and b1, as shown in Fig. S8, implying that the high double failure rate at short ISIs cannot be solely attributed to Ca2+ channel inactivation. Nevertheless, we acknowledge the possibility that Ca2+ channel inactivation may contribute to PPD, and therefore, we have further investigated this possibility. Specifically, we measured action potential (AP)-evoked Ca2+ transients at individual axonal boutons of layer 2/3 pyramidal cells in the mPFC using two-dye ratiometry techniques. Our analysis revealed no evidence for Ca2+ channel inactivation during a 40 Hz train of APs. This finding indicates that voltage-gated Ca2+ channel inactivation is unlikely to contribute to the pronounced PPD.

Author response image 1 below shows how we measured the total Ca2+ increments at axonal boutons. First we estimated endogenous Ca2+-binding ratio from analyses of single AP-induced Ca2+ transients at different concentrations of Ca2+ indicator dye (panels A to E). And then, using the Ca2+ buffer properties, we converted free [Ca2+] amplitudes to total calcium increments for the first four AP-evoked Ca2+ transients in a 40 Hz train (panels G-I). We will incorporate these results into the revised version of reviewed preprint to provide evidence against the Ca2+ channel inactivation.

Author response image 1.

On the other hand, even if the paired pulse depression is caused by depletion of release sites rather than Ca2+-channel inactivation, there does not seem to be any support for the critical assumption that all of the release sites have similar p_v. And indeed, there seems to be substantial emerging evidence from other studies for multiple types of release sites with 5 to 20-fold differences in p_v at a wide variety of synapse types (Maschi and Klyachko, eLife, 2020, https://doi.org/10.7554/elife.55210; Rodriguez Gotor et al, eLife, 2024, https://doi.org/10.7554/elife.88212 and refs. therein). If so, the paired pulse depression could be caused by depletion of release sites with high p_v, whereas the facilitation could occur at sites with much lower p_v that are still occupied. It might be possible to address this by eliminating assumptions about the distribution of p_v across release sites from the variance-mean analysis, but this seems difficult; simply showing how a few selected distributions wouldn't work - such as in standard multiple probability fluctuation analyses - wouldn't add much.

We appreciate the reviewer’s insightful comments regarding the potential increase in pfusion of reluctant vesicles. It should be noted, however, that Maschi and Klyachko (2020) showed a distribution of release probability (pr) within a single active zone rather than a heterogeneity in pfusion of individual docked vesicles. Therefore both pocc and pv of TS vesicles would contribute to the pr distribution shown in Maschi and Klyachko (2020). 

The Reviewer’s concern aligns closely with the first issue raised by Reviewer #2, to which we addressed in detail. Briefly, new release site may not be recruited during facilitation or post-tetanic augmentation, because variance of EPSCs during and after a train fell on the same parabola (Fig. 3). Secondly, strong PPD was observed not only in the baseline but also during early and late phases of facilitation, indicating that vesicles with very high pv contribute to EPSC throughout train stimulations (Fig. 2, 3, and 7). These findings argue against the possibilities for recruitment of new release sites harboring low pv vesicles and for a gradual increase in fusion probability of reluctant vesicles.

To address the reviewers’ concern, we will incorporate the perspectives into Discussion and further clarify the reasoning behind our conclusions.

In any case, the large increase - often 10-fold or more - in enhancement seen after lowering Ca2+ below 0.25 mM at a broad range of synapses and neuro-muscular junctions noted above is a potent reason to be cautious about the LS/TS model. There is morphological evidence that the transitions from a loose to tight docking state (LS to TS) occur, and even that the timing is accelerated by activity. However, 10-fold enhancement would imply that at least 90 % of vesicles start off in the LS state, and this has not been reported. In addition, my understanding is that the reverse transition (TS to LS) is thought to occur within 10s of ms of the action potential, which is 10-fold too fast to account for the reversal of facilitation seen at the same synapses (Kusick et al, 2020, https://doi.org/10.1038/s41593-020-00716-1).

As the reviewer suggested, low external Ca2+ concentration can lower release probability (pr). Given that both pv and pocc are regulated by [Ca2+]i, low external [Ca2+] may affect not only pv but also pocc, both of which would contribute to low pr. Under such conditions, it would be plausible that the baseline pr becomes much lower than 0.1 due to low pv and pocc (for instance, pv decreases from 1 to 0.5, and pocc from 0.3 to 0.1, then pr = 0.05), and then pr (= pv x pocc) has a room for an increase by a factor of ten (0.5, for example) by short-term facilitation as cytosolic [Ca2+] accumulates during a train.

If pv is close to one, pr depends pocc, and thus facilitation depends on the number of TS vesicles just before arrival of each AP of a train. Thus, post-train recovery from facilitation would depend on restoration of equilibrium between TS and LS vesicles to the baseline. Even if transition between LS and TS vesicles is very fast (tens of ms), the equilibrium involved in de novo priming (reversible transitions between recycling vesicle pool and partially docked LS vesicles) seems to be much slower (13 s in Fig. 5A of Wu and Borst 1999). Thus, we can consider a two-step priming model (recycling pool -> LS -> TS), which is comprised of a slow 1st step (-> LS) and a fast 2nd step (-> TS). Under the framework of the two-step model, the slow 1st step (de novo priming step) is the rate limiting step regulating the development and recovery kinetics of facilitation. Given that on and off rate for Ca2+ binding to Syt7 is slow, it is plausible that Syt7 may contribute to short-term facilitation (STF) by Ca2+-dependent acceleration of the 1st step (as shown in Fig. 9). During train stimulation, the number of LS vesicles would slowly accumulate in a Syt7 and Ca2+-dependent manner, and this increase in LS vesicles would shift LS/TS equilibrium towards TS, resulting in STF. After tetanic stimulation, the recovery kinetics from facilitation would be limited by slow recovery of LS vesicles.

<Reference>

Wu, L.-G. and Borst J.G.G. (1999) The reduced release probability of releasable vesicles during recovery from short-term synaptic depression. Neuron, 23(4): 821-832.

Individual points:

(1) An additional problem with the overfilling hypothesis is that syt7 knockdown increases the estimate of p_occ extracted from the variance-mean analysis, which would imply a faster transition from unoccupied to occupied, and would consequently predict faster recovery from depression. However, recovery from depression seen in experiments was slower, not faster. Meanwhile, the apparent decrease in the estimate of N extracted from the mean-variance analysis is not anticipated by the authors' model, but fits well with alternatives where p_v varies extensively among release sites because release sites with low p_v would essentially be silent in the absence of facilitation.

Slower recovery from depression observed in the Syt7 knockdown (KD) synapses (Fig. 7) may results from a deficiency in activity-dependent acceleration of TS vesicle recovery. Although basal occupancy was higher in the Syt7 KD synapses, this does not indicate a faster activity-dependent recovery.

Higher baseline occupancy does not always imply faster recovery of PPR too. Actually PPR recovery was slower in Syt7 KD synapses than WT one (18.5 vs. 23/s). Under the framework of the simple refilling model (Fig. S8Aa), the baseline occupancy and PPR recovery rate are calculated as k1 / (k1 + b1) and (k1 + b1), respectively. The baseline occupancy depends on k1/b1, while the PPR recovery on absolute values of k1 and b1. Based on pocc and PPR recovery time constant of WT and KD synapses, we expect higher k1/b1 but lower values for (k1 +b1) in Syt7 KD synapses compared to WT ones.

Lower release sites (N) in Syt7-KD synapses was not anticipated. As you suggested, such low N might be ascribed to little recruitment of release sites during a train in KD synapses. But our results do not support this model. If silent release sites are recruited during a train, the variance should upwardly deviate from the parabola predicted under a fixed N (Valera et al., 2012; Kobbersmed et al. 2020). Our result was not the case (Fig. 3). In the first version of Ms, we have argued against this possibility in line 203-208.

As discussed in both the Results and Discussion sections, the baseline EPSC was unchanged by KD (Fig. S3) because of complementary changes in the number of docking sites and their baseline occupancy (Fig. 6). These findings suggest that Syt7 may be involved in maintaining additional vacant docking sites, which could be overfilled during facilitation. It remains to be determined whether the decrease in docking sites in Syt7 KD synapses is related to its specific localization of Syt7 at the plasma membrane of active zones, as proposed in previous studies (Sugita et al., 2001; Vevea et al., 2021).

(2) Figure S4A: I like the TTX part of this control, but the 4-AP part needs a positive control to be meaningful (e.g., absence of TTX).

The reason why we used 4-AP in the presence of TTX was to increase the length constant of axon fibers and to facilitate the conduction of local depolarization in the illumination area to axon terminals. The lack of EPSC in the presence of 4-AP and TTX indicates that illumination area is distant from axon terminals enough for optic stimulation-induced local depolarization not to evoke synaptic transmission. This methodology has been employed in previous studies including the work of Little and Carter (2013).

<Reference>

Little JP and Carter AG (2013) Synaptic mechanisms underlying strong reciprocal connectivity between the medial prefrontal cortex and basolateral amygdala. J Neurosci, 33(39): 15333-15342.

(3) Line 251: At least some of the previous studies that concluded these drugs affect vesicle dynamics used logic that was based on some of the same assumptions that are problematic for the present study, so the reasoning is a bit circular.

(4) Line 329 and Line 461: A similar problem with circularity for interpreting earlier syt7 studies.

(Reply to #3 and #4) We selected the target molecules as candidates based on their well-characterized roles in vesicle dynamics, and aimed to investigate what aspects of STP are affected by these molecules in our experimental context. For example, we could find that the baseline pocc and short-term facilitation (STF) are enhanced by the baseline DAG level and train stimulation-induced PLC activation, respectively. Notably, the effect of dynasore informed us that slow site clearing is responsible for the late depression of 40 Hz train EPSC. The knock-down experiments also provided us with information on the critical role of Syt7 in replenishment of TS vesicles. These approaches do not deviate from standard scientific reasoning but rather builds upon prior knowledge to formulate and test hypotheses.

Importantly, our conclusions do not rely solely on the assumption that altering the target molecule impacts synaptic transmission. Instead, our conclusions are derived from a comprehensive analysis of diverse outcomes obtained through both pharmacological and genetic manipulations. These interpretations align closely with prior literature, further validating our conclusions.

Therefore, the use of established studies to guide candidate selection and the consistency of our findings with existing knowledge do not represent a logical circularity but rather a reinforcement of the proposed mechanism through converging lines of evidence.

Author response:

We were pleased to read the positive comments regarding our manuscript and thank the reviewers and editors for the constructive feedback which we believe will be very helpful to improve the current version of the manuscript.

Prior to addressing all comments in a full response, we provide a response to three issues that were raised in this provisional plan for revision: validation of the tracking algorithm, biological replicates, and mosquito survival.

(1) Validation of the tracking algorithm:

Reviewer 2 mentions that there is "No external validation for the flight tracking algorithm using manual annotation". We will address this comment in our full response by creating a manually labelled dataset to validate our detection algorithm.

However, we would like to point out two important points:

i) Quantifying the accuracy of a detection algorithm using a manually annotated set is indeed common practice in deep/machine learning algorithms in which manually annotated data are used to train the algorithm, and another set of manually annotated data is used to validate it. However, our detection and tracking algorithm is based on conventional computer vision techniques (not using any deep learning) that have been in use for several decades. Given that these algorithms are completely transparent and deterministic (as opposed to deep learning algorithms that are difficult to dissect and are created using partly stochastic processes) it is not common practice to use human annotations for validation. However, to address Reviewer 2's comment we will provide validation metrics in our full response.

ii) We furthermore would like to note that our main metrics of interest (e.g. fraction of mosquitoes flying) only depends on accurately detecting mosquitoes and quantifying movement, its accuracy is not affected by potential identity swaps (the typical bottleneck in tracking algorithms).

(2) Replicates:

Reviewer 3 states that "Most experiments are only done with single replicates". This statement is not accurate: In Figure 2 we used 3 independent biological replicates for 4 colonies, 2 of which are Aaa and 2 are Aaf. We indeed provide additional data for 6 more colonies using a single replicate. Combined this data set comprises 588 days of continuous recordings. For Figures 3 and 4 we have 2 replicates for each perturbation experiment. For Figure 5 we provided 3 replicates for the host-seeking experiments. As outlined, the vast majority of our experiments has multiple replicates. We realize this may not have been described clearly enough in the manuscript, we will clarify this in the revised manuscript.

(3) Mosquito survival:

Below we provide survival data for the data shown in Figures 1 - 4, we will include this data as supplementary material. Overall we note here that mortality for all experiments was similar to the 'baseline' mortality we observe in our standard colony maintenance procedures. After three weeks, we typically observed that 70% of mosquitoes were still alive.

Author response image 1.

Survival curves for the data presented in Figures 1 - 4 of the main text. Day 0 indicates the day on which the BuzzWatch experiment started

Author response:

Reply to Reviewer #1 (Public Review):

The post-processing increases number of putative neoantigens. As shown in Author response image 1, this is done through data augmentation or “mutations” of individual amino acids in a sequence by their most similar amino acid in the BLOSUM62 embedding. If most of the mutations result in a positive prediction (which we binarize through a >0.5 score) the sequence changes its prediction.

Author response image 1.

Post-processing pipeline to increase the number of putative neoantigens. Sequences can either be predicted using the forward method, for which a raw score is produced, or it can be introduced to a majority-vote prediction of the ensemble prediction of similar protein sequences.

In this article, we obtain the following candidates after post-processing.

Author response table 1.

As mentioned, the prediction column shows a binary label. The full list contained 402 sequences did not include any other sequences that met the majority vote criteria.

As noted by the reviewer, the Table 3 of our original paper includes the scores of the direct prediction, which has four sequences in common with the post-processing criteria (*Pnp, *Adar, *Lrrc28 and *Nr1h2). * indicates the mutated form of the peptide, i.e neoantigen.

We selected the top 4 predicted antigens (present both by direct prediction and after post-processing; (*Pnp, *Adar, *Lrrc28 and *Nr1h2) (Wert-Carvajal et al. 2021), but we encountered difficulty in synthesizing, *Nr1h2 (Mutated Nr1h2), and thus it could not be included in the study.

We also decided to evaluate the immunogenicity of *Wiz, which was identified as a potential TNA only after postprocessing. *Wiz exhibited lower levels of immunogenicity compared to *Pnp, *Adar, and *Lrrc28. However, unlike these, *Wiz is highly expressed in the tumor, and vaccination with *Wiz provided the strongest protection levels. These findings led us to incorporate post-processingg into the NAP-CNB platform.

We chose *Herc6 as a mutated antigen predicted not to be a TNA over other candidates because its expression in the tumor was similar to that of *Wiz.

Depending on the experiment we used 4 or 5 animals per group (this will be clarify in the revised version)

The software used for statistical analysis was GraphPad Prism.

Reply to Reviewer #2 (Public Review):

This is true, binding affinity does not always predict immune responses but in most cases, high affinity peptides are immunogenic. There are of course other parameters that drive the effective priming of tumor-reactive CD8+ T cells through antigen cross-presentation, but the mechanisms of antigen presentation are yet not completely understood. High affinity peptides are desirable as good candidates in neoantigen-based vaccines.

Author Response

Reviewer #1 (Public Review):

The authors report a new bioinformatics pipeline ("SPICE") to predict pairwise cooperative binding-sites based on input ChIP-seq data for transcription factor (TF)-of-interest, analyzed against DNA-binding sites (DNA motifs) in a database (HOCOMOCO). The pipeline also predicts the optimal distance between the paired binding sites. The pipeline correctly predicted known/reported transcription factor cooperations, and also predicted new cooperations, not yet reported in literature. The authors choose to follow up on the predicted interaction between Ikaros and Jun. Using ChIP-seq in mouse B cells, they show extensive overlap in binding regions between Ikaros and Jun in LPS+IL21 stimulated cells. In a human B-lineage cell line (MINO) they show that anti-Ikaros Ab can co-immunoprecipitate Jun protein, and that the MINO cell extracts contain protein(s) that can bind to the CNS9 probe (conserved region upstream of IL10 gene), and that binding is lost upon mutation of two basepairs in the AP1 binding motif, and reduced upon mutation of two basepairs in the non-canonical Ikaros binding motif. Part of this protein complex is super-shifted with an anti-Jun antibody, and more DNA is shifted with addition of an anti-Ikaros antibody.

The authors perform EMSA showing that recombinant Jun can bind to the tested DNA-region (IL10 CNS9) and that addition of recombinant Ikaros (or anti-Ikaros antibody in Fig 3E) can enhance binding (increase amount of DNA shifted). The authors lastly show that the IL10 CNS9 DNA region can enhance transcription in B- and T-cells with a luciferase reporter assay, and that 2 bp mutation of the Ikaros or Jun DNA motifs greatly reduce or abolish this activity.

This is interesting work, with two main contributions: The SPICE pipeline (if made available to the scientific community), and the report of interaction between Ikaros and Jun. However, the distinction between DNA motifs, and the proteins actually binding and having a biological function, should be made clear consistently throughout the manuscript. The same DNA motifs can be bound by multiple factors, for instance within transcription factor families with highly homology in the DNA-binding regions of the proteins.

The reviewer has correctly assessed the content of our manuscript.

Some specific points:

SPICE: It is unclear if this is uploaded somewhere to be available to the scientific community.

Thanks for this comment. We will upload the SPICE pipeline and its associated scripts (R and shell) via GitHub.

It was unclear if Ikaros-Jun interaction was initially found from primary Jun ChIP-seq (and secondary Ikaros motif from HOCOMOCO) or from primary Ikaros CHIP-seq (and secondary Jun motif from HOCOMOCO). And - what were the two DNA motifs (primary and secondary, and their distance) from the SPICE analysis?

The IKZF1-JUN interaction was found from primary JUN ChIP-seq data and searching for secondary IKZF1 motifs identified in the HOCOMOCO database. We will provide the primary and secondary motifs in our revised manuscript.

Authors have mostly careful considerations and statements. One additional comment is that binding does not equal function (Fig 2D), and that opening of chromatin (by any other factor(s)) can give DNA-binding factors (like Ikaros and Jun) the opportunity to bind, without functional consequence for the biological process studied.

We appreciate that the reviewer believes our considerations and statement are careful. We agree that opening of chromatin can give the opportunity of factors to bind, and we now make this point in the manuscript.

Figure 2E: Ikaros is reported to be expressed at baseline in murine B cells, yet the Ikaros ChIP-seq in unstimulated cells had what looks to be no significant or low peaks. LPS stimulation induced strong Ikaros ChIP-seq signal. A western blot showing the Ikaros protein levels in the 3 conditions could help understand if the binding pattern is due to protein expression level induction. Similar for Jun (western in the 3 conditions), which seemed to mainly bind in the LPS+IL21 condition. Furthermore, as also suggested below, tracks showing Ikaros and Jun binding from all conditions (unstimulated, LPS only and LPS+IL21 stimulated cells), at select genomic loci, would be helpful in illustrating this difference in signal between the different cell conditions. This is relevant in regards to the point of cooperativity of binding.

The main point of the paper was showing functional cooperation and proximity of binding. However, the use of purified JUN and Ikaros protein suggest cooperative binding. Exhaustive evaluation of the JUN-Ikaros association is left for future studies.

ChIP-seq in mouse B cells showed that Ikaros bound strongly in LPS stimulated cells, in the (relative) absence of Jun binding (Fig. 2C). However, in EMSA (Fig 3C), there is no binding when the AP1 site is mutated, and the authors describe this as Ikaros binding site. What does the Ikaros binding look like at this genomic location in LPS (only) stimulated cells? The authors could show the same figure as in Fig 2F but show Ikaros and Jun ChIP-seq tracks at IL10 CNS9 locus from all conditions to compare binding in unstimulated, LPS and LPS+IL21 cells.

As requested, we now show Ikaros and Jun ChIP-seq tracks from unstimulated, LPS-treated, and LPS + IL21-treated cells. Both Ikaros and cJUN were bound to the Il10 upstream CNS9 region with LPS treatment of cells (see Author response image 1, highlighted in red box), but binding was weaker than that observed with LPS + IL21.

Author response image 1.

Also: How does this reconcile with the luciferase assay in Fig 4E, where LPS (only) stimulation is used, which in Fig 2E only/mainly induced Ikaros, and not Jun ChIP-seq signal (while EMSA indicate Ikaros cannot bind the site alone, but can enhance Jun-dependent binding).

As shown above, in the LPS (only) condition, both IKZF1 (Ikaros) and cJUN bind to Il10 CNS9 locus. Thus, this is not in conflict with our luciferase assay data in Fig. 4E, which showed Ikaros is dependent on AP-1 binding. Moreover, the AP-1 site in Fig. 4D and 4E can be bound by other AP-1 factors as well, such as JUND, JUNB, BATF, etc. These points can be made in the manuscript. These factors potentially can compete with cJUN binding and their roles remain to be explored.

Comment on statements in results section: The luciferase assays in B and T cells do not demonstrate the role of the proteins Ikaros or Jun directly (page 10, lines 208 and surrounding text). The assay measures an effect of the DNA sequences (implying binding of some transcription factor(s)), but does not identify which protein factors bind there.

We agree with the reviewer. It is reasonable and even likely that different family members may be partially redundant. This point is now made on our revised manuscript.

Lastly, the authors only discuss Ikaros (using the term IKZF1 which is the gene symbol for the Ikaros protein). There are other Ikaros family members that have high homology and that are reported to bind similar DNA sequences (for instance Aiolos and Helios), which are expressed in B-cells and T-cells. A discussion of this is of relevance, as these are different proteins, although belonging to the same family (the Ikaros-family) of transcription factors. For instance, western for Aiolos and Helios will likely detect Aiolos in the B cells used, and Helios in the T cells used.

We agree with the reviewer. As requested, we now discuss the possibility that Aiolos or Helios may also contribute.

Reviewer #2 (Public Review):

The study is performed with old tool Spamo (12 year ago), source data from Encode (2010-2012), even peak caller tool version MACS is old ~ 2013. De novo motif search tool is old too (new one STREME is not mentioned). Any composite element search tool published for the recent 12 years are not cited, there are some issues in data analysis in presentation. Almost all references are from about 8-10 year ago (the most recent date is 2019)

The title is misleading

Instead of “A new pipeline SPICE identifies novel JUN-IKZF1 composite elements”

It should be written as “Application of SpaMo tool identifies novel JUN-IKZF1 composite elements”

It reflects the pipeline better but honestly shows that the novelty is missed.

Regarding the above two points, we respectfully disagree with the reviewer. Although SpaMo was used, the pipeline we developed is new and our findings are distinctive. The pipeline can systematically screen and predict novel protein-protein binding complex, and our discovery related to IKZF1-JUN composite element is new and the biological findings and validation are distinctive. This point is now made in the revised manuscript. As requested, we have added some additional references.

The study was performed on too old data from ENCODE, authors mentioned 343 Encode ChIP-Seq libraries, but authors even did not care even about to set for each library the name of target TF (Figure 1E, Figure S2, Table 2).

Although we used ENCODE data, which was in part when we initially developed the algorithm, those data are valid and using them allowed us to demonstrate the functionality of SPICE, which is versatile and can be used on datasets of one’s choice as well. As requested, in the revised manuscript we have added the names of the TFs in Figs, Fig. S2, and Table 1.

Reviewer #3 (Public Review):

The authors of this study have designed a novel screening pipeline to detect DNA motif spacing preferences between TF partners using publicly available data. They were able to recapitulate previously known composite elements, such as the AP-1/IRF4 composite elements (AICE) and predict many composite elements that are expected to be very useful to the community of researchers interested in dissecting the regulatory logic of mammalian enhancers and promoters. The authors then focus on a novel, SPICE predicted interaction between JUN and IKZF1, and show that under LPS and IL-21 treatment, JUN and IKZF1 in B cells have significant overlap in their genomic localization. Next, to know whether the two TFs physically interact, a co-immunoprecipitation experiment was performed. While JUN immunoprecipitated with an anti-IKZF1 antibody, curiously IKZF1 did not immunoprecipitate with an anti-JUN antibody. Finally, EMSA and luciferase experiments were performed to show that the two TFs bind cooperatively at an IL20 upstream probe.

The reviewer has described the basic results of the study.

Major strengths:

1) SPICE was able to recapitulate previously known composite elements, such as the AP-1/IRF4 composite elements (AICE).

2) Under LPS and IL-21 treatment, JUN and IKZF1 in B cells have significant overlap in their genomic localization. This is very good supporting evidence for the efficacy of SPICE in detecting TF partners.

We are glad that the reviewer believes that SPICE is effective in detecting TF partners.

Major weaknesses:

1) The authors fail to convincingly show that IKZF1 and Jun physically interact. A quantitative measurement of their interaction strength would have been ideal.

We agree that it is not conclusive that the factors interact directly as opposed to binding to nearby sites on DNA, which is what SPICE was intended to detect. We never intended to claim that we established a definite physical interaction. The coIP worked in one direction, but not reliably in the other, even though we have tried a total of four different antibodies. We now mention in the revised manuscript that we have tried the additional anti-JUN antibodies, cJun (60A8, CST) and JunD (D17G2, CST).

2) The super-shift experiment to show that the proteins bound to their EMSA probe were indeed IKZF1 and JUN are not very convincing and would benefit from efforts to quantify the shift (Figure 3E). Nuclear extracts from cells with single or double CRISPR knock outs of the two TFs would have been ideal.

We agree that using single or double knockouts would be helpful, but other Ikaros family or Jun family members could be involved, so such studies might not be definitive. That is why we used purified proteins to show apparent cooperative binding (Figure 4C).

3) There is a second band beneath the more prominent band in the EMSA experiment with recombinant IKZF1 and JUN (Figure 4C). This second band is most probably bound by IKZF1 because it becomes weaker when the IKZF1 site is mutated and is completely absent when only JUN is added. This is completely ignored by the authors. Therefore, experiments with EMSA fail to convincingly show that IKZF1 and Jun bind cooperatively. They could just as well bind independently to the two sites.

The second band has a faster mobility and might relate to IKZF1, although this is difficult to know. We comment on this band on revised manuscript. As noted above, the purified protein experiments do suggest cooperativity. However, our overall intent was to identify factors binding in proximity, which SPICE has successfully done, even if the binding was “independent”.