Reviewer #2 (Public review):

Summary:

This manuscript reports analyses of fMRI data from infants and toddlers watching naturalistic movies. Visual areas in the infant brain show distinct functions, consistent with previous studies using resting state and awake task-based infant fMRI. The pattern of activity in visual regions contains some features predicted by the regions' retinotopic responses. The revised version of the manuscript provides additional validation of the methodology and clarifies the claims. As a result, the data provide clear support for the claims.

Strengths:

The authors have collected a unique dataset: the same individual infants both watched naturalistic animations and a specific retinotopy task. Using these data positions the authors show that activity evoked by movies, in infants' visual areas, is correlated with the regions' retinopic response. The revised manuscript validates this methodology, using adult data. The revised manuscript also shows that an infant's movie-watching data is not sufficient or optimal to predict their visual areas' retinotopic responses; anatomical alignment with a group of previous participants provides more accurate prediction of a new participant's retinotopic response.

Weaknesses:

A key step in the analysis of the movie-watching data is the selection of independent components of the movie evoked response, by a trained researcher, that resemble retinotopic spatial patterns. While the researcher is unlikely to be biased by this infant's own retinotopy , as the authors argue, the researcher is actively looking for ICs that resemble average patterns of retinotopic response. So, how likely is it that ICs that resemble retinotopic organization arise by chance (i.e. in noise) in infant fMRI data? I do not see an analysis that addresses this question. With apologies if I missed it.

Reviewer #3 (Public review):

The manuscript reports data collected in awake toddlers recording BOLD while watching videos. The authors analyse the BOLD time series using two different statistical approaches, both very complex but that do not require any a priori determination of the movies features or contents to be associated with regressors. The two main messages are that 1) toddlers have occipital visual areas very similar to adults, given that a SRM model derive from adults BOLD is consistent with the infant brains as well; 2) the retinotopic organization and the spatial frequency selectivity of the occipital maps derived by applying correlation analysis are consistent with the maps obtained by standard and conventional mapping.

Comments on revised version:

The authors did a thorough revision of the manuscript which now is very clear. All the missing information has been added and the technical issue clarified. I think that it is a very good and important paper.

Author response:

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

eLife assessment

This study presents valuable findings on the potential of short-movie viewing fMRI protocol to explore the functional and topographical organization of the visual system in awake infants and toddlers. Although the data are compelling given the difficulty of studying this population, the evidence presented is incomplete and would be strengthened by additional analyses to support the authors' claims. This study will be of interest to cognitive neuroscientists and developmental psychologists, especially those interested in using fMRI to investigate brain organisation in pediatric and clinical populations with limited fMRI tolerance.

We are grateful for the thorough and thoughtful reviews. We have provided point-bypoint responses to the reviewers’ comments, but first, we summarize the major revisions here. We believe these revisions have substantially improved the clarity of the writing and impact of the results.

Regarding the framing of the paper, we have made the following major changes in response to the reviews:

(1) We have clarified that our goal in this paper was to show that movie data contains topographic, fine-grained details of the infant visual cortex. In the revision, we now state clearly that our results should not be taken as evidence that movies could replace retinotopy and have reworded parts of the manuscript that could mislead the reader in this regard.

(2) We have added extensive details to the (admittedly) complex methods to make them more approachable. An example of this change is that we have reorganized the figure explaining the Shared Response Modelling methods to divide the analytic steps more clearly.

(3) We have clarified the intermediate products contributing to the results by adding 6 supplementary figures that show the gradients for each IC or SRM movie and each infant participant.

In response to the reviews, we have conducted several major analyses to support our findings further:

(1) To verify that our analyses can identify fine-grained organization, we have manually traced and labeled adult data, and then performed the same analyses on them. The results from this additional dataset validate that these analyses can recover fine-grained organization of the visual cortex from movie data.

(2) To further explore how visual maps derived from movies compare to alternative methods, we performed an anatomical alignment control analysis. We show that high-quality maps can be predicted from other participants using anatomical alignment.

(3) To test the contribution of motion to the homotopy analyses, we regressed out the motion effects in these analyses. We found qualitatively similar results to our main analyses, suggesting motion did not play a substantial role.

(4) To test the contribution of data quantity to the homotopy analyses, we correlated the amount of movie data collected from each participant with the homotopy results. We did not find a relationship between data quantity and the homotopy results. 

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Ellis et al. investigated the functional and topographical organization of the visual cortex in infants and toddlers, as evidenced by movie-viewing data. They build directly on prior research that revealed topographic maps in infants who completed a retinotopy task, claiming that even a limited amount of rich, naturalistic movie-viewing data is sufficient to reveal this organization, within and across participants. Generating this evidence required methodological innovations to acquire high-quality fMRI data from awake infants (which have been described by this group, and elsewhere) and analytical creativity. The authors provide evidence for structured functional responses in infant visual cortex at multiple levels of analyses; homotopic brain regions (defined based on a retinotopy task) responded more similarly to one another than to other brain regions in visual cortex during movie-viewing; ICA applied to movie-viewing data revealed components that were identifiable as spatial frequency, and to a lesser degree, meridian maps, and shared response modeling analyses suggested that visual cortex responses were similar across infants/toddlers, as well as across infants/toddlers and adults. These results are suggestive of fairly mature functional response profiles in the visual cortex in infants/toddlers and highlight the potential of movie-viewing data for studying finer-grained aspects of functional brain responses, but further evidence is necessary to support their claims and the study motivation needs refining, in light of prior research.

Strengths:

- This study links the authors' prior evidence for retinotopic organization of visual cortex in human infants (Ellis et al., 2021) and research by others using movie-viewing fMRI experiments with adults to reveal retinotopic organization (Knapen, 2021).

- Awake infant fMRI data are rare, time-consuming, and expensive to collect; they are therefore of high value to the community. The raw and preprocessed fMRI and anatomical data analyzed will be made publicly available.

We are grateful to the reviewer for their clear and thoughtful description of the strengths of the paper, as well as their helpful outlining of areas we could improve.

Weaknesses:

- The Methods are at times difficult to understand and in some cases seem inappropriate for the conclusions drawn. For example, I believe that the movie-defined ICA components were validated using independent data from the retinotopy task, but this was a point of confusion among reviewers. 

We acknowledge the complexity of the methods and wish to clarify them as best as possible for the reviewers and the readers. We have extensively revised the methods and results sections to help avoid potential misunderstandings. For instance, we have revamped the figure and caption describing the SRM pipeline (Figure 5).

To answer the stated confusion directly, the ICA components were derived from the movie data and validated on the (completely independent) retinotopy data. There were no additional tasks. The following text in the paper explains this point:

“To assess the selected component maps, we correlated the gradients (described above) of the task-evoked and component maps. This test uses independent data: the components were defined based on movie data and validated against task-evoked retinotopic maps.” Pg. 11

In either case: more analyses should be done to support the conclusion that the components identified from the movie reproduce retinotopic maps (for example, by comparing the performance of movie-viewing maps to available alternatives (anatomical ROIs, group-defined ROIs). 

Before addressing this suggestion, we want to restate our conclusions: features of the retinotopic organization of infant visual cortex could be predicted from movie data. We did not conclude that movie data could ‘reproduce’ retinotopic maps in the sense that they would be a replacement. We recognize that this was not clear in our original manuscript and have clarified this point throughout, including in this section of the discussion:

“To be clear, we are not suggesting that movies work well enough to replace a retinotopy task when accurate maps are needed. For instance, even though ICA found components that were highly correlated with the spatial frequency map, we also selected some components that turned out to have lower correlations. Without knowing the ground truth from a retinotopy task, there would be no way to weed these out. Additionally, anatomical alignment (i.e., averaging the maps from other participants and anatomically aligning them to a held-out participant) resulted in maps that were highly similar to the ground truth. Indeed, we previously23 found that adult-defined visual areas were moderately similar to infants. While functional alignment with adults can outperform anatomical alignment methods in similar analyses27, here we find that functional alignment is inferior to anatomical alignment. Thus, if the goal is to define visual areas in an infant that lacks task-based retinotopy, anatomical alignment of other participants’ retinotopic maps is superior to using movie-based analyses, at least as we tested it.” Pg. 21

As per the reviewer’s suggestion and alluded to in the paragraph above, we have created anatomically aligned visual maps, providing an analogous test to the betweenparticipant analyses like SRM. We find that these maps are highly similar to the ground truth. We describe this result in a new section of the results:

“We performed an anatomical alignment analog of the functional alignment (SRM) approach. This analysis serves as a benchmark for predicting visual maps using taskbased data, rather than movie data, from other participants. For each infant participant, we aggregated all other infant or adult participants as a reference. The retinotopic maps from these reference participants were anatomically aligned to the standard surface template, and then averaged. These averages served as predictions of the maps in the test participant, akin to SRM, and were analyzed equivalently (i.e., correlating the gradients in the predicted map with the gradients in the task-based map). These correlations (Table S4) are significantly higher than for functional alignment (using infants to predict spatial frequency, anatomical alignment > functional alignment: ∆Fisher Z M=0.44, CI=[0.32–0.58], p<.001; using infants to predict meridians, anatomical alignment > functional alignment: ∆Fisher Z M=0.61, CI=[0.47–0.74], p<.001; using adults to predict spatial frequency, anatomical alignment > functional alignment: ∆Fisher Z

M=0.31, CI=[0.21–0.42], p<.001; using adults to predict meridians, anatomical alignment > functional alignment: ∆Fisher Z M=0.49, CI=[0.39–0.60], p<.001). This suggests that even if SRM shows that movies can be used to produce retinotopic maps that are significantly similar to a participant, these maps are not as good as those that can be produced by anatomical alignment of the maps from other participants without any movie data.” Pg. 16–17

Also, the ROIs used for the homotopy analyses were defined based on the retinotopic task rather than based on movie-viewing data alone - leaving it unclear whether movie-viewing data alone can be used to recover functionally distinct regions within the visual cortex.

We agree with the reviewer that our approach does not test whether movie-viewing data alone can be used to recover functionally distinct regions. The goal of the homotopy analyses was to identify whether there was functional differentiation of visual areas in the infant brain while they watch movies. This was a novel question that provides positive evidence that these regions are functionally distinct. In subsequent analyses, we show that when these areas are defined anatomically, rather than functionally, they also show differentiated function (e.g., Figure 2). Nonetheless, our intention was not to use the homotopy analyses to define the regions. We have added text to clarify the goal and novelty of this analysis.

“Although these analyses cannot define visual maps, they test whether visual areas have different functional signatures.” Pg. 6

Additionally, even if the goal were to define areas based on homotopy, we believe the power of that analysis would be questionable. We would need to use a large amount of the movie data to define the areas, leaving a low-powered dataset to test whether their function is differentiated by these movie-based areas.

- The authors previously reported on retinotopic organization of the visual cortex in human infants (Ellis et al., 2021) and suggest that the feasibility of using movie-viewing experiments to recover these topographic maps is still in question. They point out that movies may not fully sample the stimulus parameters necessary for revealing topographic maps/areas in the visual cortex, or the time-resolution constraints of fMRI might limit the use of movie stimuli, or the rich, uncontrolled nature of movies might make them inferior to stimuli that are designed for retinotopic mapping, or might lead to variable attention between participants that makes measuring the structure of visual responses across individuals challenging. This motivation doesn't sufficiently highlight the importance or value of testing this question in infants. Further, it's unclear if/how this motivation takes into account prior research using movie-viewing fMRI experiments to reveal retinotopic organization in adults (e.g., Knapen, 2021). Given the evidence for retinotopic organization in infants and evidence for the use of movie-viewing experiments in adults, an alternative framing of the novel contribution of this study is that it tests whether retinotopic organization is measurable using a limited amount of movie-viewing data (i.e., a methodological stress test). The study motivation and discussion could be strengthened by more attention to relevant work with adults and/or more explanation of the importance of testing this question in infants (is the reason to test this question in infants purely methodological - i.e., as a way to negate the need for retinotopic tasks in subsequent research, given the time constraints of scanning human infants?).

We are grateful to the reviewer for giving us the opportunity to clarify the innovations of this research. We believe that this research contributes to our understanding of how infants process dynamic stimuli, demonstrates the viability and utility of movie experiments in infants, and highlights the potential for new movie-based analyses (e.g., SRM). We have now consolidated these motivations in the introduction to more clearly motivate this work:

“The primary goal of the current study is to investigate whether movie-watching data recapitulates the organization of visual cortex. Movies drive strong and naturalistic responses in sensory regions while minimizing task demands12, 13, 24 and thus are a proxy for typical experience. In adults, movies and resting-state data have been used to characterize the visual cortex in a data-driven fashion25–27. Movies have been useful in awake infant fMRI for studying event segmentation28, functional alignment29, and brain networks30. However, this past work did not address the granularity and specificity of cortical organization that movies evoke. For example, movies evoke similar activity in infants in anatomically aligned visual areas28, but it remains unclear whether responses to movie content differ between visual areas (e.g., is there more similarity of function within visual areas than between31). Moreover, it is unknown whether structure within visual areas, namely visual maps, contributes substantially to visual evoked activity. Additionally, we wish to test whether methods for functional alignment can be used with infants. Functional alignment finds a mapping between participants using functional activity – rather than anatomy – and in adults can improve signal-to-noise, enhance across participant prediction, and enable unique analyses27, 32–34.” Pg. 3-4

Furthermore, the introduction culminates in the following statement on what the analyses will tell us about the nature of movie-driven activity in infants:

“These three analyses assess key indicators of the mature visual system: functional specialization between areas, organization within areas, and consistency between individuals.” Pg. 5

Furthermore, in the discussion we revisit these motivations and elaborate on them further:

[Regarding homotopy:] “This suggests that visual areas are functionally differentiated in infancy and that this function is shared across hemispheres31.” Pg. 19

[Regarding ICA:] “This means that the retinotopic organization of the infant brain accounts for a detectable amount of variance in visual activity, otherwise components resembling these maps would not be discoverable.” Pg. 19–20

[Regarding SRM:] “This is initial evidence that functional alignment may be useful for enhancing signal quality, like it has in adults27,32,33, or revealing changing function over development45.” Pg. 21

Additionally, we have expanded our discussion of relevant work that uses similar methods such as the excellent research from Knapen (2021) and others:

“In adults, movies and resting-state data have been used to characterize the visual cortex in a data-driven fashion25-27.” Pg. 4

“We next explored whether movies can reveal fine-grained organization within visual areas by using independent components analysis (ICA) to propose visual maps in individual infant brains25,26,35,42,43.” Pg. 9

Reviewer #2 (Public Review):

Summary:

This manuscript shows evidence from a dataset with awake movie-watching in infants, that the infant brain contains areas with distinct functions, consistent with previous studies using resting state and awake task-based infant fMRI. However, substantial new analyses would be required to support the novel claim that movie-watching data in infants can be used to identify retinotopic areas or to capture within-area functional organization.

Strengths:

The authors have collected a unique dataset: the same individual infants both watched naturalistic animations and a specific retinotopy task. These data position the authors to test their novel claim, that movie-watching data in infants can be used to identify retinotopic areas.

Weaknesses:

To claim that movie-watching data can identify retinotopic regions, the authors should provide evidence for two claims:

- Retinotopic areas defined based only on movie-watching data, predict retinotopic responses in independent retinotopy-task-driven data.

- Defining retinotopic areas based on the infant's own movie-watching response is more accurate than alternative approaches that don't require any movie-watching data, like anatomical parcellations or shared response activation from independent groups of participants.

We thank the reviewer for their comments. Before addressing their suggestions, we wish to clarify that we do not claim that movie data can be used to identify retinotopic areas, but instead that movie data captures components of the within and between visual area organization as defined by retinotopic mapping. We recognize that this was not clear in our original manuscript and have clarified this point throughout, including in this section of the discussion:

“To be clear, we are not suggesting that movies work well enough to replace a retinotopy task when accurate maps are needed. For instance, even though ICA found components that were highly correlated with the spatial frequency map, we also selected some components that turned out to have lower correlations. Without knowing the ground truth from a retinotopy task, there would be no way to weed these out. Additionally, anatomical alignment (i.e., averaging the maps from other participants and anatomically aligning them to a held-out participant) resulted in maps that were highly similar to the ground truth. Indeed, we previously23 found that adult-defined visual areas were moderately similar to infants. While functional alignment with adults can outperform anatomical alignment methods in similar analyses27, here we find that functional alignment with infants is inferior to anatomical alignment. Thus, if the goal is to define visual areas in an infant that lacks task-based retinotopy, anatomical alignment of other participants’ retinotopic maps is superior to using movie-based analyses, at least as we tested it.” Pg. 21

In response to the reviewer’s suggestion, we compare the maps identified by SRM to the averaged, anatomically aligned maps from infants. We find that these maps are highly similar to the task-based ground truth and we describe this result in a new section:

“We performed an anatomical alignment analog of the functional alignment (SRM) approach. This analysis serves as a benchmark for predicting visual maps using taskbased data, rather than movie data, from other participants. For each infant participant, we aggregated all other infant or adult participants as a reference. The retinotopic maps from these reference participants were anatomically aligned to the standard surface template, and then averaged. These averages served as predictions of the maps in the test participant, akin to SRM, and were analyzed equivalently (i.e., correlating the gradients in the predicted map with the gradients in the task-based map). These correlations (Table S4) are significantly higher than for functional alignment (using infants to predict spatial frequency, anatomical alignment < functional alignment: ∆Fisher Z M=0.44, CI=[0.32–0.58], p<.001; using infants to predict meridians, anatomical alignment < functional alignment: ∆Fisher Z M=0.61, CI=[0.47–0.74], p<.001; using adults to predict spatial frequency, anatomical alignment < functional alignment: ∆Fisher Z

M=0.31, CI=[0.21–0.42], p<.001; using adults to predict meridians, anatomical alignment < functional alignment: ∆Fisher Z M=0.49, CI=[0.39–0.60], p<.001). This suggests that even if SRM shows that movies can be used to produce retinotopic maps that are significantly similar to a participant, these maps are not as good as those that can be produced by anatomical alignment of the maps from other participants without any movie data.” Pg. 16–17

Note that we do not compare the anatomically aligned maps with the ICA maps statistically. This is because these analyses are not comparable: ICA is run within-participant whereas anatomical alignment is necessarily between-participant — either infant or adults. Nonetheless, an interested reader can refer to the Table where we report the results of anatomical alignment and see that anatomical alignment outperforms ICA in terms of the correlation between the predicted and task-based maps.

Both of these analyses are possible, using the (valuable!) data that these authors have collected, but these are not the analyses that the authors have done so far. Instead, the authors report the inverse of (1): regions identified by the retinotopy task can be used to predict responses in the movies. The authors report one part of (2), shared responses from other participants can be used to predict individual infants' responses in the movies, but they do not test whether movie data from the same individual infant can be used to make better predictions of the retinotopy task data, than the shared response maps.

So to be clear, to support the claims of this paper, I recommend that the authors use the retinotopic task responses in each individual infant as the independent "Test" data, and compare the accuracy in predicting those responses, based on:

-  The same infant's movie-watching data, analysed with MELODIC, when blind experimenters select components for the SF and meridian boundaries with no access to the ground-truth retinotopy data.

-  Anatomical parcellations in the same infant.

-  Shared response maps from groups of other infants or adults.

-  (If possible, ICA of resting state data, in the same infant, or from independent groups of infants).

Or, possibly, combinations of these techniques.

If the infant's own movie-watching data leads to improved predictions of the infant's retinotopic task-driven response, relative to these existing alternatives that don't require movie-watching data from the same infant, then the authors' main claim will be supported.

These are excellent suggestions for additional analyses to test the suitability for moviebased maps to replace task-based maps. We hope it is now clear that it was never our intention to claim that movie-based data could replace task-based methods. We want to emphasize that the discoveries made in this paper — that movies evoke fine-grained organization in infant visual cortex — do not rely on movie-based maps being better than alternative methods for producing maps, such as the newly added anatomical alignment.

The proposed analysis above solves a critical problem with the analyses presented in the current manuscript: the data used to generate maps is identical to the data used to validate those maps. For the task-evoked maps, the same data are used to draw the lines along gradients and then test for gradient organization. For the component maps, the maps are manually selected to show the clearest gradients among many noisy options, and then the same data are tested for gradient organization. This is a double-dipping error. To fix this problem, the data must be split into independent train and test subsets.

We appreciate the reviewer’s concern; however, we believe it is a result of a miscommunication in our analytic strategy. We have now provided more details on the analyses to clarify how double-dipping was avoided. 

To summarize, a retinotopy task produced visual maps that were used to trace both area boundaries and gradients across the areas. These data were then fixed and unchanged, and we make no claims about the nature of these maps in this paper, other than to treat them as the ground truth to be used as a benchmark in our analyses. The movie data, which are collected independently from the same infant in the session, used the boundaries from the retinotopy task (in the case of homotopy) or were compared with the maps from the retinotopy task (in the case of ICA and SRM). In other words, the statement that “the data used to generate maps is identical to the data used to validate those maps” is incorrect because we generated the maps with a retinotopy task and validated the maps with the movie data. This means no double dipping occurred.

Perhaps a cause of the reviewer’s interpretation is that the gradients used in the analysis are not clearly described. We now provide this additional description:  “Using the same manually traced lines from the retinotopy task, we measured the intensity gradients in each component from the movie-watching data. We can then use the gradients of intensity in the retinotopy task-defined maps as a benchmark for comparison with the ICA-derived maps.” Pg. 10

Regarding the SRM analyses, we take great pains to avoid the possibility of data contamination. To emphasize how independent the SRM analysis is, the prediction of the retinotopic map from the test participant does not use their retinotopy data at all; in fact, the predicted maps could be made before that participant’s retinotopy data were ever collected. To make this prediction for a test participant, we need to learn the inversion of the SRM, but this only uses the movie data of the test participant. Hence, there is no double-dipping in the SRM analyses. We have elaborated on this point in the revision, and we remade the figure and its caption to clarify this point:

We also have updated the description of these results to emphasize how double-dipping was avoided:

“We then mapped the held-out participant's movie data into the learned shared space without changing the shared space (Figure 5c). In other words, the shared response model was learned and frozen before the held-out participant’s data was considered.

This approach has been used and validated in prior SRM studies45.” Pg. 14

The reviewer suggests that manually choosing components from ICA is double-dipping. Although the reviewer is correct that the manual selection of components in ICA means that the components chosen ought to be good candidates, we are testing whether those choices were good by evaluating those components against the task-based maps that were not used for the ICA. Our statistical analyses evaluate whether the components chosen were better than the components that would have been chosen by random chance. Critically: all decisions about selecting the components happen before the components are compared to the retinotopic maps. Hence there is no double-dipping in the selection of components, as the choice of candidate ICA maps is not informed by the ground-truth retinotopic maps. We now clarify what the goal of this process is in the results:

“Success in this process requires that 1) retinotopic organization accounts for sufficient variance in visual activity to be identified by ICA and 2) experimenters can accurately identify these components.” Pg. 10

The reviewer also alludes to a concern that the researcher selecting the maps was not blind to the ground-truth retinotopic maps from participants and this could have influenced the results. In such a scenario, the researcher could have selected components that have the gradients of activity in the places that the infant has as ground truth. The researcher who made the selection of components (CTE) is one of the researchers who originally traced the areas in the participants approximately a year prior to the identification of ICs. The researcher selecting the components didn’t use the ground-truth retinotopic maps as reference, nor did they pay attention to the participant IDs when sorting the IC components. Indeed, they weren’t trying to find participants-specific maps per se, but rather aimed to find good candidate retinotopic maps in general. In the case of the newly added adult analyses, the ICs were selected before the retinotopic mapping was reviewed or traced; hence, no knowledge about the participant-specific ground truth could have influenced the selection of ICs. Even with this process from adults, we find results of comparable strength as we found in infants, as shown in Figure S3. Nonetheless, there is a possibility that this researcher’s previous experience of tracing the infant maps could have influenced their choice of components at the participant-specific level. If so, it was a small effect since the components the researcher selected were far from the best possible options (i.e., rankings of the selected components averaged in the 64th percentile for spatial frequency maps and the 68th percentile for meridian maps). We believe all reasonable steps were taken to mitigate bias in the selection of ICs.

Reviewer #3 (Public Review):

The manuscript reports data collected in awake toddlers recording BOLD while watching videos. The authors analyse the BOLD time series using two different statistical approaches, both very complex but do not require any a priori determination of the movie features or contents to be associated with regressors. The two main messages are that 1) toddlers have occipital visual areas very similar to adults, given that an SRM model derived from adult BOLD is consistent with the infant brains as well; 2) the retinotopic organization and the spatial frequency selectivity of the occipital maps derived by applying correlation analysis are consistent with the maps obtained by standard and conventional mapping.

Clearly, the data are important, and the author has achieved important and original results. However, the manuscript is totally unclear and very difficult to follow; the figures are not informative; the reader needs to trust the authors because no data to verify the output of the statistical analysis are presented (localization maps with proper statistics) nor so any validation of the statistical analysis provided. Indeed what I think that manuscript means, or better what I understood, may be very far from what the authors want to present, given how obscure the methods and the result presentation are.

In the present form, this reviewer considers that the manuscript needs to be totally rewritten, the results presented each technique with appropriate validation or comparison that the reader can evaluate.

We are grateful to the reviewer for the chance to improve the paper. We have broken their review into three parts: clarification of the methods, validation of the analyses, and enhancing the visualization.

Clarification of the methods

We acknowledge that the methods we employed are complex and uncommon in many fields of neuroimaging. That said, numerous papers have conducted these analyses on adults (Beckman et al., 2005; Butt et al., 2015; Guntupalli et al., 2016; Haak & Beckman, 2018; Knapen, 2021; Lu et al., 2017) and non-human primates (Arcaro & Livingstone, 2017; Moeller et al., 2009). We have redoubled our efforts in the revision to make the methods as clear as possible, expanding on the original text and providing intuitions where possible. These changes have been added throughout and are too vast in number to repeat here, especially without context, but we hope that readers will have an easier time following the analyses now. 

Additionally, we updated Figures 3 and 5 in which the main ICA and SRM analyses are described. For instance, in Figure 3’s caption we now add details about how the gradient analyses were performed on the components: 

“We used the same lines that were manually traced on the task-evoked map to assess the change in the component’s response. We found a monotonic trend within area from medial to lateral, just like we see in the ground truth.” Pg. 11

Regarding Figure 5, we reconsidered the best way to explain the SRM analyses and decided it would be helpful to partition the diagram into steps, reflecting the analytic process. These updates have been added to Figure 5, and the caption has been updated accordingly.

We hope that these changes have improved the clarity of the methods. For readers interested in learning more, we encourage them to either read the methods-focused papers that debut the analyses (e.g., Chen et al., 2015), read the papers applying the methods (e.g., Guntupalli et al., 2016), or read the annotated code we publicly release which implements these pipelines and can be used to replicate the findings.

Validation of the analyses

One of the requests the reviewer makes is to validate our analyses. Our initial approach was to lean on papers that have used these methods in adults or primates (e.g., Arcaro,

& Livingstone, 2017; Beckman et al., 2005; Butt et al., 2015; Guntupalli et al., 2016; Haak & Beckman, 2018; Knapen, 2021; Moeller et al., 2009) where the underlying organization and neurophysiology is established. However, we have made changes to these methods that differ from their original usage (e.g., we used SRM rather than hyperalignment, we use meridian mapping rather than traveling wave retinotopy, we use movie-watching data rather than rest). Hence, the specifics of our design and pipeline warrant validation. 

To add further validation, we have rerun the main analyses on an adult sample. We collected 8 adult participants who completed the same retinotopy task and a large subset of the movies that infants saw. These participants were run under maximally similar conditions to infants (i.e., scanned using the same parameters and without the top of the head-coil) and were preprocessed using the same pipeline. Given that the relationship between adult visual maps and movie-driven (or resting-state) analyses has been shown in many studies (Beckman et al., 2005; Butt et al., 2015; Guntupalli et al., 2016; Haak & Beckman, 2018; Knapen, 2021; Lu et al., 2017), these adult data serve as a validation of our analysis pipeline. These adult participants were included in the original manuscript; however, they were previously only used to support the SRM analyses (i.e., can adults be used to predict infant visual maps). The adult results are described before any results with infants, as a way to engender confidence. Moreover, we have provided new supplementary figures of the adult results that we hope will be integrated with the article when viewing it online, such that it will be easy to compare infant and adult results, as per the reviewer’s request. 

As per the figures and captions below, the analyses were all successful with the adult participants: 1) Homotopic correlations are higher than correlations between comparable areas in other streams or areas that are more distant within stream. 2) A multidimensional scaling depiction of the data shows that areas in the dorsal and ventral stream are dissimilar. 3) Using independent components analysis on the movie data, we identified components that are highly correlated with the retinotopy task-based spatial frequency and meridian maps. 4) Using shared response modeling on the movie data, we predicted maps that are highly correlated with the retinotopy task-based spatial frequency and meridian maps.

These supplementary analyses are underpowered for between-group comparisons, so we do not statistically compare the results between infants and adults. Nonetheless, the pattern of adult results is comparable overall to the infant results. 

We believe these adult results provide a useful validation that the infant analyses we performed can recover fine-grained organization.

The reviewer raises an additional concern about the lack of visualization of the results. We recognize that the plots of the summary statistics do not provide information about the intermediate analyses. Indeed, we think the summary statistics can understate the degree of similarity between the components or predicted visual maps and the ground truth. Hence, we have added 6 new supplementary figures showing the intensity gradients for the following analyses: 1. spatial frequency prediction using ICA, 2. meridian prediction using ICA, 3. spatial frequency prediction using infant SRM, 4.

meridian prediction using infant SRM, 5. spatial frequency prediction using adult SRM, and 6. meridian prediction using adult SRM.

We hope that these visualizations are helpful. It is possible that the reviewer wishes us to also visually present the raw maps from the ICA and SRM, akin to what we show in Figure 3A and 3B. We believe this is out of scope of this paper: of the 1140 components that were identified by ICA, we selected 36 for spatial frequency and 17 for meridian maps. We also created 20 predicted maps for spatial frequency and 20 predicted meridian maps using SRM. This would result in the depiction of 93 subfigures, requiring at least 15 new full-page supplementary figures to display with adequate resolution. Instead, we encourage the reader to access this content themselves: we have made the code to recreate the analyses publicly available, as well as both the raw and preprocessed data for these analyses, including the data for each of these selected maps.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) As mentioned in the public review, the authors should consider incorporating relevant adult fMRI research into the Introduction and explain the importance of testing this question in infants.

Our public response describes the several citations to relevant adult research we have added, and have provided further motivation for the project.

(2) The authors should conduct additional analyses to support their conclusion that movie data alone can generate accurate retinotopic maps (i.e., by comparing this approach to other available alternatives).

We have clarified in our public response that we did not wish to conclude that movie data alone can generate accurate retinotopic maps, and have made substantial edits to the text to emphasize this. Thus, because this claim is already not supported by our analyses, we do not think it is necessary to test it further.

(3) The authors should re-do the homotopy analyses using movie-defined ROIs (i.e., by splitting the movie-viewing data into independent folds for functional ROI definition and analyses).

As stated above, defining ROIs based on the movie content is not the intended goal of this project. Even if that were the general goal, we do not believe that it would be appropriate to run this specific analysis with the data we collected. Firstly, halving the data for ROI definition (e.g., using half the movie data to identify and trace areas, and then use those areas in the homotopy analysis to run on the other half of data) would qualitatively change the power of the analyses described here. Secondly, we would be unable to define areas beyond hV4/V3AB with confidence, since our retinotopic mapping only affords specification of early visual cortex. Thus we could not conduct the MDS analyses shown in Figure 2.

(4) If the authors agree that a primary contribution of this study and paper is to showcase what is possible to do with a limited amount of movie-viewing data, then they should make it clearer, sooner, how much usable movie data they have from infants. They could also consider conducting additional analyses to determine the minimum amount of fMRI data necessary to reveal the same detailed characteristics of functional responses in the visual cortex.

We agree it would be good to highlight the amount of movie data used. When the infant data is first introduced in the results section, we now state the durations:

“All available movies from each session were included (Table S2), with an average duration of 540.7s (range: 186--1116s).” Pg. 5

Additionally, we have added a homotopy analysis that describes the contribution of data quantity to the results observed. We compare the amount of data collected with the magnitude of same vs. different stream effect (Figure 1B) and within stream distance effect (Figure 1C). We find no effect of movie duration in the sample we tested, as reported below:

“We found no evidence that the variability in movie duration per participant correlated with this difference [of same stream vs. different stream] (r=0.08, p=.700).” Pg. 6-7

“There was no correlation between movie duration and the effect (Same > Adjacent: r=-

0.01, p=.965, Adjacent > Distal: r=-0.09, p=.740).” Pg. 7

(5) If any of the methodological approaches are novel, the authors should make this clear. In particular, has the approach of visually inspecting and categorizing components generated from ICA and movie data been done before, in adults/other contexts?

The methods we employed are similar to others, as described in the public review.

However, changes were necessary to apply them to infant samples. For instance, Guntupalli et al. (2016) used hyperalignment to predict the visual maps of adult participants, whereas we use SRM. SRM and hyperalignment have the same goal — find a maximally aligned representation between participants based on brain function — but their implementation is different. The application of functional alignment to infants is novel, as is their use in movie data that is relatively short by comparison to standard adult data. Indeed, this is the most thorough demonstration that SRM — or any functional alignment procedure — can be usefully applied to infant data, awake or sleeping. We have clarified this point in the discussion.

“This is initial evidence that functional alignment may be useful for enhancing signal quality, like it has in adults27,32,33, or revealing changing function over development45, which may prove especially useful for infant fMRI52.” Pg. 21

(6) The authors found that meridian maps were less identifiable from ICA and movie data and suggest that this may be because these maps are more susceptible to noise or gaze variability. If this is the case, you might predict that these maps are more identifiable in adult data. The authors could consider running additional analyses with their adult participants to better understand this result.

As described in the manuscript, we hypothesize that meridian maps are more difficult to identify than spatial frequency maps because meridian maps are a less smooth, more fine-grained map than spatial frequency. Indeed, it has previously been reported (Moeller et al., 2009) that similar procedures can result in meridian maps that are constituted by multiple independent components (e.g., a component sensitive to horizontal orientations, and a separate component sensitive to vertical components). Nonetheless, we have now conducted the ICA procedure on adult participants and again find it is easier to identify spatial frequency components compared to meridian maps, as reported in the public review.

Minor corrections:

(1) Typo: Figure 3 title: "Example retintopic task vs. ICA-based spatial frequency maps.".

Fixed

(2) Given the age range of the participants, consider using "infants and toddlers"? (Not to diminish the results at all; on the contrary, I think it is perhaps even more impressive to obtain awake fMRI data from ~1-2-year-olds). Example: Figure 3 legend: "A) Spatial frequency map of a 17.1-monthold infant.".

We agree with the reviewer that there is disagreement about the age range at which a child starts being considered a toddler. We have changed the terms in places where we refer to a toddler in particular (e.g., the figure caption the reviewer highlights) and added the phrase “infants and toddlers” in places where appropriate. Nonetheless, we have kept “infants” in some places, particularly those where we are comparing the sample to adults. Adding “and toddlers” could imply three samples being compared which would confuse the reader.

(3) Figure 6 legend: The following text should be omitted as there is no bar plot in this figure: "The bar plot is the average across participants. The error bar is the standard error across participants.".

Fixed

(4) Table S1 legend: Missing first single quote: Runs'.

Fixed

Reviewer #2 (Recommendations For The Authors):

I request that this paper cite more of the existing literature on the fMRI of human infants and toddlers using task-driven and resting-state data. For example, early studies by (first authors) Biagi, Dehaene-Lambertz, Cusack, and Fransson, and more recent studies by Chen, Cabral, Truzzi, Deen, and Kosakowski.

We have added several new citations of recent task-based and resting state studies to the second sentence of the main text:

“Despite the recent growth in infant fMRI1-6, one of the most important obstacles facing this research is that infants are unable to maintain focus for long periods of time and struggle to complete traditional cognitive tasks7.”

Reviewer #3 (Recommendations For The Authors):

In the following, I report some of my main perplexities, but many more may arise when the material is presented more clearly.

The age of the children varies from 5 months to about 2 years. While the developmental literature suggests that between 1 and 2 years children have a visual system nearly adult-like, below that age some areas may be very immature. I would split the sample and perhaps attempt to validate the adult SRM model with the youngest children (and those can be called infants).

We recognize the substantial age variability in our sample, which is why we report participant-specific data in our figures. While splitting up the data into age bins might reveal age effects, we do not think we can perform adequately powered null hypothesis testing of the age trend. In order to investigate the contribution of age, larger samples will be needed. That said, we can see from the data that we have reported that any effect of age is likely small. To elaborate: Figures 4 and 6 report the participant-specific data points and order the participants by age. There are no clear linear trends in these plots, thus there are no strong age effects.

More broadly, we do not think there is a principled way to divide the participants by age. The reviewer suggests that the visual system is immature before the first year of life and mature afterward; however, such claims are the exact motivation for the type of work we are doing here, and the verdict is still out. Indeed, the conclusion of our earlier work reporting retinotopy in infants (Ellis et al., 2021) suggests that the organization of the early visual cortex in infants as young as 5 months — the youngest infant in our sample — is surprisingly adult-like.

The title cannot refer to infants given the age span.

There is disagreement in the field about the age at which it is appropriate to refer to children as infants. In this paper, and in our prior work, we followed the practice of the most attended infant cognition conference and society, the International Congress of Infant Studies (ICIS), which considers infants as those aged between 0-3 years old, for the purposes of their conference. Indeed, we have never received this concern across dozens of prior reviews for previous papers covering a similar age range. That said, we understand the spirit of the reviewer’s comment and now refer to the sample as “infants and toddlers” and to older individuals in our sample as “toddlers” wherever it is appropriate (the younger individuals would fairly be considered “infants” under any definition).

Figure 1 is clear and an interesting approach. Please also show the average correlation maps on the cortical surface.

While we would like to create a figure as requested, we are unsure how to depict an area-by-area correlation map on the cortical surface. One option would be to generate a seed-based map in which we take an area and depict the correlation of that seed (e.g., vV1) with all other voxels. This approach would result in 8 maps for just the task-defined areas, and 17 maps for anatomically-defined areas. Hence, we believe this is out of scope of this paper, but an interested reader could easily generate these maps from the data we have released.

Figure 2 results are not easily interpretable. Ventral and dorsal V1-V3 areas represent upper or lower VF respectively. Higher dorsal and ventral areas represent both upper and lower VF, so we should predict an equal distance between the two streams. Again, how can we verify that it is not a result of some artifacts?

In adults, visual areas differ in their functional response properties along multiple dimensions, including spatial coding. The dorsal/ventral stream hypothesis is derived from the idea that areas in each stream support different functions, independent of spatial coding. The MDS analysis did not attempt to isolate the specific contribution of spatial representations of each area but instead tested the similarity of function that is evoked in naturalistic viewing. Other covariance-based analyses specifically isolate the contribution of spatial representations (Haak et al., 2013); however, they use a much more constrained analysis than what was implemented here. The fact that we find broad differentiation of dorsal and ventral visual areas in infants is consistent with adults (Haak & Beckman, 2018) and neonate non-human primates (Arcaro & Livingstone, 2017). 

Nonetheless, we recognize that we did not mention the differences in visual field properties across areas and what that means. If visual field properties alone drove the functional response then we would expect to see a clustering of areas based on the visual field they represent (e.g., hV4 and V3AB should have similar representations). Since we did not see that, and instead saw organization by visual stream, the result is interesting and thus warrants reporting. We now mention this difference in visual fields in the manuscript to highlight the surprising nature of the result.

“This separation between streams is striking when considering that it happens despite differences in visual field representations across areas: while dorsal V1 and ventral V1 represent the lower and upper visual field, respectively, V3A/B and hV4 both have full visual field maps. These visual field representations can be detected in adults41; however, they are often not the primary driver of function39. We see that in infants too: hV4 and V3A/B represent the same visual space yet have distinct functional profiles.” Pg. 8

The reviewer raises a concern that the MDS result may be spurious and caused by noise. Below, we present three reasons why we believe these results are not accounted for by artifacts but instead reflect real functional differentiation in the visual cortex. 

(1) Figure 2 is a visualization of the similarity matrix presented in Figure S1. In Figure S1, we report the significance testing we performed to confirm that the patterns differentiating dorsal and ventral streams — as well as adjacent areas from distal areas — are statistically reliable across participants. If an artifact accounted for the result then it would have to be a kind of systematic noise that is consistent across participants.

(2) One of the main sources of noise (both systematic and non-systematic) with infant fMRI is motion. Homotopy is a within-participant analysis that could be biased by motion. To assess whether motion accounts for the results, we took a conservative approach of regressing out the framewise motion (i.e., how much movement there is between fMRI volumes) from the comparisons of the functional activity in regions. Although the correlations numerically decreased with this procedure, they were qualitatively similar to the analysis that does not regress out motion:

“Additionally, if we control for motion in the correlation between areas --- in case motion transients drive consistent activity across areas --- then the effects described here are negligibly different (Figure S5).” Pg. 7

(3) We recognize that despite these analyses, it would be helpful to see what this pattern looks like in adults where we know more about the visual field properties and the function of dorsal and ventral streams. This has been done previously (e.g., Haak & Beckman, 2018), but we have now run those analyses on adults in our sample, as described in the public review. As with infants, there are reliable differences in the homotopy between streams (Figure S1). The MDS results show that the adult data was more complex than the infant data, since it was best described by 3 dimensions rather than 2. Nonetheless, there is a rotation of the MDS such that the structure of the ventral and dorsal streams is also dissociable. 

Figure 3 also raises several alternative interpretations. The spatial frequency component in B has strong activity ONLY at the extreme border of the VF and this is probably the origin of the strong correlation. I understand that it is only one subject, but this brings the need to show all subjects and to report the correlation. Also, it is important to show the putative average ICA for retinotopy and spatial frequencies across subjects and for adults. All methods should be validated on adults where we have clear data for retinotopy and spatial frequency.

The reviewer notes that the component in Figure 3 shows strong negative response in the periphery. It is often the case, as reported elsewhere (Moeller et al., 2009), that ICA extracts portions of visual maps. To make a full visual map would require combining components into a composite (e.g., a component that has a high response in the periphery and another component that has a high response in the fovea). If we were to claim that this component, or others like it, could replace the need for retinotopic mapping, then we would want to produce these composite maps; however, our conclusion in this project is that the topographic information of retinotopic maps manifest in individual components of ICA. For this purpose, the analysis we perform adequately assesses this topography.

Regarding the request to show the results for all subjects, we address this in the public response and repeat it here briefly: we have added 6 new figures to show results akin to Figure 3C and D. It is impractical to show the equivalent of Figure 3A and B for all participants, yet we do release the data necessary to see to visualize these maps easily.

Finally, the reviewer suggests that we validate the analyses on adult participants. As shown in Figure S3 and reported in the public response, we now run these analyses on adult participants and observe qualitatively similar results to infants.

How much was the variation in the presumed spatial frequency map? Is it consistent with the acuity range? 5-month-old infants should have an acuity of around 10c/deg, depending on the mean luminance of the scene.

The reviewer highlights an important weakness of conducting ICA: we cannot put units on the degree of variation we see in components. We now highlight this weakness in the discussion:

“Another limitation is that ICA does not provide a scale to the variation: although we find a correlation between gradients of spatial frequency in the ground truth and the selected component, we cannot use the component alone to infer the spatial frequency selectivity of any part of cortex. In other words, we cannot infer units of spatial frequency sensitivity from the components alone.” Pg. 20

Figure 5 pipeline is totally obscure. I presumed that I understood, but as it is it is useless. All methods should be clearly described, and the intermediate results should be illustrated in figures and appropriately discussed. Using such blind analyses in infants in principle may not be appropriate and this needs to be verified. Overall all these techniques rely on correlation activities that are all biased by head movement, eye movement, and probably the dummy sucking. All those movements need to be estimated and correlated with the variability of the results. It is a strong assumption that the techniques should work in infants, given the presence of movements.

We recognize that the SRM methods are complex. Given this feedback, we remade Figure 5 with explicit steps for the process and updated the caption (as reported in the public review).

Regarding the validation of these methods, we have added SRM analyses from adults and find comparable results. This means that using these methods on adults with comparable amounts of data as what we collected from infants can predict maps that are highly similar to the real maps. Even so, it is not a given that these methods are valid in infants. We present two considerations in this regard. 

First, as part of the SRM analyses reported in the manuscript, we show that control analyses are significantly worse than the real analyses (indicated by the lines on Figure 6). To clarify the control analysis: we break the mapping (i.e., flip the order of the data so that it is backwards) between the test participant and the training participants used to create the SRM. The fact that this control analysis is significantly worse indicates that SRM is learning meaningful representations that matter for retinotopy. 

Second, we believe that this paper is a validation of SRM for infants. Infant fMRI is a nascent field and SRM has the potential to increase the signal quality in this population. We hope that readers will see these analyses as a proof of concept that SRM can be used in their work with infants. We have stated this contribution in the paper now.

“Additionally, we wish to test whether methods for functional alignment can be used with infants. Functional alignment finds a mapping between participants using functional activity -- rather than anatomy -- and in adults can improve signal-to-noise, enhance across participant prediction, and enable unique analyses27,32-34.” Pg. 4

“This is initial evidence that functional alignment may be useful for enhancing signal quality, like it has in adults27,32,33, or revealing changing function over development45.” Pg. 21

Regarding the reviewer’s concern that motion may bias the results, we wish to emphasize the nature of the analyses being conducted here: we are using data from a group of participants to predict the neural responses in a held-out participant. For motion to explain consistency between participants, the motion would need to be timelocked across participants. Even if motion was time-locked during movie watching, motion will impair the formation of an adequate model that can contain retinotopic information. Thus, motion should only hurt the ability for a shared response to be found that can be used for predicting retinotopic maps. Hence, the results we observed are despite motion and other sources of noise.

What is M??? is it simply the mean value??? If not, how it is estimated?

M is an abbreviation for mean. We have now expanded the abbreviation the first time we use it.

Figure 6 should be integrated with map activity where the individual area correlation should be illustrated. Probably fitting SMR adult works well for early cortical areas, but not for more ventral and associative, and the correlation should be evaluated for the different masks.

With the addition of plots showing the gradients for each participant and each movie (Figures S10–S13) we hope we have addressed this concern. We additionally want to clarify that the regions we tested in the analysis in Figure 6 are only the early visual areas V1, V2, V3, V3A/B, and hV4. The adult validation analyses show that SRM works well for predicting the visual maps in these areas. Nonetheless, it is an interesting question for future research with more extensive retinotopic mapping in infants to see if SRM can predict maps beyond extrastriate cortex.

Occipital masks have never been described or shown.

The occipital mask is from the MNI probabilistic structural atlas (Mazziotta et al., 2001), as reported in the original version and is shared with the public data release. We have added the additional detail that the probabilistic atlas is thresholded at 0% in order to be liberally inclusive. 

“We used the occipital mask from the MNI structural atlas63 in standard space -- defined liberally to include any voxel with an above zero probability of being labelled as the occipital lobe -- and used the inverted transform to put it into native functional space.” Pg. 27–28

Methods lack the main explanation of the procedures and software description.

We hope that the additions we have made to address this reviewer’s concerns have provided better explanations for our procedures. Additionally, as part of the data and code release, we thoroughly explain all of the software needed to recreate the results we have observed here.

eLife assessment

In this important study, Bu et al investigate how cell overcrowding triggers a mechano-transduction pathway involving TRPV4 channels, focusing on high-grade ductal carcinoma in situ (DCIS) cells. The authors show that cell crowding in these malignant cells leads to a reduction in cell volume and promotes a pro-invasive phenotype through calcium homeostasis and TRPV4 channel trafficking to the plasma membrane; this phenomenon is specific to invasive cell lines like MCF10CA and DCIS and is corroborated by patient tissue samples. The work suggests the role of TRPV4 in cell motility and mechanical sensing, offering potential therapeutic insights for targeting cancer metastasis. While the study presents robust and convincing data, the absence of TRPV4 genetic ablation is a critical limitation, which would further confirm its role in these processes.

Reviewer #1 (Public review):

Summary:

In this study, Bu et al examined the dynamics of TRPV4 channel in cell overcrowding in carcinoma conditions. They investigated how cell crowding (or high cell confluence) triggers a mechano-transduction pathway involving TRPV4 channels in high-grade ductal carcinoma in situ (DCIS) cells that leads to large cell volume reduction (or cell volume plasticity) and pro-invasive phenotype.

In vitro, this pathway is highly selective for highly malignant invasive cell lines derived from a normal breast epithelial cell line (MCF10A) compared to the parent cell line, but not present in another triple-negative invasive breast epithelial cell line (MDA-MB-231). The authors convincingly showed that enhanced TRPV4 plasma membrane localization correlates with high-grade DCIS cells in patient tissue samples.<br /> Specifically in non-invasive MCF10DCIS.com cells, they showed that overcrowding or over-confluence leads to a decrease in cell volume and intracellular calcium levels. This condition also triggers the trafficking of TRPV4 channels from intracellular stores (nucleus and potentially endosomes), to the plasma membrane (PM). When these over-confluent cells are incubated with a TRPV4 activator, there is an acute and substantial influx of calcium, attesting to the fact that there are a high number of TRPV4 channels present on the PM. Long-term incubation of these over-confluent cells with the TRPV4 activator results in the internalization of the PM-localized TRPV4 channels.

In contrast, cells plated at lower confluence primarily have TRPV4 channels localized in the nucleus and cytosol. Long-term incubation of these cells at lower confluence with a TRPV4 inhibitor leads to the relocation of TRPV4 channels to the plasma membrane from intracellular stores and a subsequent reduction in cell volume. Similarly, incubation of these cells at low confluence with PEG 3000 (a hyperosmotic agent) promotes the trafficking of TRPV4 channels from intracellular stores to the plasma membrane.

Strengths:

The study is elegantly designed and the findings are novel. Their findings on this mechano-transduction pathway involving TRPV4 channels, calcium homeostasis, cell volume plasticity, motility, and invasiveness will have a great impact in the cancer field and are potentially applicable to other fields as well. Experiments are well-planned and executed, and the data is convincing. The authors investigated TRVP4 dynamics using multiple different strategies- overcrowding, hyperosmotic stress, and pharmacological means, and showed a good correlation between different phenomena.

Weaknesses:

A major emphasis in the study is on pharmacological means to relate TRPV4 channel function to the phenotype. I believe the use of genetic means would greatly enhance the impact and provide compelling proof for the involvement of TRPV4 channels in the associated phenotype. In this regard, I wonder if siRNA-mediated knockdown of TRPV4 in over-confluent cells (or knockout) would lead to an increase in cell volume and normalize the intracellular calcium levels back to normal, thus ultimately leading to a decrease in cell invasiveness.

Reviewer #2 (Public review):

Summary:

The metastasis poses a significant challenge in cancer treatment. During the transition from non-invasive cells to invasive metastasis cells, cancer cells usually experience mechanical stress due to a crowded cellular environment. The molecular mechanisms underlying mechanical signaling during this transition remain largely elusive. In this work, the authors utilize an in vitro cell culture system and advanced imaging techniques to investigate how non-invasive and invasive cells respond to cell crowding, respectively.

Strengths:

The results clearly show that pre-malignant cells exhibit a more pronounced reduction in cell volume and are more prone to spreading compared to non-invasive cells. Furthermore, the study identifies that TRPV4, a calcium channel, relocates to the plasma membrane both in vitro and in vivo (patient samples). Activation and inhibition of the TRPV4 channel can modulate the cell volume and cell mobility. These results unveil a novel mechanism of mechanical sensing in cancer cells, potentially offering new avenues for therapeutic intervention targeting cancer metastasis by modulating TRPV4 activity. This is a very comprehensive study, and the data presented in the paper are clear and convincing. The study represents a very important advance in our understanding of the mechanical biology of cancer.

Weaknesses:

However, I do think that there are several additional experiments that could strengthen the conclusions of this work. A critical limitation is the absence of genetic ablation of the TRPV4 gene to confirm its essential role in the response to cell crowding.

Author response:

Reviewer #1 (Public review):

Summary:

In this study, Bu et al examined the dynamics of TRPV4 channel in cell overcrowding in carcinoma conditions. They investigated how cell crowding (or high cell confluence) triggers a mechano-transduction pathway involving TRPV4 channels in high-grade ductal carcinoma in situ (DCIS) cells that leads to large cell volume reduction (or cell volume plasticity) and pro-invasive phenotype.

In vitro, this pathway is highly selective for highly malignant invasive cell lines derived from a normal breast epithelial cell line (MCF10CA) compared to the parent cell line, but not present in another triple-negative invasive breast epithelial cell line (MDA-MB-231). The authors convincingly showed that enhanced TRPV4 plasma membrane localization correlates with high-grade DCIS cells in patient tissue samples.

Specifically in invasive MCF10DCIS.com cells, they showed that overcrowding or over-confluence leads to a decrease in cell volume and intracellular calcium levels. This condition also triggers the trafficking of TRPV4 channels from intracellular stores (nucleus and potentially endosomes), to the plasma membrane (PM). When these over-confluent cells are incubated with a TRPV4 activator, there is an acute and substantial influx of calcium, attesting to the fact that there are a high number of TRPV4 channels present on the PM. Long-term incubation of these over-confluent cells with the TRPV4 activator results in the internalization of the PM-localized TRPV4 channels.

In contrast, cells plated at lower confluence primarily have TRPV4 channels localized in the nucleus and cytosol. Long-term incubation of these cells at lower confluence with a TRPV4 inhibitor leads to the relocation of TRPV4 channels to the plasma membrane from intracellular stores and a subsequent reduction in cell volume. Similarly, incubation of these cells at low confluence with PEG 3000 (a hyperosmotic agent) promotes the trafficking of TRPV4 channels from intracellular stores to the plasma membrane.

Strengths:

The study is elegantly designed and the findings are novel. Their findings on this mechano-transduction pathway involving TRPV4 channels, calcium homeostasis, cell volume plasticity, motility, and invasiveness will have a great impact in the cancer field and are potentially applicable to other fields as well. Experiments are well-planned and executed, and the data is convincing. The authors investigated TRVP4 dynamics using multiple different strategies- overcrowding, hyperosmotic stress, and pharmacological means, and showed a good correlation between different phenomena.

Weaknesses:

A major emphasis in the study is on pharmacological means to relate TRPV4 channel function to the phenotype. I believe the use of genetic means would greatly enhance the impact and provide compelling proof for the involvement of TRPV4 channels in the associated phenotype. In this regard, I wonder if siRNA-mediated knockdown of TRPV4 in over-confluent cells (or knockout) would lead to an increase in cell volume and normalize the intracellular calcium levels back to normal, thus ultimately leading to a decrease in cell invasiveness.

We greatly appreciate the positive feedback regarding the design of our study and the novelty of our findings. We also acknowledge the constructive suggestion to complement our pharmacological approaches with genetic manipulation of TRPV4.

In response to the comment regarding siRNA-mediated knockdown or knockout of TRPV4, we fully agree that this would further substantiate our findings. We will use shRNA targeting TRPV4 approaches to further explore the functional effects of TRPV4 knockdown on cell volume plasticity, intracellular calcium level changes, and invasiveness phenotypes through motility assays at the single cell level under cell crowding or hyperosmotic stress and will include these results in our revised manuscript.

Reviewer #2 (Public review):

Summary:

The metastasis poses a significant challenge in cancer treatment. During the transition from non-invasive cells to invasive metastasis cells, cancer cells usually experience mechanical stress due to a crowded cellular environment. The molecular mechanisms underlying mechanical signaling during this transition remain largely elusive. In this work, the authors utilize an in vitro cell culture system and advanced imaging techniques to investigate how non-invasive and invasive cells respond to cell crowding, respectively.

Strengths:

The results clearly show that pre-malignant cells exhibit a more pronounced reduction in cell volume and are more prone to spreading compared to non-invasive cells. Furthermore, the study identifies that TRPV4, a calcium channel, relocates to the plasma membrane both in vitro and in vivo (patient samples). Activation and inhibition of the TRPV4 channel can modulate the cell volume and cell mobility. These results unveil a novel mechanism of mechanical sensing in cancer cells, potentially offering new avenues for therapeutic intervention targeting cancer metastasis by modulating TRPV4 activity. This is a very comprehensive study, and the data presented in the paper are clear and convincing. The study represents a very important advance in our understanding of the mechanical biology of cancer.

Weaknesses:

However, I do think that there are several additional experiments that could strengthen the conclusions of this work. A critical limitation is the absence of genetic ablation of the TRPV4 gene to confirm its essential role in the response to cell crowding.

We are grateful for the positive assessment of our study and the acknowledgment of the impact of our findings on the understanding of mechanical signaling in cancer progression. We also appreciate the suggestion to include genetic ablation experiments to confirm the role of TRPV4 in cell crowding responses. As noted in our response to reviewer #1, we plan to use shRNA TRPV4 to examine the functional effects of TRPV4 knockdown on cell volume plasticity, changes in intracellular calcium levels, and invasive phenotypes through motility assays at the single-cell level under conditions of cell crowding or hyperosmotic stress. We will include these results in our revised manuscript.

Once again, we thank the reviewers for their valuable feedback, which will help us further improve our manuscript.

Reviewer #1 (Public review):

Summary:

The use of antalarmin, a selective CRF1 receptor antagonist, prevents the deficits in sociability in (acutely) morphine-treated males, but not in females. In addition, cell-attached experiments show a rescue to control levels of the morphine-induced increased firing in PVN neurons from morphine-treated males. Similar results are obtained in CRF receptor 1-/- male mice, confirming the involvement of CRF receptor 1-mediated signaling in both sociability deficits and neuronal firing changes in morphine-treated male mice.

Strengths:

The experiments and analyses appear to be performed to a high standard, and the manuscript is well written and the data clearly presented. The main finding, that CRF-receptor plays a role in sociability deficits occurring after acute morphine administration, is an important contribution to the field.

Weaknesses:

The link between the effect of pharmacological and genetic modulation of CRF 1 receptor on sociability and on PVN neuronal firing, is less well supported by the data presented. No evidence of causality is provided.

Major points:

(1) The results of behavioral tests and the neural substrate are purely correlative. To find causality would be important to selectively delete or re-express CRF1 receptor sequence in the VPN. Re-expressing the CRF1 receptor in the VPN of male mice and testing them for social behavior and for neuronal firing would be the easier step in this direction.

(2) It would be interesting to discuss the relationship between morphine dose and CRF1 receptor expression.

(3) It would be important to show the expression levels of CRF1 receptors in PVN neurons in controls and morphine-treated mice, both males and females.

(4) It would be important to discuss the mechanisms by which CRF1 receptor controls the firing frequency of APV+/OXY+ neurons in the VPN of male mice.

Minor points:

(1) The phase of the estrous cycles in which females are analyzed for both behavior and electrophysiology should be stated.

(2) It would be important to show the statistical analysis between sexes.

Reviewer #2 (Public review):

This manuscript reports a series of studies that sought to identify a biological basis for morphine-induced social deficits. This goal has important translational implications and is, at present, incompletely understood in the field. The extant literature points to changes in periventricular CRF and oxytocin neurons as critical substrates for morphine to alter social behavior. The experiments utilize mice, administered morphine prior to a sociability assay. Both male and female mice show reduced sociability in this procedure. Pretreatment with the CRF1 receptor antagonist, antalarmin, clearly abolished the morphine effect in males, and the data are compelling. Consistently, CRF1-/- male mice appeared to be spared of the effect of morphine (while wild-type and het mice had reduced sociability). The same experiment was reported as non-feasible in females due to the effect of dose on exploratory behavior per se. Seeking a neural correlate of the behavioral pharmacology, acute cell-attached recordings of PVN neurons were made in acute slices from mice pretreated with morphine or anatalarmin. Morphine increased firing frequencies, and both antalarmin and CRF1-/- mice were spared of this effect. Increasing confidence that this is a CRF1 mediated effect, there is a gene deletion dose effect where het's had an intermediate response to morphine. In general, these experiments are well-designed and sufficiently powered to support the authors' inferences. A final experiment repeated the cell-attached recordings with later immunohistochemical verification of the recorded cells as oxytocin or vasopressin positive. Here the data are more nuanced. The majority of sampled cells were positive for both oxytocin and vasopressin, in cells obtained from males, morphine pretreatment increased firing in this population and was CRF1 dependent, however in females the effect of morphine was more modest without sensitivity to CRF1. Given that only ~8 cells were only immunoreactive for oxytocin, it may be premature to attribute the changes in behavior and physiology strictly to oxytocinergic neurons. In sum, the data provide convincing behavioral pharmacological evidence and a regional (and possibly cellular) correlation of these effects suggesting that morphine leads to sociality deficits via CRF interacting with oxytocin in the hypothalamus. While this hypothesis remains plausible, the current data do not go so far as directly testing this mechanism in a site or cell-specific way. With regard to the presentation of these data and their interpretation, the manuscript does not sufficiently draw a clear link between mu-opioid receptors, their action on CRF neurons of the PVN, and the synaptic connectivity to oxytocin neurons. Importantly, sex, cell, and site-specific variations in the CRF are well established (see Valentino & Bangasser) yet these are not reviewed nor are hypotheses regarding sex differences articulated at the outset. The manuscript would have more impact on the field if the implications of the sex-specific effects evident here were incorporated into a larger literature.

With regards to the model proposed in the discussion, it seems that there is an assumption that ip morphine or antalarmin have specific effects on the PVN and that these mediate behavior - but this is impossible to assume and there are many meaningful alternatives (for example, both MOR and CRF modulation of the raphe or accumbens are worth exploration). While it is up to the authors to conduct additional studies, a demonstration that the physiology findings are in fact specific to the PVN would greatly increase confidence that the pharmacology is localized here. Similarly, direct infusion of antalarmin to the PVN, or cell-specific manipulation of OT neurons (OT-cre mice with inhibitory dreadds) combined with morphine pre-exposure would really tie the correlative data together for a strong mechanistic interpretation.

Because the work is framed as informing a clinical problem, the discussion might have increased impact if the authors describe how the acute effects of CRF1 antagonists and morphine might change as a result of repeated use or withdrawal.

Reviewer #3 (Public review):

Summary:

In the current manuscript, Piccin et al. identify a role for CRF type 1 receptors in morphine-induced social deficits using a 3-chamber social interaction task in mice. They demonstrate that pre-treatment with a CRFR1 antagonist blocks morphine-induced social deficits in male, but not female, mice, and this is associated with the CRF R1 antagonist blocking morphine-induced increases in PVN neuronal excitability in male but not female mice. They followed up by using a transgenic mouse CRFR1 knockout mouse line. CRFR1 genetic deletion also blocked morphine-induced social deficits, similar to the pharmacological approach, in male mice. This was also associated with morphine-induced increases in PVN neuronal excitability being blocked in CRFR1 knockout mice. Interestingly they found that the pharmacological antagonism of the CRFR1 specifically blocked morphine-induced increases in oxytocin/AVP neurons in the PVN in male mice.

Strengths:

The authors used both male and female mice where possible and the studies were fairly well controlled. The authors provided sufficient methodological detail and detailed statistical information. They also examined measures of locomotion in all of the behavioral tasks to separate changes in sociability from overall changes in locomotion. The experiments were well thought out and well controlled. The use of both the pharmacological and genetic approaches provides converging lines of evidence for the role of CRFR1 in morphine-induced social deficits. Additionally, they have identified the PVN as a potential site of action for these CRFR1 effects.

Weaknesses:

While the authors included both sexes they analyzed them independently. This was done for simplicity's sake as they have multiple measures but there are several measures where the number of factors is reduced and the inclusion of sex as a factor would be possible. Additionally, single doses of both the CRFR1 antagonist and morphine are used within an experiment without justification for the doses. In fact, a lower dose of morphine was needed for the genetic CRFR1 mouse line. This would suggest that the dose of morphine being used is likely causing some aversion that may be more present in the females, as they have lower overall time in the ROI areas of both the object and the mouse following morphine exposure. As for the discussion, the authors do not sufficiently address why CRFR1 has an effect in males but not females and what might be driving that difference, or why male and female mice have different distribution of PVN cell types during the recordings. Additionally, the authors attribute their effect to CRF and CRFR1 within the PVN but do not consider the role of extrahypothalamic CRF and CRFR1. While the PVN does contain the largest density of CRF neurons there are other CRF neurons, notably in the central amygdala and BNST, that have been shown to play important roles in the impact of stress on drug-related behavior. This also holds true for the expression of CRFR1 in other regions of the brain, including the VTA, which is important for drug-related behavior and social behavior. The treatments used in the current manuscript were systemic or brain-wide deletion of CRFR1. Therefore, the authors should consider that the effects could be outside the PVN.

eLife assessment

This study provides novel insights into COVID-19 immune responses by using the delta of the normalised accessible surface area (DASA) to map IgM responses to the SARS-CoV-2 Membrane protein M1-subtype across multiple European cohorts. The evidence supporting the findings is solid, with thorough validation and comprehensive analysis, although additional clarity on T-independent B cell reactions and the impact of comorbidities would further strengthen the conclusions. The methods and data presented are valuable for advancing diagnostic and prognostic tools for COVID-19, particularly in the context of long COVID.

Reviewer #1 (Public Review):

Summary of the Study:

The manuscript delves into the COVID-19 virus membrane protein M1-subtype and its IgM responses in COVID-19 cohorts. The authors conducted an extensive epitope screening and prediction through delta of the normalized accessible surface area (DASA) and validated their findings across multiple cohorts in Europe. The study aims to provide novel insights into the immune responses to COVID-19 and explore potential clinical implications for long COVID prognostics.

Strengths:

(1) Innovative Approach:<br /> The use of DASA for epitope screening is innovative and allows for detailed mapping of immune responses.

(2) Validation Across Cohorts:<br /> The study's validation of findings across multiple European cohorts adds robustness and generalizability to the results.

(3) Comprehensive Analysis:<br /> The manuscript presents a thorough analysis of IgM responses, contributing valuable data to the understanding of immune responses in COVID-19.

Weaknesses:

(1) Lack of Clarity on T-Independent B Cell Reactions:<br /> The rationale and results regarding T-independent B cell reactions are not well-explained, requiring additional bridging sentences or data for better comprehension.

(2) Limited Sample Size for B Cell Stimulation:<br /> The in vitro B cell stimulation experiments involve a very small number of individuals (2 reacted vs 1 unreacted), which weakens the strength of the conclusions drawn from these experiments.

(3) Insufficient Exploration of Comorbidities:<br /> The manuscript could benefit from exploring correlations with other clinical data on comorbidities or sub-grouping the long COVID cohort by specific outcomes.

Appraisal of the Study's Aims and Conclusions :

The authors have partially achieved their aims by providing novel insights into COVID-19 immune responses and highlighting the potential for using IgM responses in long COVID prognostics. However, the conclusions would be more convincing with additional data and clarity on certain aspects, such as the T-independent B cell reactions and the impact of comorbidities.

Impact on the Field and Utility to the Community:

This study has the potential to significantly impact the field of COVID-19 research by advancing the understanding of immune responses to the virus. The novel insights into IgM responses and epitope screening could inform future diagnostic and prognostic tools for COVID-19, particularly in the context of long COVID. Additionally, the methods and data presented could be valuable to researchers exploring similar viral immune responses.

Additional Context:

For readers and researchers, it is essential to note that while the study offers intriguing results, the manuscript would benefit from more comprehensive data and clearer explanations in certain areas. The inclusion of the DASA equation in the manuscript or a figure would improve readability and contextual comprehension. Further exploration of clinical comorbidities and additional external validation data would enhance the study's robustness and applicability.

Reviewer #2 (Public Review):

Summary:

This paper identifies a novel SARS-CoV-2 epitope that measures host-virus interactions that have clinical correlations and can act as a signature of infection. In doing so, the authors present a novel structure-driven epitope profiling pipeline that allows them to rapidly iterate through multiple possible peptide epitope candidates for directly measuring host-virus binding. With this approach, the authors identify an IgM antibody response driven by the N-terminus of the Membrane protein of SARS-CoV-2, and demonstrate that epitope is directly correlative with cell-level measurements of infection, and can even act as a clinical signature of infection. The findings are significant to those interested in epitope identification and present a unique step forward for incorporating structural data in an iterative screening approach. The study itself presents some unique connections between the models presented, the IgM being generated, and clinical outcomes, but the claim that these IgM levels are indicative of anything more than past infection will require further detailed analysis.

Strengths:

(1) The methodological approach presented in this study is incredibly powerful and shows major promise to identify other peptide epitopes of proteins for antibody profiling. The simplicity of the methodological approach to string together established protocols and measurements offers a unique elegant promise that this is a generalizable method to many other systems and disease contexts.

(2) The clever use of a SASA metric to study and identify each of the major components demonstrates how structural information is a powerful way to approach identifying and nominating candidate peptides.

(3) This paper spans an exciting range of structural data to clinical-derived measurements, demonstrating the powerful possibilities that can arise from connecting structural biophysical data to clinical measurements to build generalized pipelines or models

Weaknesses:

(1) While the authors use SASA as a great way to screen peptides based on the presumption that SASA can act as a measure of the stability of protein folding, there are many caveats that may come with this measurement that can reduce generalizability. Assessing SASA per residue is a high variance metric that requires many additional layers of further analysis to make inferences about peptide stability. Further, since proteins are inherently dynamic, alternative configurations may yield fluctuating SASA values that inherently bias and introduce noise into the results. It would be useful to compare these SASA metrics for peptides to other structural measures often associated with protein stability used in the literature, such as Radius of Gyration, Hydrodynamic Radius, Secondary Structure degree, etc.

(2) In Figure 3G, the author put forth that IgM ELISA results and whole spike IgG correlate with one another. While it is clear that IgM for M1 and IgM for spike S1' subunit both correlate similarly to whole spike IgG levels, the correlation in both cases is incredibly weak, with whole spike IgG fluctuating widely across a narrow range of IgM for M1 values. This interpretation is also contradicted by 3G's best-fit lines that would have a large residual value to the data. Lastly, the Pearson correlation values for both correlations are misleading here as Pearson correlation indicates the strength and direction of two linear variables. This means that any dataset will inherently have a Pearson r value of ~0.40 but one may not be predictive of the other. It would be better for the authors to instead use measures such as Spearman R or additional statistical analysis like histogramming to demonstrate this coupling.

(3) It is not clear from the text if the authors are the first to use LASSO models to correlate IgM levels with infection scores in patients. LASSO-based logistic regressions are powerful tools used widely in statistical approaches to measure the association between two variables. However, there is a lack of citations indicating that the authors' approach is based on previous efforts and matches the best practice in generating these models on clinical data. It would be useful to add citations to indicate that this approach is following established statistical best practices in line with the field. If the use of the LASSO approach is novel, it would be key to mention this and highlight why the authors feel a LASSO model is the appropriate approach here.

(4) The authors demonstrate in Figure 5 that their IgM levels are very clearly correlative with a history of SARS-CoV-2 infection, and provides another avenue for the detection of prior infections. However, these claims are extended to compare to direct symptoms such as fatigue, depression, and quality of life. Specifically, the authors claim that IgM persistence is correlated with lower quality of life and stress-indicative symptoms. However, Figure 5D contradicts this, highlighting that both persistent and non-persistent IgM groups have similar trends and patterns in fatigue, depression, and quality of life. The authors should reexamine this interpretation of their data, and revisit if there are alternative analyses that may indicate where persistent and non-persistent IgM groups separate.

(5) One under-discussed component of this paper is the potential for sequence variation impacting IgM generation and detection. With resistance being a consistent issue amongst infectious diseases and immune evasion, it may be useful to discuss the possible sequence variance seen in the M protein sequence of M1, as well as to see if the IgM levels induced upon M1 presentation can be separated out from their existing analyses (it may not be!). Regardless, it would be useful for the authors to consider the potential for sequence variation in the M1 peptide and its downstream effects.

Reviewer #3 (Public Review):

Summary:

Kearns et al. explored a computational approach DASAr to identify stable peptide epitopes on SARS-CoV-2 proteins. They find that the computational approach has a high success rate at identifying stable and soluble peptides that may reserve the native conformation. The approach identified multiple peptides in Spike, Nucleoprotein, Membrane, and Envelope proteins of SARS-CoV-2. Most surprisingly, a high prevalence of IgM response is to recognize a newly exposed Membrane epitope, M1. Anti-M1 IgM titer is associated with a protective anti-Spike titer, severe disease and long COVID. The data also indicate that anti-M1 IgM may arise from T cell-independent B cell activation.

Strengths:

The computational approach can be widely applied to study antibody epitopes in many pathogens. The observations from this study provide clues to further understanding the role of anti-M1 response and the mechanisms of anti-M1 IgM response to SARS-CoV-2 associated diseases.

Weaknesses:

A subset of the conclusions of this paper are well supported by data, but some statements and analyses need to be clarified, revised, and extended.

eLife assessment

This useful study characterises motor and somatosensory cortex neural activity during naturalistic eating and drinking tongue movement in nonhuman primates. The data, which include both electrophysiology and nerve block manipulations, will be of value to neuroscientists and neural engineers interested in tongue use. However, data analysis needs to be improved to strengthen the inadequate support for some of the main claims in the paper.

Author response:

We thank the reviewers for their valuable comments and recommendations for improvement. In this provisional response we aim to address a few of the major concerns and briefly outline a plan for revision. We plan to submit a more detailed response along with the revised manuscript.

The reviewers have suggested additional analyses to strengthen the manuscript. As noted, the primary focus of this paper is on single units, to act as a starting point in the characterization of orofacial sensorimotor cortical activity in relation to tongue direction. Research on the cortical mechanisms that underlie sensorimotor control of tongue movements has lagged research on limb movements. Thus, the goal of our paper was to first characterize the individual neuron’s 3D directional tuning properties to provide a basis for future in-depth analysis of population dynamics. However, as multiple reviewers have pointed out the strengths of further investigating population activity, we will aim to address this through additional analysis and discussion. Our starting point for this will be to try other decoding algorithms and dimensionality reduction techniques.

Reviewers 1 and 2 suggested we compare a subset of trials from the nerve block dataset that has similar kinematics to the control to eliminate the confounding effect of differing kinematics between the two conditions. We did this for feeding, by sampling an equal number of trials with similar kinematics for both control and nerve block despite the different overall distribution. We will be sure to make this clearer within the text. We will also implement this for drinking by subsampling trials from each category with similar kinematics to see if this can account for the difference in neural activity.

We understand that while using a small number of datasets is typical in non-human primate neuroscience, the inclusion of additional data would greatly reinforce our findings. We are working to process data from other sessions and have completed a few since this submission, which we will run through the analysis and consider adding a comparison into the manuscript.

Reviewer 3 has raised a valid point that the different movement of the jaw may be a confounding factor in our study of tongue movements. We reported in our recent paper (see Supplementary Fig. 4 in Laurence-Chasen et al., 2023) that “Through iterative sampling of sub-regions of the test trials, we found that correlation of tongue kinematic variables with mandibular motion does not account for decoding accuracy. Even at times where tongue motion was completely un-correlated with the jaw, decoding accuracy could be quite high.” We expect that this also will be true for the analysis of single-unit activity.  

To address the concern on the robustness of our analytical methods, we plan to show the variability of neural firing rates across trials using the Fano factor and use a bootstrap test for the directional tuning analysis.

As recommended, we will expand the introduction/discussion to further contextualize the results of this paper within the existing literature and attempt to clarify some of the sections that reviewers have identified.

“Have the authors confirmed or characterized the strength of their inactivation or block, I was unable to find any electrophysiological evidence characterizing the perturbation.”

The strength of the nerve block is characterized by a decrease in baseline firing rate of SIo neurons. We can include a figure showing this as supplementary material in the revised version.

“Can the authors explain (or at least speculate) why there was such a large difference in behavioral effect due to nerve block between the two monkeys (Figure 7)?”

We acknowledge this as a variable inherent to this type of experimentation. Previous studies have found large kinematic variation in the effect of oral nerve block as well as in the following compensatory strategies between subjects. Every animal’s biology and how they respond to perturbation will be different, which is something we are unable to prevent. Indeed, our subjects exhibited different feeding behavior even in the absence of nerve block perturbation (see Figure 2 in Laurence-Chasen et al., 2022). This is why each individual serves as its own control.

Reviewer #1 (Public review):

Summary:

In their paper, Hosack and Arce-McShane investigate how the 3D movement direction of the tongue is represented in the orofacial part of the sensory-motor cortex and how this representation changes with the loss of oral sensation. They examine the firing patterns of neurons in the orofacial parts of the primary motor cortex (MIo) and somatosensory cortex (SIo) in non-human primates (NHPs) during drinking and feeding tasks. While recording neural activity, they also tracked the kinematics of tongue movement using biplanar video-radiography of markers implanted in the tongue. Their findings indicate that most units in both MIo and SIo are directionally tuned during the drinking task. However, during the feeding task, directional turning was more frequent in MIo units and less prominent in SIo units. Additionally, in some recording sessions, they blocked sensory feedback using bilateral nerve block injections, which resulted in fewer directionally tuned units and changes in the overall distribution of the preferred direction of the units.

Strengths:

The most significant strength of this paper lies in its unique combination of experimental tools. The author utilized a video-radiography method to capture 3D kinematics of the tongue movement during two behavioral tasks while simultaneously recording activity from two brain areas. Moreover, they employed a nerve-blocking procedure to halt sensory feedback. This specific dataset and experimental setup hold great potential for future research on the understudied orofacial segment of the sensory-motor area.

Weaknesses:

Aside from the last part of the result section, the majority of the analyses in this paper are focused on single units. I understand the need to characterize the number of single units that directly code for external variables like movement direction, especially for less-studied areas like the orofacial part of the sensory-motor cortex. However, as a field, our decade-long experience in the arm region of sensory-motor cortices suggests that many of the idiosyncratic behaviors of single units can be better understood when the neural activity is studied at the level of the state space of the population. By doing so, for the arm region, we were able to explain why units have "mixed selectivity" for external variables, why the tuning of units changes in the planning and execution phase of the movement, why activity in the planning phase does not lead to undesired muscle activity, etc. See (Gallego et al. 2017; Vyas et al. 2020; Churchland and Shenoy 2024) for a review. Therefore, I believe investigating the dynamics of the population activity in orofacial regions can similarly help the reader go beyond the peculiarities of single units and in a broader view, inform us if the same principles found in the arm region can be generalized to other segments of sensory-motor cortex.

Further, for the nerve-blocking experiments, the authors demonstrate that the lack of sensory feedback severely alters how the movement is executed at the level of behavior and neural activity. However, I had a hard time interpreting these results since any change in neural activity after blocking the orofacial nerves could be due to either the lack of the sensory signal or, as the authors suggest, due to the NHPs executing a different movement to compensate for the lack of sensory information or the combination of both of these factors. Hence, it would be helpful to know if the authors have any hint in the data that can tease apart these factors. For example, analyzing a subset of nerve-blocked trials that have similar kinematics to the control.

Reviewer #2 (Public review):

Summary:

This manuscript by Hosack and Arce-McShane examines the directional tuning of neurons in macaque primary motor (MIo) and somatosensory (SIo) cortex. The neural basis of tongue control is far less studied than, for example, forelimb movements, partly because the tongue's kinematics and kinetics are difficult to measure. A major technical advantage of this study is using biplanar video-radiography, processed with modern motion tracking analysis software, to track the movement of the tongue inside the oral cavity. Compared to prior work, the behaviors are more naturalistic behaviors (feeding and licking water from one of three spouts), although the animals were still head-fixed.

The study's main findings are that:

• A majority of neurons in MIo and a (somewhat smaller) percentage of SIo modulated their firing rates during tongue movements, with different modulations depending on the direction of movement (i.e., exhibited directional tuning). Examining the statistics of tuning across neurons, there was anisotropy (e.g., more neurons preferring anterior movement) and a lateral bias in which tongue direction neurons preferred that was consistent with the innervation patterns of tongue control muscles (although with some inconsistency between monkeys).

• Consistent with this encoding, tongue position could be decoded with moderate accuracy even from small ensembles of ~28 neurons.

• There were differences observed in the proportion and extent of directional tuning between the feeding and licking behaviors, with stronger tuning overall during licking. This potentially suggests behavioral context-dependent encoding.

• The authors then went one step further and used a bilateral nerve block to the sensory inputs (trigeminal nerve) from the tongue. This impaired the precision of tongue movements and resulted in an apparent reduction and change in neural tuning in Mio and SIo.

Strengths:

The data are difficult to obtain and appear to have been rigorously measured, and provide a valuable contribution to this under-explored subfield of sensorimotor neuroscience. The analyses adopt well-established methods, especially from the arm motor control literature, and represent a natural starting point for characterizing tongue 3D direction tuning.

Weaknesses:

There are alternative explanations for some of the interpretations, but those interpretations are described in a way that clearly distinguishes results from interpretations, and readers can make their own assessments. Some of these limitations are described in more detail below.

One weakness of the current study is that there is substantial variability in results between monkeys, and that only one session of data per monkey/condition is analyzed (8 sessions total). This raises the concern that the results could be idiosyncratic. The Methods mention that other datasets were collected, but not analyzed because the imaging pre-processing is very labor-intensive. While I recognize that time is precious, I do think in this case the manuscript would be substantially strengthened by showing that the results are similar on other sessions.

This study focuses on describing directional tuning using the preferred direction (PD) / cosine tuning model popularized by Georgopoulous and colleagues for understanding neural control of arm reaching in the 1980s. This is a reasonable starting point and a decent first-order description of neural tuning. However, the arm motor control field has moved far past that viewpoint, and in some ways, an over-fixation on static representational encoding models and PDs held that field back for many years. The manuscript benefits from drawing the readers' attention (perhaps in their Discussion) that PDs are a very simple starting point for characterizing how cortical activity relates to kinematics, but that there is likely much richer population-level dynamical structure and that a more mechanistic, control-focused analytical framework may be fruitful. A good review of this evolution in the arm field can be found in Vyas S, Golub MD, Sussillo D, Shenoy K. 2020. Computation Through Neural Population Dynamics. Annual Review of Neuroscience. 43(1):249-75

Can the authors explain (or at least speculate) why there was such a large difference in behavioral effect due to nerve block between the two monkeys (Figure 7)?

Do the analyses showing a decrease in tuning after nerve block take into account the changes (and sometimes reduction in variability) of the kinematics between these conditions? In other words, if you subsampled trials to have similar distributions of kinematics between Control and Block conditions, does the effect hold true? The extreme scenario to illustrate my concern is that if Block conditions resulted in all identical movements (which of course they don't), the tuning analysis would find no tuned neurons. The lack of change in decoding accuracy is another yellow flag that there may be a methodological explanation for the decreased tuning result.

The manuscript states that "Our results suggest that the somatosensory cortex may be less involved than the motor areas during feeding, possibly because it is a more ingrained and stereotyped behavior as opposed to tongue protrusion or drinking tasks". Could an alternative explanation be more statistical/technical in nature: that during feeding, there will be more variability in exactly what somatosensation afferent signals are being received from trial to trial (because slight differences in kinematics can have large differences in exactly where the tongue is and the where/when/how of what parts of it are touching other parts of the oral cavity)? This variability could "smear out" the apparent tuning using these types of trial-averaged analyses. Given how important proprioception and somatosensation are for not biting the tongue or choking, the speculation that somatosensory cortical activity is suppressed during feedback is very counter-intuitive to this reviewer.

Reviewer #3 (Public review):

Summary:

In this study, the authors aim to uncover how 3D tongue direction is represented in the Motor (M1o) and Somatosensory (S1o) cortex. In non-human primates implanted with chronic electrode arrays, they use X-ray-based imaging to track the kinematics of the tongue and jaw as the animal is either chewing food or licking from a spout. They then correlate the tongue kinematics with the recorded neural activity. Using linear regressions, they characterize the tuning properties and distributions of the recorded population during feeding and licking. Then, they recharacterize the tuning properties after bilateral lidocaine injections in the two sensory branches of the trigeminal nerve. They report that their nerve block causes a reorganization of the tuning properties. Overall, this paper concludes that M1o and S1o both contain representations of the tongue direction, but their numbers, their tuning properties, and susceptibility to perturbed sensory input are different.

Strengths:

The major strengths of this paper are in the state-of-the-art experimental methods employed to collect the electrophysiological and kinematic data.

Weaknesses:

However, this paper has a number of weaknesses in the analysis of this data.

It is unclear how reliable the neural responses are to the stimuli. The trial-by-trial variability of the neural firing rates is not reported. Thus, it is unclear if the methods used for establishing that a neuron is modulated and tuned to a direction are susceptible to spurious correlations. The authors do not use shuffling or bootstrapping tests to determine the robustness of their fits or determining the 'preferred direction' of the neurons. This weakness colors the rest of the paper.

The authors compare the tuning properties during feeding to those during licking but only focus on the tongue-tip. However, the two behaviors are different also in their engagement of the jaw muscles. Thus many of the differences observed between the two 'tasks' might have very little to do with an alternation in the properties of the neural code - and more to do with the differences in the movements involved. Many of the neurons are likely correlated with both Jaw movements and tongue movements - this complicates the interpretations and raises the possibility that the differences in tuning properties across tasks are trivial.

The population analyses for decoding are rudimentary and provide very coarse estimates (left, center, or right), it is also unclear what the major takeaways from the population decoding analyses are. The reduced classification accuracy could very well be a consequence of linear models being unable to account for the complexity of feeding movements, while the licking movements are 'simpler' and thus are better accounted for.

The nature of the nerve block and what sensory pathways are being affected is unclear - the trigeminal nerve contains many different sensory afferents - is there a characterization of how effectively the nerve impulses are being blocked? Have the authors confirmed or characterized the strength of their inactivation or block, I was unable to find any electrophysiological evidence characterizing the perturbation.

Overall, while this paper provides a descriptive account of the observed neural correlations and their alteration by perturbation, a synthesis of the observed changes and some insight into neural processing of tongue kinematics would strengthen this paper.

eLife assessment

The authors combined molecular dynamics simulations and experiments to study the role of ATP as a hydrotrope of protein aggregates. The topic is of major current interest and thus the study potentially makes an important contribution to the community. With the revised version, the level of evidence is considered generally solid, although there remains concern regarding the unusually high ATP concentration used in the simulation.

Reviewer #1 (Public review):

Summary:

This work combines molecular dynamics (MD) simulations along with experimental elucidation of the efficacy of ATP as biological hydrotrope. While ATP is broadly known as the energy currency, it has also been suggested to modulate the stability of biomolecules and their aggregation propensity. In the computational part of the work, the authors demonstrate that ATP increases the population of the more expanded conformations (higher radius of gyration) in both a soluble folded mini-protein Trp-cage and an intrinsically disordered protein (IDP) Aβ40. Furthermore, ATP is shown to destabilise the pre-formed fibrillar structures using both simulation and experimental data (ThT assay and TEM images). They have also suggested that the biological hydrotrope ATP has significantly higher efficacy as compared to the commonly used chemical hydrotrope sodium xylene sulfonate (NaXS).

Strengths:

This work presents a comprehensive and compelling investigation of the effect of ATP on the conformational population of two types of proteins: globular/folded and IDP. The role of ATP as an "aggregate solubilizer" of pre-formed fibrils has been demonstrated using both simulation and experiments. They also elucidate the mechanism of action of ATP as a multi-purpose solubilizer in a protein-specific manner. Depending on the protein, it can interact through electrostatic interactions (for predominantly charged IDPs like Aβ40), or primarily van der Waals' interactions through (for Trp-Cage).

Weaknesses:

The weaknesses and suggestions mentioned in my first review have been adequately addressed by the authors in the revised version of the manuscript.

Reviewer #3 (Public review):

Since its first experimental report in 2017 (Patel et al. Science 2017), there have been several studies on the phenomenon in which ATP functions as a biological hydrotrope of protein aggregates. In this manuscript, by conducting molecular dynamics simulations of three different proteins, Trp-cage, Abeta40 monomer, and Abeta40 dimer at concentrations of ATP (0.1, 0.5 M), which are higher than those at cellular condition (a few mM), Sarkar et al. find that the amphiphilic nature of ATP, arising from its molecular structure consisting of phosphate group (PG), sugar ring, and aromatic base, enables it to interact with proteins in a protein-specific manner and prevents their aggregation and solubilize if they aggregate. The authors also point out that in comparison with NaXS, which is the traditional chemical hydrotrope, ATP is more efficient in solubilizing protein aggregates because of its amphiphilic nature.

Trp-cage, featured with hydrophobic core in its native state, is denatured at high ATP concentration. The authors show that the aromatic base group (purine group) of ATP is responsible for inducing the denaturation of helical motif in the native state.

For Abeta40, which can be classified as an IDP with charged residues, it is shown that ATP disrupts the salt bridge (D23-K28) required for the stability of beta-turn formation.

By showing that ATP can disassemble preformed protein oligomers (Abeta40 dimer), the authors suggest that ATP is "potent enough to disassemble existing protein droplets, maintaining proper cellular homeostasis," and enhancing solubility.

Overall, the message of the paper is clear and straightforward to follow. In addition to the previous studies in the literature on this subject. (J. Am. Chem. Soc. 2021, 143, 31, 11982-11993; J. Phys. Chem. B 2022, 126, 42, 8486-8494; J. Phys. Chem. B 2021, 125, 28, 7717-7731; J. Phys. Chem. B 2020, 124, 1, 210-223), the study, which tested using MD simulations whether ATP is a solubilizer of protein aggregates, deserves some attention from the community and is worth publishing.

Weakness

My only major concern is that the simulations were performed at unusually high ATP concentrations (100 and 500 mM of ATP), whereas the real cellular concentration of ATP is 1-5 mM.

I was wondering if there is any report on a titration curve of protein aggregates against ATP, and what is the transition mid-point of ATP-induced solubility of protein aggregates. For instance, urea or GdmCl have long been known as the non-specific denaturants of proteins, and it has been well experimented that their transition mid-points of protein unfolding are in the range of ~(1 - 6) M depending on the proteins.

The authors responded to my comment on ATP concentration that because of the computational issue in all-atom simulations, they had no option but to employ mM-protein concentrations instead of micromolar concentrations, thus requiring 1000-folds higher ATP concentration, which is at least in accordance with the protein/ATP stoichiometry. However, I believe this is an issue common to all the researchers conducting MD simulations. Even if the system is in the same stoichiometric ratio, it is never clear to me (is it still dilute enough?) whether the mechanism of solubilization of aggregate at 1000 fold higher concentration of ATP remains identical to the actual process.

Author response:

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

Public Reviews: 

Reviewer #1 (Public Review): 

In this manuscript, Ferhat and colleagues describe their study aimed at developing a blood-brain barrier (BBB) penetrant agent that could induce hypothermia and provide neuroprotection from the sequelae of status epilepticus (SE) in mice. Hypothermia is used clinically in an attempt to reduce neurological sequelae of injury and disease. Hypothermia can be effective, but physical means used to reduce core body temperature are associated with untoward effects. Pharmacological means to induce hypothermia could be as effective with fewer untoward complications. Intracerebroventricularly applied neurotensin can cause hypothermia; however, neurotensin applied peripherally is degraded and does not cross the BBB. Here the authors develop and characterize a neurotensin conjugate that can reach the brain, induce hypothermia, and reduce seizures, cognitive changes, and inflammatory changes associated with status epilepticus. 

Strengths: <br /> (1) In general, the study is well-reasoned, well-designed, and seemingly well-executed. 

(2) Strong dose-response assessment of multiple neurotensin conjugates in mice. 

(3) Solid assessment of binding affinity, in vitro stability in blood, and brain uptake of the conjugate. 

(4) Appropriate inclusion of controls for SE and for drug injections. However, perhaps a vehicle control could have been employed. 

Sham animals received saline 0.9% which is the vehicle control considering it was used to dilute the water-soluble VH-N412 molecule.

(5) Multifaceted assessment of neurodegeneration, inflammation, and mossy fiber sprouting in the different groups. 

(6) Inclusion of behavioral assessments. 

(7) Evaluates NSTR1 receptor distribution in multiple ways; however, does not evaluate changes in receptor distribution or ping wo/w SE and/or various drugs. 

(8) Demonstrates that this conjugate can induce hypothermia and have positive effects on the sequelae of SE. Could have a great impact on the application of pharmacologically-induced hypothermia as a neuroprotective measure in patients. 

Weaknesses: 

(1) The authors make the claim, repeatedly, that the hypothermia caused by the neurotensin conjugate is responsible for the effects they see; however, what they really show is that the conjugate causes hypothermia AND has favorable effects on the sequelae of SE. They need to discuss that they did not administer the conjugate without allowing the pharmacological hypothermia (e.g., by warming the animal, etc.). 

We agree with Reviewer 1. We indeed hypothesize that it is principally the hypothermia induced by the NT conjugate that is responsible for the effects we observe. However, we do not exclude the possibility that the conjugate itself can have direct effects on the sequelae of SE. We tried to address this question with the in vitro experiments. Our results suggest that indeed, in the absence of hypothermia, the conjugate showed intrinsic neuroprotection of cultured hippocampal neurons challenged with excitotoxic agents such as NMDA or KA. Besides the description of these results in the “Results Section”, end of page 19 of the original manuscript, we had discussed them at the end of the “Discussion Section”, top of page 43 of the original manuscript.

In order to separate the hypothermia component from the potential direct neuroprotective effects of the NT conjugate, we did consider abolishing hypothermia in animals that were injected with the NT conjugate by warming them up. However, it is particularly difficult to increase in a well- controlled manner the body temperature of mice, in particular undergoing seizures, in a closed temperature-controlled chamber. In response to Reviewer 1 demand, we added a few sentences in the “Discussion Section”, page 45 of the revised version.

(2) In the status epilepticus studies, it is unclear how or whether they monitored animals for the development of spontaneous seizures. Can the authors please describe this?

The KA model we used was originally discovered more than 30 years ago, developed and very well characterized and mastered in our laboratory by Ben-Ari (Ben-Ari et al., 1979). Most of KA-treated mice that developed SE after KA injection developed spontaneous seizures subsequent to a latent period of about 1 week as described in Figure 3A, Results Section page 11 and in the reference we had mentioned in the Materials and Methods Section, page 27 (Schauwecker and Steward, 1997).

We agree that information regarding the development of spontaneous seizures is missing. We added 2 references, Gröticke et al., 2008; Wu et al., 2021 in the Materials and Methods Section, page 28 of the revised version, that describe the occurrence of spontaneous seizures after KA administration in mice. We also now added the following information in the Materials and Methods Section, end of page 29: In order to study mice in the chronic stage of epilepsy with spontaneous seizures, they were observed daily (at least 3 hours per day) for general behavior and occurrence of SRS. These are highly reproducible in the mouse KA model, allowing for visual monitoring and scoring of epileptic activity. After 3 weeks, most animals exhibited SRS, with 2 to 3 seizures per day, similar to previous observations (Wu et al., 2021). The detection of at least one spontaneous seizure per day was used as criterion indicating the animals had reached chronic phase that can ultimately be confirmed by mossy fiber sprouting (see Figure 7).

(3) They do not evaluate changes in receptor distribution or ping wo/w SE and/or various drugs. 

It is not clear to us what changes in receptor distribution need evaluation. We suppose the question concerns NTSR1 receptor. It would indeed be very interesting to compare NTSR1 in brain regions and different brain cells wo/w SE and/or various drugs, to assess receptor distribution or re-distribution, if any. However, addressing such a question is a project in itself that could not be addressed in the present study. Reviewer 1 also evokes ping wo/w SE and/or various drugs and if our understanding is correct, Reviewer 1 alludes to PING, Pyramidal Interneuronal Network γ (Dugladze et al., 2013, see reference below). Although we did not assess PING per se, we used multi-electrode arrays (MEA) on hippocampal brain slices stimulated wo/w KA to assess whether the VH-N412 conjugate could modulate pyramidal neuron activity. In order to respond to Reviewer 1 concern we added these data as Figure S2 with corresponding modifications in the Material and Methods Section (pages 34-35), in the Results Section (page 19) and in the Discussion Section page 43 of the revised version of our manuscript.

Dugladze T, Maziashvili N, Börgers C, Gurgenidze S, Häussler U, Winkelmann A, Haas CA, Meier JC, Vida I, Kopell NJ, Gloveli T. GABA(B) autoreceptor-mediated cell type-specific reduction of inhibition in epileptic mice. Proc Natl Acad Sci U S A. 2013 Sep 10;110(37):15073-8. doi: 10.1073/pnas.1313505110. Epub 2013 Aug 26. PMID: 23980149; PMCID: PMC3773756.

Bas du formulaire

(4) It is not clear why several different mouse strains were employed. 

We used 2 mouse strains in our work as mentioned in the Materials and Methods Section, page 21. The conjugates we developed and hypothermia evaluation were initially tested on adult Swiss CD-1 males. For the KA model and for behavioral tests, adult male FVB/N mice were used because they are considered as reliable and well described mouse models of epilepsy, where seizures are associated with cell death (Schauwecker, 2003). This not the case for a number of mouse strains that demonstrate very heterogeneous behavior in SE and heterogeneous neuronal death, sprouting and neuroinflammation. The FVB/N are also well suited for behavioral tests.

In response to the Reviewer 1 demand, the following sentence has been introduced in the Results Section, page 11 and in the Materials and Methods Section, page 21 of the revised manuscript: We assessed our conjugates in a model of KA-induced seizures using adult male FVB/N mice. This mouse strain was selected as a reliable and well described mouse model of epilepsy, where seizures are associated with cell death and neuroinflammation (Schauwecker, 2003; Wu et al., 2021).

Reviewer #2 (Public Review): 

Summary: 

The authors generated analogs consisting of modified neurotensin (NT) peptides capable of binding to low-density lipoprotein (LDL) and NT receptors. Their lead analog was further evaluated for additional validation as a novel therapeutic. The putative mechanism of action for NT in its antiseizure activity is hypothermia, and as therapeutic hypothermia has been demonstrated in epilepsy, NT analogs may confer antiseizure activity and avoid the negative effects of induced hypothermia. 

Strengths: 

The authors demonstrate an innovative approach, i.e. using LDLR as a means of transport into the brain, that may extend to other compounds. They systematically validate their approach and its potential through binding, brain penetration, in vivo antiseizure efficacy, and neuroprotection studies. 

Weaknesses: 

Tolerability studies are warranted, given the mechanism of action and the potential narrow therapeutic index. In vivo studies were used to assess the efficacy of the peptide conjugate analogs in the mouse KA model. However, it would be beneficial to have shown tolerability in naïve animals to better understand the therapeutic potential of this approach. 

Tolerability studies were performed, but the results were not presented in the first version of the manuscript. In order to comply with Reviewer 2 demand, we have added the following text in the Results section, page 11 of the revised version to describe our tolerability results.

Finally, tolerability studies were performed with the administration up to 20 and 40 mg/kg Eq. NT (i.e. 25.8 and 51.6 mg/kg of VH-N412) with n=3 for these doses. The rectal temperature of the animals did not fall below 32.5 to 33.2°C, similar to the temperature induced with the 4 mg/kg Eq. NT dose. We observed no mortality or notable clinical signs other than those associated with the rapid HT effect such as a decrease in locomotor activity. We thus report a very interesting therapeutic index since the maximal tolerated dose (MTD) was > 40 mg/kg Eq. NT, while the maximum effect is observed at a 10x lower dose of 4 mg/kg Eq. NT and an ED50 established at 0.69 mg/kg as shown in Figure 1G.

Mice may be particularly sensitive to hypothermia. It would be beneficial to show similar effects in a rat model. 

We have tested our conjugate in mice, rats, and pigs, with in all cases nice dose response curves. We added a few words in the Discussion Section, page 38 of the revised version to mention that we can elicit hypothermia with our conjugates in the above-mentioned species.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

(1) In Figures 4, 5, 6, 8, and 9, scale bars are needed on all panels. 

We have looked carefully at the Figures. Scale bars are present on all Figures, as mentioned in the Legends of all Figures, but not necessarily on all panel pictures at the same magnification.

(2) The supplemental would seemingly be better moved into the main body of the manuscript. 

In agreement with Reviewer 1 demand, we moved the Supplemental Figures into the main body of the manuscript, except for Figure S1, previously Figure S3, and the new Figure S2. Tables S1 to S5 remain as Supplemental files.

Reviewer #2 (Recommendations For The Authors): 

Activation of LDLRs can have widespread effects in the CNS and peripherally. The authors should further discuss any beneficial or untoward effects of binding to LDL and activating LDLRs. 

As mentioned in the Introduction and in a number of references where we describe the development of our family of LDLR peptide ligands (see below), we only selected peptide ligands that do not compete with LDL, one of the major ligands of the LDLR. We indeed showed that while LDL binds the ligand-binding domain of the LDLR, the peptide ligands we developed bind to the EGF-precursor homology domain of the receptor (See Malcor et al., 2008 below).

We have studied our peptide ligands in vitro and in vivo for more than 15 years and we have not observed beneficial or adverse effects. Actually, one of the members of our LDLR peptide family has been validated as a theragnostic agent and is in Phase 1 clinical trials for brain glioblastoma and pancreatic cancer. Hence, to our knowledge, the peptide ligand we describe in the present study shows no beneficial or untoward effects on LDL binding and activation of the LDLR. In response to Reviewer 2 recommendation, we added the following information and references in the Introduction Section, page 6 of the revised version of our manuscript: These peptides bind the EGF precursor homology domain of the LDLR and thus do not compete with LDL binding on the ligand-binding domain. To our knowledge, they have no beneficial or untoward effects on LDL binding and LDLR activity (Malcor et al., 2012; Jacquot et al., 2016; David et al., 2018; Varini et al., 2019; Acier et al., 2021, Yang et al., 2023; Broc et al., 2024).

Broc B, Varini K, Sonnette R, Pecqueux B, Benoist F, Masse M, Mechioukhi Y, Ferracci G, Temsamani J, Khrestchatisky M, Jacquot G, Lécorché P. LDLR-Mediated Targeting and Productive Uptake of siRNA-Peptide Ligand Conjugates In Vitro and In Vivo. Pharmaceutics. 2024 Apr 17;16(4):548. doi: 10.3390/pharmaceutics16040548. PMID: 38675209; PMCID: PMC11054735.

Yang X, Varini K, Godard M, Gassiot F, Sonnette R, Ferracci G, Pecqueux B, Monnier V, Charles L, Maria S, Hardy M, Ouari O, Khrestchatisky M, Lécorché P, Jacquot G, Bardelang D. Preparation and In Vitro Validation of a Cucurbit[7]uril-Peptide Conjugate Targeting the LDL Receptor. J Med Chem. 2023 Jul 13;66(13):8844-8857. doi: 10.1021/acs.jmedchem.3c00423. Epub 2023 Jun 20. PMID: 37339060. 

Acier A, Godard M, Gassiot F, Finetti P, Rubis M, Nowak J, Bertucci F, Iovanna JL, Tomasini R, Lécorché P, Jacquot G, Khrestchatisky M, Temsamani J, Malicet C, Vasseur S, Guillaumond F. LDL receptor-peptide conjugate as in vivo tool for specific targeting of pancreatic ductal adenocarcinoma. Commun Biol. 2021 Aug 19;4(1):987. doi: 10.1038/s42003-021-02508-0. PMID: 34413441; PMCID: PMC8377056.

Varini K, Lécorché P, Sonnette R, Gassiot F, Broc B, Godard M, David M, Faucon A, Abouzid K, Ferracci G, Temsamani J, Khrestchatisky M, Jacquot G. Target engagement and intracellular delivery of mono- and bivalent LDL receptor- binding peptide-cargo conjugates: Implications for the rational design of new targeted drug therapies. J Control Release. 2019 Nov 28;314:141-161. doi: 10.1016/j.jconrel.2019.10.033. Epub 2019 Oct 20. PMID: 31644939.

David M, Lécorché P, Masse M, Faucon A, Abouzid K, Gaudin N, Varini K, Gassiot F, Ferracci G, Jacquot G, Vlieghe P, Khrestchatisky M. Identification and characterization of highly versatile peptide-vectors that bind non- competitively to the low-density lipoprotein receptor for in vivo targeting and delivery of small molecules and protein cargos. PLoS One. 2018 Feb 27;13(2):e0191052. doi: 10.1371/journal.pone.0191052. PMID: 29485998; PMCID: PMC5828360.

Molino Y, David M, Varini K, Jabès F, Gaudin N, Fortoul A, Bakloul K, Masse M, Bernard A, Drobecq L, Lécorché P, Temsamani J, Jacquot G, Khrestchatisky M. Use of LDL receptor-targeting peptide vectors for in vitro and in vivo cargo transport across the blood-brain barrier. FASEB J. 2017 May;31(5):1807-1827. doi: 10.1096/fj.201600827R. Epub 2017 Jan 20. PMID: 28108572.

Jacquot G, Lécorché P, Malcor JD, Laurencin M, Smirnova M, Varini K, Malicet C, Gassiot F, Abouzid K, Faucon A, David M, Gaudin N, Masse M, Ferracci G, Dive V, Cisternino S, Khrestchatisky M. Optimization and in Vivo Validation of Peptide Vectors Targeting the LDL Receptor. Mol Pharm. 2016 Dec 5;13(12):4094-4105. doi: 10.1021/acs.molpharmaceut.6b00687. Epub 2016 Oct 11. PMID: 27656777.

Malcor JD, Payrot N, David M, Faucon A, Abouzid K, Jacquot G, Floquet N, Debarbieux F, Rougon G, Martinez J, Khrestchatisky M, Vlieghe P, Lisowski V. Chemical optimization of new ligands of the low-density lipoprotein receptor as potential vectors for central nervous system targeting. J Med Chem. 2012 Mar 8;55(5):2227-41. doi: 10.1021/jm2014919. Epub 2012 Feb 14. PMID: 22257077.

As described above, the authors should also comment on the tolerability of these analogs. 

Tolerability studies were performed, but the results were not presented in the first version of the manuscript. In order to comply with Reviewer 2 demand, we have added the following text in the Results section, page 11 of the revised version to describe our tolerability results.

Finally, tolerability studies were performed with the administration up to 20 and 40 mg/kg Eq. NT (i.e. 25.8 and 51.6 mg/kg of VH-N412) with n=3 for these doses. The rectal temperature of the animals did not fall below 32.5 to 33.2°C, similar to the temperature induced with the 4 mg/kg Eq. NT dose. We observed no mortality or notable clinical signs other than those associated with the rapid HT effect such as a decrease in locomotor activity. We thus report a very interesting therapeutic index since the maximal tolerated dose (MTD) was > 40 mg/kg Eq. NT, while the maximum effect is observed at a 10x lower dose of 4 mg/kg Eq. NT and an ED50 established at 0.69 mg/kg as shown in Figure 1G.

eLife assessment

The authors developed a method to allow a hypothermic agent, neurotensin, to cross the blood-brain barrier so it could potentially protect the brain from seizures and the adverse effects of seizures. The work is important because it is known that cooling the brain can protect it but developing a therapeutic approach based on that knowledge has not been done. The paper is well presented and the data are convincing. Revisions to clarify some of the methods and results improved the paper and more data about tolerability would improve the paper further.

Reviewer #1 (Public review):

In this manuscript, Ferhat and colleagues describe their study aimed at developing a blood brain barrier (BBB) penetrant agent that could induce hypothermia and provide neuroprotection from the sequelae of status epilepticus (SE) in mice. Hypothermia is used clinically in an attempt to reduce neurological sequelae of injury and disease. Hypothermia can be effective, but physical means used to reduce core body temperature is associated with untoward effects. Pharmacological means to induce hypothermia could be as effective with fewer untoward complications. Intracerebroventricularly applied neurotensin can cause hypothermia; however, neurotensin applied peripherally is degraded and does not cross the BBB. Here the authors develop and characterize a neurotensin conjugate that can reach the brain, induce hypothermia, and reduce seizures, cognitive changes, and inflammatory changes associated with status epilepticus.

Strengths:

(1) In general, the study is well reasoned, well designed, and seemingly well executed.<br /> (2) Strong dose-response assessment of multiple neurotensin conjugates in mice.<br /> (3) Solid assessment of binding affinity, in vitro stability ion blood, and brain uptake of the conjugate.<br /> (4) Appropriate inclusion of controls for SE and for drug injections.<br /> (5) Multifaceted assessment of neurodegeneration, inflammation, and mossy fiber sprouting in the different groups.<br /> (6) Inclusion of behavioral assessments.<br /> (7) Evaluate NSTR1 receptor distribution in multiple ways.<br /> (8) Demonstrate that this conjugate can induce hypothermia and have positive effects on the sequelae of SE. Could have great impact on the application of pharmacologically-induced hypothermia as a neuroprotective measure in patients.

Weaknesses:

(1) The authors make the claim, repeatedly, that the hypothermia caused by the neurotensin conjugate is responsible for the effects they see; however, what they really show is that the conjugate causes hypothermia AND has favorable effects on the sequelae of SE. They have now discussed this limitation in the manuscript.

Reviewer #2 (Public review):

Summary:

The authors generated analogs consisting of modified neurotensin (NT) peptides capable of binding to low density lipoprotein (LDL) and NT receptors. Their lead analog was further evaluated for additional validation as a novel therapeutic. The putative mechanism of action for NT in its antiseizure activity is hypothermia, and as therapeutic hypothermia has been demonstrated in epilepsy, NT analogs may confer antiseizure activity and avoid the negative effects of induced hypothermia.

Strengths:

The authors demonstrate an innovative approach, i.e. using LDLR as a means of transport into the brain, that may extend to other compounds. They systematically validate their approach and its potential through binding, brain penetration, in vivo antiseizure efficacy, and neuroprotection studies.

Weaknesses:

Tolerability studies are warranted, given the mechanism of action and the potential narrow therapeutic index. In vivo studies were used to assess efficacy of the peptide conjugate analogs in the mouse KA model. However, it would be beneficial to have shown tolerability in naïve animals to better understand the therapeutic potential of this approach.

Mice may be particularly sensitive to hypothermia. It would be beneficial to show similar effects in a rat model.

Author response:

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

We are deeply appreciative of the reviewers' insightful comments and constructive feedback on our manuscript. In response, we have implemented substantial revisions to enhance the clarity and impact of our work. Key changes include: 

Reframing: We have shifted our focus from cognitive control to attention and memory processes, aligning more closely with our experimental design. This reframing is reflected throughout the manuscript, including additional citations highlighting the triple network model's involvement in memory processing. To reflect this change, we have updated the title to "Causal dynamics of salience, default mode, and frontoparietal networks during episodic memory formation and recall: A multi-experiment iEEG replication".

Control analyses using resting-state epochs: We have conducted new analyses comparing task periods to resting baseline epochs. These results demonstrate enhanced directed information flow from the anterior insula to both the default mode and frontoparietal networks during encoding and recall periods compared to resting state across all four experiments. This finding underscores the anterior insula's critical role in memory and attention processing.

Control analysis using the inferior frontal gyrus: To address specificity concerns, we performed control analyses using the inferior frontal gyrus as a comparison region. This analysis confirms that the observed directed information flow to the default mode and frontoparietal networks is specific to the anterior insula, rather than a general property of task-engaged brain regions.

These revisions, combined with our rigorous methodologies and comprehensive analyses, provide compelling support for the central claims of our manuscript. We believe these changes significantly enhance the scientific contribution of our work.

Our point-by-point responses to the reviewers' comments are provided below.

Reviewer 1:

-  The authors present results from an impressively sized iEEG sample. For reader context, this type of invasive human data is difficult and time-consuming to collect and many similar studies in high-level journals include 5-20 participants, typically not all of whom have electrodes in all regions of interest. It is excellent that they have been able to leverage open-source data in this way. 

-  Preprocessing of iEEG data also seems sensible and appropriate based on field standards. 

-  The authors tackle the replication issues inherent in much of the literature by replicating findings across task contexts, demonstrating that the principles of network communication evidenced by their results generalize in multiple task memory contexts. Again, the number of iEEG patients who have multiple tasks' worth of data is impressive. 

We thank the reviewer for the encouraging comments and appreciate the positive feedback.  

(1.1) The motivation for investigating the tripartite network during memory tasks is not currently well-elaborated. Though the authors mention, for example, that "the formation of episodic memories relies on the intricate interplay between large-scale brain networks (p. 4)", there are no citations provided for this statement, and the reader is unable to evaluate whether the nodes and networks evidenced to support these processes are the same as networks measured here. 

Recommendation: Detail with citations the motivation for assessing the tripartite network in these tasks. Include work referencing network-level and local effects during encoding and recall.

We appreciate the reviewer's feedback and suggestions for improving our framing. We have substantially expanded and revised the Introduction to elaborate on the motivation for investigating the tripartite network during memory tasks, supported by relevant citations.

We now provide a stronger rationale for examining these networks in the context of episodic memory, emphasizing that while the tripartite network has been extensively studied in cognitive control tasks, growing evidence suggests its relevance to episodic memory as a domain-general network. We cite several key studies that demonstrate the involvement of the salience, default mode, and frontoparietal networks in memory processes, including work by Sestieri et al. (2014) and Vatansever et al. (2021), which show the consistent engagement of these networks during memory tasks. We have also included references to studies examining network-level and local effects during encoding and recall, such as the work by Xie et al. (2012) on disrupted intrinsic connectivity in amnestic mild cognitive impairment, and Le Berre et al. (2017) on the role of insula connectivity in memory awareness (pages 4-5).

Furthermore, we have clarified how our study aims to address gaps in the current understanding by investigating the electrophysiological basis of these network interactions during memory formation and retrieval, which has not been explored in previous research. This expanded framing provides a clearer motivation for our investigation and places our study within the broader context of memory and network neuroscience research (pages 3-6).  

(1.2) In addition, though the tripartite network has been proposed to support cognitive control processes, and the neural basis of cognitive control is the framed focus of this work, the authors do not demonstrate that they have measured cognitive control in addition to simple memory encoding and retrieval processes. Tasks that have investigated cognitive control over memory (such as those cited on p. 13 - Badre et al., 2005; Badre & Wagner, 2007; Wagner et al., 2001; Wagner et al., 2005) generally do not simply include encoding, delay, and recall (as the tasks used here), but tend to include some manipulation that requires participants to engage control processes over memory retrieval, such as task rules governing what choice should be made at recall (e.g., from Badre et al., 2005 Fig. 1: congruency of match, associative strength, number of choices, semantic similarity). Moreover, though there are task-responsive signatures in the nodes of the tripartite networks, concluding that cognitive control is present because cognitive control networks are active would be a reverse inference.

Recommendation: If present, highlight components of the tasks that are known to elicit cognitive control processes and cite relevant literature. If the tasks cannot be argued to elicit cognitive control, reframe the motivation to focus on task-related attention or memory processes. If the latter, reframe the motivation for investigating the tripartite network in this context absent control.

We appreciate the reviewer's insightful comment and recommendation. We acknowledge that our tasks do not include specific manipulations designed to elicit cognitive control processes over memory retrieval. In light of this, we have reframed our motivation and discussion to focus on the role of the tripartite network in attention and memory processes more broadly, rather than cognitive control specifically (pages 3-6).

As noted in Response 1.1, we have revised the Introduction to emphasize the domain-general nature of these networks and their involvement in various cognitive processes, including memory. We also highlight how the salience, default mode, and frontoparietal networks contribute to different aspects of memory formation and retrieval, drawing on relevant literature.

Our revised framing examines the salience network's role in detecting behaviorally relevant stimuli and orienting attention during encoding, the default mode network's involvement in internally-driven processes during recall, and the frontoparietal network's contribution to maintaining and manipulating information in working memory. We now present our study as an investigation into how these networks interact during different phases of memory processing, rather than focusing specifically on cognitive control. This approach aligns better with our experimental design and allows us to explore the broader applicability of the tripartite network model to memory processes. 

This revised reframing provides a more accurate representation of our study's scope and contribution to understanding the role of large-scale brain networks in memory formation and retrieval (pages 3-6). 

(1.3) It is currently unclear if the directed information flow from AI to DMN and FPN nodes truly arises from task-related processes such as cognitive control or if it is a function of static brain network characteristics constrained by anatomy (such as white matter connection patterns, etc.). This is a concern because the authors did not find that influences of AI on DMN or FPN are increased relative to a resting baseline (collected during the task) or that directed information flow differs in successful compared to unsuccessful retrieval. I doubt that this AI influence is 1) supporting a switch between the DMN and FPN via the SN or 2) relevant for behavior if it doesn't differ from baseline-active task or across accuracy conditions. An additional comparison that may help investigate whether this is reflective of static connectivity characteristics would be a baseline comparison during non-task rest or sleep periods.  

Recommendation: As described in the task of the concern, analyze the PTE across the same contacts during sleep or task-free rest periods (if present in the dataset). 

We thank the reviewer for this suggestion. We have now carried out additional analyses using resting-state baseline epochs. We found that directed information flow from the AI to both the DMN and FPN were enhanced during the encoding and recall periods compared to resting-state baseline in all four experiments. These new results have now been included in the revised Results (page 12):    

“Enhanced information flow from the AI to the DMN and FPN during episodic memory processing, compared to resting-state baseline  

We next examined whether directed information flow from the AI to the DMN and FPN nodes during the memory tasks differed from the resting-state baseline. Resting-state baselines were extracted immediately before the start of the task sessions and the duration of task and rest epochs were matched to ensure that differences in network dynamics could not be explained by differences in duration of the epochs. Directed information flow from the AI to both the DMN and FPN were higher during both the memory encoding and recall phases and across the four experiments, compared to baseline in all but two cases (Figures S6, S7). These findings provide strong evidence for enhanced role of AI directed information flow to the DMN and FPN during memory processing compared to the resting state.” 

(1.4) Related to the above concern, it is also questionable how directed information flow from AI facilitates switching between FPN and DMN during both encoding and recall if high gamma activity does not significantly differ in AI versus PCC or mPFC during recall as it does during encoding. It seems erroneous to conclude that the network-level communication is happening or happening with the same effect during both task time points when these effects are decoupled in such a way from the power findings.  

We appreciate the reviewer's insightful observation regarding the apparent discrepancy between our directed information flow findings and the high-gamma activity results. This comment highlights an important distinction in interpreting our results, and we thank the reviewer for the opportunity to address this point.

Our findings demonstrate that directed information flow from the AI to the DMN and FPN persists during both encoding and recall, despite differences in local high-gamma activity patterns. This dissociation suggests that the network-level communication facilitated by the AI may operate independently of local activation levels in individual nodes. It is important to note that our directed connectivity analysis (using phase transfer entropy) was conducted on broadband signals (0.5-80 Hz), while the power analysis focused specifically on the high-gamma band (80-160 Hz). These different frequency ranges may capture distinct aspects of neural processing. The broadband connectivity might reflect more general, sustained network interactions, while high-gamma activity may be more sensitive to specific task demands or cognitive processes.

The phase transfer entropy analysis captures directed interactions over extended time periods, while the high-gamma power analysis provides a more temporally precise measure of local neural activity. The persistent directed connectivity from AI during recall, despite changes in local activity, might reflect the AI's ongoing role in coordinating network interactions, even when its local activation is not significantly different from other regions.

Rather than facilitating "switching" between FPN and DMN, as we may have previously overstated, our results suggest that the AI maintains a consistent pattern of influence on both networks across task phases. This influence might serve different functions during encoding (e.g., orienting attention to external stimuli) and recall (e.g., monitoring and evaluating retrieved information), even if local activation patterns differ.

It is crucial to note that in the three verbal tasks, our analysis of memory recall is time-locked to word production onset. However, the precise timing of the internal recall process initiation is unknown. This limitation may affect our ability to capture the full dynamics of network interactions during recall, particularly in the early stages of memory retrieval. Interestingly, in the spatial memory task WMSM, the PCC/precuneus exhibited an earlier onset and enhanced activity compared to the AI. This task may provide a clearer window into recall processes:

findings align with the view that DMN nodes may play a crucial role in triggering internal recall processes. However, the precise timing of internal retrieval initiation remains a challenge in the three verbal tasks, potentially limiting our ability to capture the full dynamics of regional activity, and its replicability, during early stages of recall.

These observations highlight the need for more detailed investigation of the temporal dynamics of network interactions during memory recall. To further elucidate the relationship between directed connectivity and local activity, future studies could employ time-resolved connectivity analyses and investigate coupling between different frequency bands. This could provide a more precise understanding of how network-level communication relates to local neural dynamics across different task phases.

We have revised the manuscript to more accurately reflect these points and avoid overstating the implications of our findings (pages 15-19). We thank the reviewer for prompting this important clarification, which we believe strengthens the interpretation and discussion of our results.

(1.5) Missing information about the methods used for time-frequency conversion for power calculation and the power normalization/baseline-correction procedure bars a thorough evaluation of power calculation methods and results. 

Recommendation: Include more information about how power was calculated. For example, how were time-series data converted to time-frequency (with complex wavelets, filter-hilbert, etc.)? What settings were used (frequency steps, wavelet length)? How were power values checked for outliers and normalized (decibels, Z-transform)? How was baseline correction applied (subtraction, division)?

We have now included detailed information related to our power calculation and normalization steps as we note on page 28: “We first filtered the signals in the high-gamma (80160 Hz) frequency band (Canolty et al., 2006; Helfrich & Knight, 2016; Kai J. Miller, Weaver, & Ojemann, 2009) using sequential band-pass filters in increments of 10 Hz (i.e., 80–90 Hz, 90– 100 Hz, etc.), using a fourth order two-way zero phase lag Butterworth filter. We used these narrowband filtering processing steps to correct for the 1/f decay of power. We then calculated the amplitude (envelope) of each narrow band signal by taking the absolute value of the analytic signal obtained from the Hilbert transform (Foster, Rangarajan, Shirer, & Parvizi, 2015). Each narrow band amplitude time series was then normalized to its own mean amplitude, expressed as a percentage of the mean. Finally, we calculated the mean of the normalized narrow band amplitude time series, producing a single amplitude time series. Signals were then smoothed using 0.2s windows with 90% overlap (Kwon et al., 2021) and normalized with respect to 0.2s pre-stimulus periods by subtracting the pre-stimulus baseline from the post-stimulus signal.” 

(1.6) If revisions to the manuscript can address concerns about directed information flow possibly being due to anatomical constraints - such as by indicating that directed information flow is not present during non-task rest or sleep - this work may convey important information about the structure and order of communication between these networks during attention to tasks in general. However, the ability of the findings to address cognitive control-specific communication and the nature of neurophysiological mechanisms of this communication - as opposed to the temporal order and structure of recruited networks - may be limited.

We appreciate the reviewer's insightful feedback, which has led to significant improvements in our manuscript. In response, we have made the following key changes. We have shifted our focus from cognitive control to the broader roles of the tripartite network in attention and memory processes. This reframing aligns more closely with our experimental design and the nature of our tasks. We have revised the Introduction, Results, and Discussion sections to reflect this perspective, providing a more accurate representation of our study's scope and contribution. Additionally, to strengthen our findings, we have conducted new analyses comparing task periods to resting-state baselines. These analyses revealed that directed information flow from the anterior insula to both the DMN and FPN was significantly enhanced during memory encoding and recall periods compared to resting-state across all four experiments. This finding provides robust evidence for the specific involvement of these network interactions in memory processing. Please also see Response 1.2 above. 

(1.7) Because phase-transfer entropy is presented as a "causal" analysis in this investigation (PTE), I also believe it is important to highlight for readers recent discussions surrounding the description of "causal mechanisms" in neuroscience (see "Confusion about causation" section from Ross and Bassett, 2024, Nature Neuroscience). A large proportion of neuroscientists (admittedly, myself included) use "causal" only to refer to a mechanism whose modulation or removal (with direct manipulation, such as by lesion or stimulation) is known to change or control a given outcome (such as a successful behavior). As Ross and Bassett highlight, it is debatable whether such mechanistic causality is captured by Granger "causality" (a.k.a. Granger prediction) or the parametric PTE, and the imprecise use of "causation" may be confusing. The authors could consider amending language regarding this analysis if they are concerned about bridging these definitions of causality across a wide audience. 

We thank the reviewer for this suggestion. We would like to clarify here that we define causality in our manuscript as follows: a brain region has a causal influence on a target if knowing the past history of temporal signals in both regions improves the ability to predict the target's signal in comparison to knowing only the target's past, as defined in earlier studies (Granger, 1969; Lobier, Siebenhühner, Palva, & Matias, 2014). We have now included this clarification in the Introduction section (page 6).  

We also agree with the reviewer that to more mechanistically establish a causal link between the neural dynamics and behavior, lesion or brain stimulation studies are necessary. We have now acknowledged this in the revised Discussion as we note: “Although our computational methods suggest causal influences, direct causal manipulations, such as targeted brain stimulation during memory tasks, are needed to establish definitive causal relationships between network nodes.” (page 19). 

Minor additional information that would be helpful to the reader to include: 

(1.8) How exactly was line noise (p. 24) removed? (For example, if notch filtered, how were slight offsets of the line noise from exactly 60.0Hz and harmonics identified and handled?). 

We would like to clarify here that to filter line noise and its harmonics, we used bandstop filters at 57-63 Hz, 117-123 Hz, and 177-183 Hz. To create a band-stop filter, we used a fourth order two-way zero phase lag Butterworth filter. This information has now been included in the revised Methods (page 26). 

(1.9) Why were the alpha and beta bands collapsed for narrowband filtering?

Please note that we did not combine the alpha (8-12 Hz) and beta (12-30 Hz) bands for narrowband filtering, rather these two frequency bands were analyzed separately. However, we combined the delta (0.5-4 Hz) and theta (4-8 Hz) frequency bands into a combined delta-theta (0.5-8 Hz) frequency band for our analysis since previous human electrophysiology studies have not settled on a specific band of frequency (delta or theta) for memory processing. Previous human iEEG (Ekstrom et al., 2005; Ekstrom & Watrous, 2014; Engel & Fries, 2010; Gonzalez et al., 2015; Watrous, Tandon, Conner, Pieters, & Ekstrom, 2013) as well as scalp EEG and MEG studies, have shown that both the delta and theta frequency band oscillations play a prominent role for human memory encoding as well as retrieval (Backus, Schoffelen, Szebényi, Hanslmayr, & Doeller, 2016; Clouter, Shapiro, & Hanslmayr, 2017; Griffiths, Martín-Buro, Staresina, & Hanslmayr, 2021; Guderian & Düzel, 2005; Guderian, Schott, Richardson-Klavehn, & Düzel, 2009).  

Reviewer 2:

In this study, the authors leverage a large public dataset of intracranial EEG (the University of Pennsylvania RAM repository) to examine electrophysiologic network dynamics involving the participation of salience, frontoparietal, and default mode networks in the completion of several episodic memory tasks. They do this through a focus on the anterior insula (AI; salience network), which they hypothesize may help switch engagement between the DMN and FPN in concert with task demands. By analyzing high-gamma spectral power and phase transfer entropy (PTE; a putative measure of information "flow"), they show that the AI shows higher directed PTE towards nodes of both the DMN and FPN, during encoding and recall, across multiple tasks. They further demonstrate that high-gamma power in the PCC/precuneus is decreased relative to the AI during memory encoding. They interpret these results as evidence of "triple-network" control processes in memory tasks, governed by a key role of the AI. 

I commend the authors on leveraging this large public dataset to help contextualize network models of brain function with electrophysiological mechanisms - a key problem in much of the fMRI literature. I also appreciate that the authors emphasized replicability across multiple memory tasks, in an effort to demonstrate conserved or fundamental mechanisms that support a diversity of cognitive processes. However, I believe that their strong claims regarding causal influences within circumscribed brain networks cannot be supported by the evidence as presented. In my efforts to clearly communicate these inadequacies, I will suggest several potential analyses for the authors to consider that might better link the data to their central hypotheses.

We thank the reviewer for the encouraging comments and suggestions for improving the manuscript. Please see our detailed responses and clarifications below. 

(2.1) As a general principle, the effects that the authors show - both in regards to their highgamma power analysis and PTE analysis - do not offer sufficient specificity for a reader to understand whether these are general effects that may be repeated throughout the brain, or whether they reflect unique activity to the networks/regions that are laid out in the Introduction's hypothesis. This lack of specificity manifests in several ways, and is best communicated through examples of control analyses. 

We appreciate the reviewer's insightful comment regarding the specificity of our findings. We agree that additional analyses could provide valuable context for interpreting our results. In response, we have conducted the following additional analyses and made corresponding revisions to the manuscript:

Following the reviewer's suggestion, we have selected the inferior frontal gyrus (IFG, BA 44) as a control region. The IFG serves as an ideal control region due to its anatomical adjacency to the AI, its involvement in a wide range of cognitive control functions including response inhibition (Cai, Ryali, Chen, Li, & Menon, 2014), and its frequent co-activation with the AI in fMRI studies. Furthermore, the IFG has been associated with controlled retrieval of memory (Badre et al., 2005; Badre & Wagner, 2007; Wagner et al., 2001), making it a compelling region for comparison. We repeated our PTE analysis using the IFG as the source region, comparing its directed influence on the DMN and FPN nodes to that of the AI.  

Our analysis revealed a striking contrast between the AI and IFG in their patterns of directed information flow. While the AI exhibited strong causal influences on both the DMN and FPN, the IFG showed the opposite pattern. Specifically, both the DMN and FPN demonstrated higher influence on the IFG than the reverse, during both encoding and recall periods, and across all four memory experiments (Figures S4, S5). 

These findings highlight the unique role of the AI in orchestrating large-scale network dynamics during memory processes. The AI's pattern of directed information flow stands in contrast to that of the IFG, despite their anatomical proximity and shared involvement in cognitive control processes. This dissociation underscores the specificity of the AI's function in coordinating network interactions during memory formation and retrieval. These results have now been included in our revised Results on page 11.  

(2.2) First, the PTE analysis is focused solely on the AI's interactions with nodes of the DMN and FPN; while it makes sense to focus on this putative "switch" region, the fact that the authors report significant PTE from the AI to nodes of both networks, in encoding and retrieval, across all tasks and (crucially) also at baseline, raises questions about the meaningfulness of this statistic. One way to address this concern would be to select a control region that would be expected to have little/no directed causal influence on these networks and repeat the analysis. Alternatively (or additionally), the authors could examine the time course of PTE as it evolves throughout an encoding/retrieval interval, and relate that to the timing of behavioral events or changes in high-gamma power. This would directly address an important idea raised in their own Discussion, "the AI is wellpositioned to dynamically engage and disengage with other brain areas."  

Please see Response 2.1 above for additional analyses related to control region.  

We also appreciate the reviewer's suggestion regarding time-resolved PTE analysis. However, it's important to note that our current methodology does not allow for such fine-grained temporal analysis. This is due to the fact that PTE, which is an information theoretic measure and relies on constructing histograms of occurrences of singles, pairs, or triplets of instantaneous phase estimates from the phase time-series (Hillebrand et al., 2016) (Methods), requires sufficient number of cycles in the phase time-series for its reliable estimation (Lobier et al., 2014). PTE is based on estimating the time-delayed directed influences from one time-series to the other and its estimate is the most accurate when a large number of time-points (cycles) are available (Lobier et al., 2014). Since our encoding and recall epochs in the verbal recall tasks were only 1.6 seconds long, which corresponds to only 800 time-points with a 500 Hz sampling rate, we used the entire encoding and recall epochs for the most efficient estimate of PTE, rather than estimating PTE in a time-resolved manner. Please note that this is consistent with previous literature which have used ~ 225000 time-points (3 minutes of resting-state data with 1250 Hz sampling rate) for estimating PTE, for example, see (Hillebrand et al., 2016). 

This limitation prevents us from examining how directed connectivity evolves throughout the encoding and retrieval intervals on a moment-to-moment basis. Future studies employing longer task epochs or alternative methods for time-resolved connectivity analysis could provide valuable insights into the dynamic engagement and disengagement of the AI with other brain areas based on task demands. Such analyses could potentially reveal task-specific temporal patterns in the AI's influence on DMN and FPN nodes during different phases of memory processing.

Finally, it is crucial to note that in the three verbal tasks, our analysis of memory recall is timelocked to word production onset. However, the precise timing of the internal retrieval process initiation is unknown. This limitation may affect our ability to capture the full dynamics of network interactions during recall, particularly in the early stages of memory retrieval. Interestingly, in the spatial memory task, where this timing issue is less problematic due to the nature of the task, we observe that the PCC/precuneus shows an earlier onset of activity compared to the AI. This process is aligned with the view that DMN nodes may trigger internal recall processes, the full extent and replication of which across verbal and spatial tasks could not be examined in this study.  

We have added a discussion of these limitations and future directions to the manuscript to provide a more nuanced interpretation of our findings and to highlight important areas for further investigation (page 19). 

(2.3) Second, the authors state that high-gamma suppression in the PCC/precuneus relative to the AI is an anatomically specific signature that is not present in the FPN. This claim does not seem to be supported by their own evidence as presented in the Supplemental Data (Figures S2 and S3), which to my eye show clear evidence of relative suppression in the MFG and dPPC (e.g. S2a and S3a, most notably) which are notated as "significant" with green bars. I appreciate that the magnitude of this effect may be greater in the PCC/precuneus, but if this is the claim it should be supported by appropriate statistics and interpretation.  

We thank the reviewer for raising this point. We have now directly compared the high-gamma power of the PCC/precuneus with the dPPC and MFG nodes of the FPN and we note that the suppression effects of the PCC/precuneus are stronger compared to those of the dPPC and MFG during memory encoding (Figures S8, S9). 

(2.4) I commend the authors on emphasizing replicability, but I found their Bayes Factor (BF) analysis to be difficult to interpret and qualitatively inconsistent with the results that they show. For example, the authors state that BF analysis demonstrates "high replicability" of the gamma suppression effect in Figure 3a with that of 3c and 3d. While it does appear that significant effects exist across all three tasks, the temporal structure of high gamma signals appears markedly different between the two in ways that may be biologically meaningful. Moreover, it appears that the BF analysis did not support replicability between VFR and CATVFR, which is very surprising; these are essentially the same tasks (merely differing in the presence of word categories) and would be expected to have the highest degree of concordance, not the lowest. I would suggest the authors try to analytically or conceptually reconcile this surprising finding. 

We appreciate the reviewer's commendation on our emphasis on replicability and thank the reviewer for the opportunity to provide clarification.

First, we would like to clarify the nature of our BF analysis. Bayes factors are calculated as the ratio of the marginal likelihood of the replication data, given the posterior distribution estimated from the original data, and the marginal likelihood for the replication data under the null hypothesis of no effect (Ly, Etz, Marsman, & Wagenmakers, 2019). Specifically, BFs use the posterior distribution from the first experiment as a prior distribution for the replication test of the second experiment to constitute a joint multivariate distribution (i.e., the additional evidence for the alternative hypothesis given what was already observed in the original study) and this joint distribution is dependent on the similarity between the two experiments (Ly et al., 2019).  This analysis revealed that PCC/precuneus suppression, in comparison to the AI during memory encoding, observed in the VFR during memory encoding was detected in two other tasks, PALVCR, and WMSM with high BFs. In the CATVFR task, although there were short time periods of PCC/precuneus suppression (Figure 3), the effects were not strong enough like the three other tasks.  

Regarding the high-gamma suppression effect, our BF analysis indeed supports replicability across the VFR, PALVCR, and WMSM tasks. While we agree with the reviewer that the temporal structure of high-gamma signals appears different across tasks, the BF analysis focuses on the overall presence of the suppression effect rather than its precise temporal profile. The high BFs indicate that the core finding - PCC/precuneus suppression relative to the AI during memory encoding - is replicated across these tasks, despite differences in the timing of this suppression. Moreover, at no time point did responses in the PCC/precuneus exceed that of the AI in any of the four memory encoding tasks. 

The reason for differences in temporal profiles is not clear. While VFR and CATVFR are similar, the addition of categorical structure in CATVFR may have introduced cognitive processes that alter the temporal dynamics of regional responses. Moreover, differences in electrode placements across participants in each experiment may also have contributed to variability in the observed effects. Further studies using within-subjects experimental designs are needed to address this. 

We have updated our Results and Discussion sections to reflect these points and to provide a more nuanced interpretation of the replicability across tasks.  

(2.5) To aid in interpretability, it would be extremely helpful for the authors to assess acrosstask similarity in high-gamma power on a within-subject basis, which they are wellpowered to do. For example, could they report the correlation coefficient between HGP timecourses in paired-associates versus free-recall tasks, to better establish whether these effects are consistent on a within-subject basis? This idea could similarly be extended to the PTE analysis. Across-subject correlations would also be a welcome analysis that may provide readers with better-contextualized effect sizes than the output of a Bayes Factor analysis.  

We thank the reviewer for this suggestion. However, a within-subject analysis was not possible because very few participants participated in multiple memory tasks. 

For example, for the AI-PCC/Pr analysis, only 1 individual participated in both the VFR and PALVCR tasks (Tables S2a, S2c). Similarly, for AI-mPFC analysis, only 3 subjects participated in both the VFR and PALVCR tasks (Tables S2a, S2c).  

Due to these small sample sizes, it was not feasible for us to assess replicability across tasks on a within-subject basis in our dataset. Therefore, for all our analysis, we have pooled electrode pairs across subjects and then subjected these to a linear mixed effects modeling framework for assessing significance and then subsequently assessing replicability of these effects using the Bayes factor (BF) framework.    

Recommendations For The Authors: 

(2.6) I would emphasize manuscript organization in a potential rewrite; it was very difficult to follow which analyses were attempting to show a contrast between effects versus a similarity between effects. Results were grouped by the underlying experimental conditions (e.g. encoding/recall, network identity, etc.) but may be better grouped according to the actual effects that were found. 

We thank the reviewer for this suggestion. We considered this possibility, but we feel that the Results section is best organized in the order of the hypotheses we set out to test, starting from analyzing local brain activity using high-gamma power analysis, and then results related to analyzing brain connectivity using PTE. All these results are systematically ordered by presenting results related to encoding first and then the recall periods as they appear sequentially in our task-design, presenting the results related to the VFR task first and then demonstrating replicability of the results in the three other experiments. Results are furthermore arranged by nodes, where we first discuss results related to the DMN nodes, and then the same for the FPN nodes. This is to ensure systematic, unbiased organization of all our results for the readers to clearly follow the hypotheses, statistical analyses, and the brain regions considered. Therefore, for transparency and ethical reasons, we would respectfully like to present our results as they appear in our current manuscript, rather than presenting the results based on effect sizes. 

However, please note that we indeed have ordered our results in the Discussion section based on actual effects, as suggested by the reviewer.  

(2.7) The absence of a PTE effect when analyzing through the lens of successful vs. unsuccessful memory is an important limitation of the current study and a significant departure from the wealth of subsequent memory effects reported in the literature (which the authors have already done a good job citing, e.g. Burke et al. 2014 Neuroimage). I'm glad that the authors raised this in their Discussion, but it is important that the results of such an analysis actually be shown in the manuscript. 

We thank the reviewer for this suggestion. We have now included the results related to PTE dynamics for successful vs. unsuccessful memory trials in the revised Results section as we note on page 12: 

“Differential information flow from the AI to the DMN and FPN for successfully recalled and forgotten memory trials 

We examined memory effects by comparing PTE between successfully recalled and forgotten memory trials. However, this analysis did not reveal differences in directed influence from the AI on the DMN and FPN or the reverse, between successfully recalled and forgotten memory trials during the encoding as well as recall periods in any of the memory experiments (all ps>0.05).”

(2.8) I believe the claims of causality through the use of the PTE are overstated throughout the manuscript and may contribute to further confusion in the literature regarding how causality in the brain can actually be understood. See Mehler and Kording, 2018 arXiv for an excellent discussion on the topic (https://arxiv.org/abs/1812.03363). My recommendation would be to significantly tone down claims that PTE reflects causal interactions in the brain. 

We thank the reviewer for this suggestion. We would like to clarify here that we define causality in our manuscript as follows: a brain region has a causal influence on a target if knowing the past history of temporal signals in both regions improves the ability to predict the target's signal in comparison to knowing only the target's past, as defined in earlier studies (Granger, 1969; Lobier et al., 2014). We have now included this clarification in the Introduction section (page 6).  

We also agree with the reviewer that to more mechanistically establish a causal link between the neural dynamics and behavior, lesion or brain stimulation studies are necessary. We have now acknowledged this in the revised Discussion as we note: “Although our computational methods suggest causal influences, direct causal manipulations, such as targeted brain stimulation during memory tasks, are needed to establish definitive causal relationships between network nodes.” (page 19). 

Finally, we have now significantly toned down our claims that PTE reflects causal interactions in the brain, in the Introduction, Results, and Discussion sections of our revised manuscript.  

(2.9) Relatedly, it may be useful for the authors to consider a supplemental analysis that uses classic measures of inter-regional synchronization, e.g. the PLV, and compare to their PTE findings. They cite literature to suggest a metric like the PTE may be useful, but this hardly rules out the potential utility of investigating narrowband phase synchronization. 

We thank the reviewer for this suggestion. We have now run new analyses based on PLV to examine phase synchronization between the AI and the DMN and FPN. However, we did not find a significant PLV for the interactions between the AI and DMN and FPN nodes for the different task periods compared to the resting baselines, as we note on page 13: 

“Narrowband phase synchronization between the AI and the DMN and FPN during encoding and recall compared to resting baseline  

We next directly compared the phase locking values (PLVs) (see Methods for details) between the AI and the PCC/precuneus and mPFC nodes of the DMN and also the dPPC and MFG nodes of the FPN for the encoding and the recall periods compared to resting baseline. However, narrowband PLV values did not significantly differ between the encoding/recall vs. rest periods, in any of the delta-theta (0.5-8 Hz), alpha (8-12 Hz), beta (12-30 Hz), gamma (30-80 Hz), and high-gamma (80-160 Hz) frequency bands. These results indicate that PTE, rather than phase synchronization, more robustly captures the AI dynamic interactions with the DMN and the FPN.” 

Please note that phase locking measures such as the PLV or coherence do not probe directed causal influences and cannot address how one region drives another. Instead, our study examined the direction of information flow between the AI and the DMN and FPN using robust estimators of the direction of information flow. PTE assesses with the ability of one time-series to predict future values of other time-series, thus estimating the time-delayed causal influences between the two time-series, whereas PLV or coherence can only estimate “instantaneous” phase synchronization, but not predict the future time-series. 

Additionally, please note that the directed information flow from the AI to both the DMN and FPN were enhanced during the encoding and recall periods compared to resting state across all four experiments, in a new set of analyses that we have carried out in our revised manuscript. Specifically, we have now carried out our task versus rest comparison by using resting baseline epochs before the start of the entire session of the task periods, rather than our previously used rest epochs which were in between the task periods. These new results have now been included in the revised Results as we note on page 12:  

“Enhanced information flow from the AI to the DMN and FPN during episodic memory processing, compared to resting-state baseline

We next examined whether directed information flow from the AI to the DMN and FPN nodes during the memory tasks differed from the resting-state baseline. Resting-state baselines were extracted immediately before the start of the task sessions and the duration of task and rest epochs were matched to ensure that differences in network dynamics could not be explained by differences in duration of the epochs. Directed information flow from the AI to both the DMN and FPN were higher during both the memory encoding and recall phases and across the four experiments, compared to baseline in all but two cases (Figures S6, S7). These findings provide strong evidence for enhanced role of AI directed information flow to the DMN and FPN during memory processing compared to the resting state.”  

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eLife assessment

In this manuscript, the authors present valuable findings on the apparent role of a salience-network anterior insula node in directing fronto-parietal and default-mode network activity within a tripartite network during control of memory, drawn from an impressive invasive human neurophysiological dataset. We commend the use of a large intracranial EEG dataset to approach this question. While many aspects of the evidence are solid, there are some remaining points which are methodologically incomplete and could be further improved with some specific control analyses and word changes.

Reviewer #1 (Public review):

Summary

Das and Menon describe an analysis of a large open-source iEEG dataset (UPENN-RAM). From encoding and recall phases of memory tasks, they analyzed power and phase-transfer entropy as a measure of directed information flow in regions across a hypothesized tripartite network system. The anterior insula (AI) was found to have heightened high gamma power during encoding and retrieval, which corresponded to suppression of high gamma power in medial prefrontal cortex (mPFC) and posterior cingulate cortex (PCC) during encoding but not recall. In contrast, directed information flow from (but not to) AI to mPFC and PCC is high during both time periods when PTE is analyzed with broadband but not narrowband activity. They claim that these findings significantly advance an understanding of how network communication facilitates cognitive operations during memory tasks, and that the AI of the salience network (SN) is responsible for influencing both the frontoparietal network (FPN) and default-mode network (DMN) during memory encoding and retrieval.

I find this question interesting and important, and agree with the authors that iEEG presents a unique opportunity to investigate the temporal dynamics within network nodes. Their findings convey intriguing information about the structure and order of communication between network regions during on-task cognition in general (though, perhaps not specific to memory - see Weaknesses), with the AI of the SN ostensibly playing an important role in possibly influencing the DMN and FPN.

Strengths

- The authors present results from an impressively sized iEEG sample. For reader context, this type of invasive human data is difficult and time-consuming to collect and many similar studies in high-level journals include 5-20 participants, typically not all of whom have electrodes in all regions of interest. It is excellent that they have been able to leverage open-source data in this way.<br /> - Preprocessing of iEEG data also seems sensible and appropriate based on field standards.<br /> - The authors tackle the replication issues inherent in much of the literature by replicating findings across task contexts, demonstrating that the principles of network communication evidenced by their results generalize in multiple task memory contexts. Again, the number of iEEG patients who have multiple tasks' worth of data is impressive.<br /> - Though the revised manuscript presents a broader and more novel investigation of the tripartite network's role in memory encoding and retrieval (as opposed to cognitive control of memory) the authors now thoroughly review the literature motivating this investigation of open-source data.

Weaknesses

- As the authors discuss, it is currently unclear if the directed information flow from AI to DMN and FPN nodes truly arises from memory-associated processes as opposed to more general attentional and cognitive demands, especially given that information flow does not relate meaningfully to task performance (whether memory retrieval is successful or not). I also note this is a concern because - though the authors have now demonstrated that information flow is increased compared to an off-task baseline - influences of AI on DMN or FPN were not increased relative to baseline epochs during the task in the original preprint version, again suggesting these effects may not be specific to the memory component of the analyzed tasks. The authors have thoughtfully noted in the Discussion several ways that experimental design can be improved in future studies to address this limitation.

Because phase-transfer entropy is referenced as a "causal" analysis in this investigation (PTE), I believe it is important to highlight for readers recent discussions surrounding the description of "causal mechanisms" in neuroscience (see "Confusion about causation" section from Ross and Bassett, 2024, Nature Neuroscience). A large proportion of neuroscientists (myself included) use "causal" only to refer to a mechanism whose modulation or removal (with direct manipulation, such as by lesion or stimulation) is known to change or control a given outcome (such as a successful behavior). As Ross and Bassett highlight, it is debatable whether such mechanistic causality is captured by Granger "causality" (a.k.a. Granger prediction) or the parametric PTE, and imprecise use of "causation" may be confusing. The authors have defined in the revised Introduction what their definition of "causality" is within the context of this investigation.

Reviewer #2 (Public review):

Based on reviewer feedback, Das and Menon have made several modifications to their manuscript, including a revised Introduction with a reframed motivation (now more oriented around the role of tripartite network in memory operations), new control analyses (as requested by Reviewers, including an updated and more appropriate baseline period and a control region, the IFG), an assessment of narrowband phase synchronization (as requested), as well as updates for clarity throughout the Methods section.

While I believe the authors have been responsive to reviewer feedback, and these modifications do enhance the manuscript, I have a few suggestions for how these new analyses could be made more statistically robust and better contextualized against the main findings of the manuscript. I continue to have some reservations about a tendency for their data to be overinterpreted, and for conclusions to be drawn more strongly than the data actually warrant.

(1) Clarifying the new control analyses. The authors have been responsive to our feedback and implemented several new analyses. The use of a pre-task baseline period and a control brain region (IFG) definitively help to contextualize their results, and the findings shown in the revision do suggest that (1) relative to a pre-task baseline, directed interactions from the AI are stronger and (2) relative to a nearby region, the IFG, the AI exhibits greater outward-directed influence.

However, it is difficult to draw strong quantitative conclusions from the analyses as presented, because they do not directly statistically contrast the effect in question (directed interactions with the FPN and DMN) between two conditions (e.g. during baseline vs. during memory encoding/retrieval). As I understand it, in their main figures the authors ask, "Is there statistically greater influence from the AI to the DMN/FPN in one direction versus another?" And in the AI they show greater "outward" PTE than "inward" PTE from other networks during encoding/retrieval. The balance of directed information favors an outward influence from the AI to DMN/FPN.

But in their new analyses, they simply show that the degree of "outward" PTE is greater during task relative to baseline in (almost) all tasks. I believe a more appropriately matched analysis would be to quantify the inward/outward balance during task states, quantify the inward/outward balance during rest states, and then directly statistically compare the two. It could be that the relative balance of directed information flow is non-significantly changed between task and rest states, which would be important to know.

Likewise, a similar principle applies to their IFG analysis. They show that the IFG tends to have an "inward" balance of influence from the DMN/FPN (the opposite of the AIs effect), but this does not directly answer whether the AI occupies a statistically unique position in terms of the magnitude of its influence on other regions. More appropriate, as I suggest above, would be to quantify the relative balance inward/outward influence, both for the IFG and the AI, and then directly compare those two quantities. (Given the inversion of the direction of effect, this is likely to be a significant result, but I think it deserves a careful approach regardless.)

(2) Consider additional control regions. The authors justify their choice of IFG as a control region very well. In my original comments, I perhaps should have been more clear that the most compelling control analyses here would be to subject every region of the brain outside these networks (with good coverage) to the same analysis, quantify the degree of inward/outward balance, and then see how the magnitude of the AI effect stacks up against all possible other options. If the assertion is that the AI plays a uniquely important role in these memory processes, showing how its influence stacks up against all possible "competitors" would be a very compelling demonstration of their argument.

(3) Reporting of successful vs. unsuccessful memory results. I apologize if I was not clear in my original comment (2.7, pg. 13 of the response document) regarding successful vs. unsuccessful memory. The fact that no significant difference was found in PTE between successful/unsuccessful memory is a very important finding that adds valuable context to the rest of the manuscript. I believe it deserves a figure, at least in the Supplement, so that readers can visualize the extent of the effect in successful/unsuccessful trials. This is especially important now that the manuscript has been reframed to focus more directly on claims regarding episodic memory processing; if that is indeed the focus, and their central analysis does not show a significant effect conditionalized on the success of memory encoding/retrieval, it is important that readers can see these data directly.

(4) Claims regarding causal relationships in the brain. I understand that the authors have defined "causal" in a specific way in the context of their manuscript; I do believe that as a matter of clear and transparent scientific communication, the authors nonetheless bear a responsibility to appreciate how this word may be erroneously interpreted/overinterpreted and I would urge further review of the manuscript to tone down claims of causality. Reflective of this, I was very surprised that even as both reviewers remarked on the need to use the word "causal" with extreme caution, the authors added it to the title in their revised manuscript.

eLife assessment

This study provides compelling data that defines the structure of the S. cerevisiae APC/C. The structure reveals overall conservation of its mechanism of action compared to the human APC/C but some important differences that indicate that activation by co-activator binding and phosphorylation are not identical to the human APC/C. Thus this study will be of considerable value to the field.

Reviewer #1 (Public Review):

Summary:

This work focuses on the structure and regulation of the Anaphase-Promoting Complex/Cyclosome (APC/C), a large multi-subunit ubiquitin ligase that controls the onset of chromosome segregation in mitosis. Previous high-resolution structural studies have uncovered numerous structural features and regulatory mechanisms of the human APC/C, but it has remained unclear if these mechanisms are conserved in other model eukaryotes. To address this gap in our understanding, the authors employed cryo-electron microscopy to generate structural models of APC/C from the budding yeast S. cerevisiae, a key model organism in cell cycle analysis. In their comparison of the human and yeast complexes, the authors uncover many conserved structural features that are documented here in detail, revealing widespread similarities in the fundamental structural features of the enzyme. Interestingly, the authors also find evidence that two of the key mechanisms of human APC/C regulation are not conserved in the yeast enzyme. Specifically:

(1) The ubiquitin ligase activity of the APC/C depends on its association with a co-activator subunit such as CDH1 or CDC20, which serves both as a substrate-binding adaptor and as an activator of interactions with the E2 co-enzyme. Previous studies of the human APC/C revealed that co-activator binding induces a conformational change that enables E2 binding. In contrast, the current work shows that this E2-binding conformation already exists in the absence of a co-activator in the yeast enzyme, suggesting that the enhancement of E2 binding in yeast depends on other, as yet undiscovered, mechanisms.

(2) APC/C phosphorylation on multiple subunits is known to enhance APC/C activation by the CDC20 co-activator in mitosis. Previous studies showed that phosphorylation acts by promoting the displacement of an autoinhibitory loop that occupies part of the CDC20-binding site. In the yeast enzyme, however, there is no autoinhibitory loop in the CDC20-binding site, and there is no apparent effect of APC/C phosphorylation on co-activator binding sites. Thus, phosphorylation activates the yeast CDC20-APC/C by unknown mechanisms.

Strengths:

The strength of this paper is that it provides a comprehensive analysis of yeast APC/C structure and how it compares to previously determined human structures. The article systematically unwraps the key features of the structure in a subunit-by-subunit fashion, carefully revealing the key features that are the same or different in the two species. These descriptions are based on a thorough overview of past work in the field; indeed, this article serves as a concise review of the key features, conserved or otherwise, of APC/C structure and regulation.

Weaknesses:

No significant weaknesses were identified.

Reviewer #2 (Public Review):

Summary:

This paper from the Barford lab describes medium/high-resolution cryo-EM structures of three versions of the S. cerevisiae anaphase-promoting complex/cyclosome (APC/C):

(1) the recombinant apo complex purified from insect cells,

(2) the apo complex phosphorylated in vitro by cyclin-dependent kinase, and

(3) an active APC/C-Cdh1-substrate ternary complex.

The focus of the paper is on comparing similarities and differences between S. cerevisiae and human APC/C structures, mechanisms of activation by coactivator, and regulation by phosphorylation. The authors find that the overall structures of S. cerevisiae and human APC/C are remarkably similar, including the binding sites and orientation for the substrate-recruiting coactivator, Cdh1. In addition, the mechanism of Cdh1 inhibition by phosphorylation appears conserved across kingdoms. However, key differences were also observed that reveal divergence in APC/C mechanisms that are important for researchers in this field to know. Specifically, the mechanism of APC/C-Cdc20 activation by mitotic phosphorylation appears to be different, due to the absence of the key Apc1 autoinhibition loop in the S. cerevisiae complex. In addition, the conformational activation of human APC/C by coactivator binding was not observed in the S. cerevisiae complex, implying that stimulation of E2 binding must occur via a different mechanism in this species.

Strengths:

Consistent with the numerous prior cryo-EM structures of human APC/C from the Barford lab, the technical quality of the structure models is a major strength of this work. In addition, the detailed comparison of similarities and differences between the two species will be a very valuable resource for the scientific community. The manuscript is written very well and allows readers lacking expertise in cryo-EM to understand the important aspects of the conservation of APC/C structure and mechanism across kingdoms.

Weaknesses:

The lack of experimentation in this work to test some of the putative differences in APC/C mechanism (e.g. stimulation of E2 binding by coactivator and stimulation of activity by mitotic phosphorylation) could be considered a weakness. Nonetheless, the authors do a nice job explaining how the structure interpretations imply these differences likely exist, and this work sets the stage nicely for future studies to understand these differences at a mechanistic level. There is enough value in having the S. cerevisiae structure models and the comparison to the human structures, without any additional experimentation.

The validation of APC/C phosphorylation in the unphosphorylated and hyperphosphorylated states is not very robust. Given the lack of significant effects of phosphorylation on APC/C structure observed here (compared to the human complex), this becomes important. A list of phosphorylation sites identified by mass spec before and after in vitro phosphorylation is provided but lacks quantitative information. This list indicates that a significant number of phosphorylation sites are detected in the purified APC/C prior to reaction with purified kinases. Many more sites are detected after in vitro kinase reaction, but it isn't clear how extensively any of the sites are modified. There is reason for caution then, in accepting the conclusions that structures of unphosphorylated and hyperphosphorylated APC/C from S. cerevisiae are nearly identical.

Reviewer #3 (Public Review):

Vazquez-Fernandez et al. present a comprehensive and detailed analysis of the S. cerevisiae APC/C complex, providing new insights into its structure and function. The authors determined the medium-resolution structures of three recombinant S. cerevisiae APC/C complexes, including unphosphorylated apo-APC/C (4.9 Å), the ternary APC/CCDH1-substrate complex (APC/CCDH1:Hsl1 , 4.0 Å), and phosphorylated apo-APC/C (4.4 Å). Prior structures of human, E. cuniculi, S. cerevisiae, and S. pombe APC/C subunits, as well as AlphaFold2 predictions were used to guide model building. Although the determined structures are not sufficient to fully explain the molecular mechanism of APC/C activation and regulation in S. cerevisiae, they provide valuable insights into the similarities and differences with the human complex, shedding light on the conserved and divergent features of APC/C function.

The manuscript synthesizes the structural analysis of the APC/C complex in S. cerevisiae, with literature into a cohesive and clear picture of the complex's structure and function. It is well-written and clear, making the complex biology of the APC/C complex accessible to a wide range of readers. The complex forms a triangular shape, with a central cavity surrounded by two modules: the TPR lobe and the platform module. The TPR lobe consists of three TPR proteins (APC3, APC6, and APC8), which stack on top of each other to form a quasi-symmetric structure. The platform module is composed of the large APC1 subunit, together with APC4 and APC5. The authors also analyzed the structure of several smaller subunits that are involved in regulating the activity of the APC/C complex and showed their structural similarities to and discrepancies from their human counterparts. These subunits, including CDC26/APC12, SWM1/APC13, APC9, and MND2/APC15, form extended, irregular structures that simultaneously contact multiple large globular APC/C subunits.

While the authors report the similarity between the overall structure of S. cerevisiae and human APC/C complexes, they also found two unexpected differences. First, in the S. cerevisiae apo-complex, the E2 binding site on APC11RING is accessible, whereas, in humans, it requires CDH1 binding. Second, a structural element similar to the human APC1 auto-inhibitory segment is missing in S. cerevisiae. In humans, the phosphorylation-dependent displacement of this segment allows CDC20 binding to APC/C. In S. cerevisiae, the binding requires phosphorylation however the structures reported here are suggestive that this could involve a different (presently unknown) mechanism. These structural insights highlight the importance of understanding the species-specific features of APC/C function.

Strengths:

The manuscript does a great job of revealing new structures.

Opportunity for increasing impact: It would have been nice if some functional differences were demonstrated, for example regarding the mechanism of CDC20 binding, and the comparison between apo-APC/C and ternary APC/CCDH1:Hsl1 does not explain the molecular activation mechanism of S. cerevisiae APC/C. Nonetheless, the authors nicely integrate their data with well-established literature on the similarities and differences between yeast and human systems.

Author response:

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

Reviewer #1 (Recommendations For The Authors):

(1) The introduction includes the following sentence: "CDH1 interacts with the APC/C during G1 and S-phase. On entering mitosis, CDK and polo kinases phosphorylate the APC/C and CDH1 to effect switching to CDC20." In fact, CDH1 is inactivated from late G1 to mid-mitosis as a result of phosphorylation by G1/S, S phase, and mitotic Cdk-cyclin complexes. Phosphorylation of the APC/C, not inactivation of CDH1, enables the switch to CDC20. 

Thank you for this. We have corrected the text and include the Zachariae et al (1998) reference.

(2) Supplementary Table 1 provides a long list of APC/C sites phosphorylated in vitro by Cdk2-cyclin A-Cks2 and Plk1 (note that the main text states only Cdk2-cyclin A). It seems likely that the high amount of kinase in these reactions has led to minor levels of phosphorylation at many of these sites. Although I realize that these results are peripheral to the central findings of the paper, it would be helpful to see confidence scores or other evidence of significance for the indicated phosphopeptides. Perhaps the Cdk consensus sites could be marked on the table in some way, and a description of the MS methods could be provided in the Methods section. 

We have implemented this useful suggestion to highlight the Cdk consensus sites. Unfortunately we don’t have confidence scores of significance of the indicated phosphopeptides.

Reviewer #2 (Recommendations For The Authors): 

(1) My only real concern is with the phosphorylated APC/C structure. The authors provide a table that lists a bunch of phosphorylation sites detected before and after in vitro phosphorylation by purified kinases, and in the purified protein gels, some mobility shifts that would be consistent with significant phosphorylation are observed for some of the subunits. However, the mass spec data are non-quantitative. It would be more useful to provide estimated stoichiometries for the various phosphorylation sites to help support the expectation that the complex is heavily phosphorylated and that the structure presented actually represents hyperphosphorylated APC/C. No evidence of phosphorylated amino acids is noted in the cryo-EM structures, presumably because resolution is not high enough and/or there is too much flexibility in these areas. Given that hyperphosphorylation does not affect enzymatic activity and has very little impact on the complex structure, it seems important to provide readers with additional confidence that the complex is indeed heavily phosphorylated and that the complex isolated from insect cells is not heavily phosphorylated. Since the complex is purified from a eukaryotic expression system it seems formally possible that key phosphorylation sites could already be present due to the activity of endogenous Cdk or other kinases in insect cells and, indeed, quite a few sites are noted to exist even without in vitro phosphorylation. Providing stoichiometry of these sites might help address the likelihood that key regulatory sites are already occupied upon purification. It might at least be worth addressing this in the text. 

The suggestion to comment on the level of phosphorylation of the ‘unphosphorylated’ and Cdk-treated ‘phosphorylated’ APC/C is an excellent idea. The text has been modified on page 9 to include such a discussion. Unfortunately we don’t have quantification of the stoichiometry of the phospho-sites.

(2) On a minor note, in the results text the authors mention that cyclin A-Cdk2 is used for in vitro phosphorylation, but in the methods, it states both cyclin A-Cdk2 and Plk1 are used. This should be edited for consistency. 

Thank you for noticing this. Now corrected.

(3) Another minor issue - the authors state in the introduction (third paragraph) that "CDH1 interacts with the APC/C during G1 and S-phase". Actually, Cdh1 becomes phosphorylated and APC/CCdh1 inactivated at S-phase onset, both in S. cerevisiae and humans. In fact, phosphorylation of Cdh1 is an important driver of the irreversible transition from G1 to S-phase. This statement should be corrected. 

Thank you for noticing this. This error has been corrected and include the Zachariae et al (1998) reference.

Reviewer #3 (Recommendations For The Authors):

To be addressed in a revised manuscript: 

(1) The authors should cite and discuss Cole Ferguson et al., Mol Cell 2022. This study describes the loss of APC7 in a human disease and provides a detailed structural and biochemical examination of the effects of APC7 loss on human APC/C. Given that much of our understanding of APC7 comes from this work, it should be highlighted in the introduction and discussed in depth in light of the new work on S. cerevisiae APC/C. 

Thank you for mentioning this interesting paper. We discuss its main findings in the ‘Discussion’. Given the paper shows that deletion of APC7 has no discernible effect on the stability of human APC/C, we have deleted the discussion that APC7 stabilises human APC/C analogous to the stabilisation conferred on S. cerevisiae APC/C by APC9.

(2) There are multiple cases in the manuscript where the text was referring to the human complex but APC/CCdh1:Hsl1 was written, including labeling of Figure 4b. It would be useful to consider nomenclature considering that Hsl1 is a yeast protein. 

Thank you for noticing this. We mistakenly wrote ‘Hsl1’ instead of ‘Emi1’. Now corrected.

(3) The authors should tone down claims regarding their discoveries absence of APC7 in S. cerevisiae. The absence of APC7 has been known for nearly two decades and the authors confirm this {Pan et al.l 2007, Journal of Cell Science) and then show the structure. 

We agree with this as explained in response to point 1.

(4) On page 7, the authors are writing about the four helices mediating the APC/C-CDH1 interactions but list only 3. 

We have revised the sentence to clarify this point.

eLife assessment

In this useful study, the authors investigate the regulatory mechanisms related to toxin production and pathogenicity in Aspergillus flavus. Their observations indicate that the SntB protein regulates morphogenesis, aflatoxin biosynthesis, and the oxidative stress response. The data supporting the conclusions are compelling and contribute significantly the advancing the understanding of SntB function.

Reviewer #1 (Public Review):

The study identifies the epigenetic reader SntB as a crucial transcriptional regulator of growth, development, and secondary metabolite synthesis in Aspergillus flavus, although the precise molecular mechanisms remain elusive. Using homologous recombination, researchers constructed sntB gene deletion (ΔsntB), complementary (Com-sntB), and HA tag-fused sntB (sntB-HA) strains. Results indicated that deletion of the sntB gene impaired mycelial growth, conidial production, sclerotia formation, aflatoxin synthesis, and host colonization compared to the wild type (WT). The defects in the ΔsntB strain were reversible in the Com-sntB strain.

Further experiments involving ChIP-seq and RNA-seq analyses of sntB-HA and WT, as well as ΔsntB and WT strains, highlighted SntB's significant role in the oxidative stress response. Analysis of the catalase-encoding catC gene, which was upregulated in the ΔsntB strain, and a secretory lipase gene, which was downregulated, underpinned the functional disruptions observed. Under oxidative stress induced by menadione sodium bisulfite (MSB), the deletion of sntB reduced catC expression significantly. Additionally, deleting the catC gene curtailed mycelial growth, conidial production, and sclerotia formation, but elevated reactive oxygen species (ROS) levels and aflatoxin production. The ΔcatC strain also showed reduced susceptibility to MSB and decreased aflatoxin production compared to the WT.

This study outlines a pathway by which SntB regulates fungal morphogenesis, mycotoxin synthesis, and virulence through a sequence of H3K36me3 modification to peroxisomes and lipid hydrolysis, impacting fungal virulence and mycotoxin biosynthesis.

The authors have achieved the majority of their aims at the beginning of the study, finding target genes, which led to catC mediated regulation of development, growth and aflatoxin metabolism. Overall most parts of the study are solid and clear.

Comments on revision:

The authors have thoroughly addressed all the concerns I raised. The current manuscript is robust and effectively presents evidence supporting its claims. The overall quality of the manuscript has significantly improved.

Reviewer #2 (Public Review):

The authors fully addressed my concerns and made appropriate changes in the manuscript. The quality of the manuscript is now significantly improved.

Author response:

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

Thank you for your careful reviews of our manuscript. This revision is mainly aimed at addressing some minor errors in the text, English writing, grammar, etc. The details are as follows:

(1) We added the information for the sntB-HA strain in table 1.

(2) We added the primer information for the construction of sntB-HA strain in table 2.

(3) Some errors in English writing, grammar. Please see the revised manuscript with markers.

Reviewer #1 (Public review):

Summary:

The study used root tips from semi-hydroponic tea seedlings. The strategy followed sequential steps to draw partial conclusions.

Initially, protoplasts obtained from root tips were processed for scRNA-seq using the 10x Genomics platform. The sequencing data underwent pre-filtering at cell and gene levels, leading to 10,435 cells. These cells were then classified into eight clusters using t-SNE algorithms. The present study scrutinised cell typification through protein sequence similarity analysis of homologs of cell type marker genes. The analysis was conducted to ensure accuracy using validated genes from previous scRNA-seq studies and the model plant Arabidopsis thaliana. The cluster cell annotation was confirmed using in situ RT-PCR analyses. This methodology provided a comprehensive insight into the cellular differentiation of the sample under study. The identified clusters, spanning 1 to 8, have been accurately classified as xylem, epidermal, stem cell niche, cortex/endodermal, root cap, cambium, phloem, and pericycle cells.

Then, the authors performed a pseudo-time analysis to validate the cell cluster annotation by examining the differentiation pathways of the root cells. Lastly, they created a differentiation heatmap from the xylem and epidermal cells and identified the biological functions associated with the highly expressed genes.

Upon thoroughly analysing the scRNA-seq data, the researchers delved into the cell heterogeneity of nitrate and ammonium uptake, transport, and nitrogen assimilation into amino acids. The scRNA-seq data was validated by in situ RT-PCR. It allows the localisation of glutamate and alanine biosynthetic enzymes along the cell clusters and confirms that both constituent the primary amino acid metabolism in the root. Such investigation was deemed necessary due to the paramount importance of these processes in theanine biosynthesis since this molecule is synthesised from glutamate and alanine-derived ethylamine.

Afterwards, the authors analysed the cell-specific expression patterns of the theanine biosynthesis genes, combining the same molecular tools. They concluded that theanine biosynthesis is more enriched in cluster 8 "pericycle cells" than glutamate biosynthesis (Lines 271-272). However, the statement made in Line 250 states that the highest expression levels of genes responsible for glutamate biosynthesis were observed in Clusters 1, 3, 4, 6 and 8, leading to an unclear conclusion.<br /> The regulation of theanine biosynthesis by the MYB transcription factor family is well-established. In particular, CsMYB6, a transcription factor expressed specifically in roots, has been found to promote theanine biosynthesis by binding to the promoter of the TSI gene responsible for theanine synthesis. However, their findings indicate that CsMYB6 expression is present in Cluster 3 (SCN), Cluster 6 (cambium cells), and Cluster 1 (xylem cells) but not in Cluster 8 (pericycle cells), which is known for its high expression of CsTSI. Similarly, their scRNA-seq data indicated that CsMYB40 and CsHHO3, which activate and repress CsAlaDC expression, respectively, did not show high expression in Cluster 1 (the cell cluster with high CsAlaDC expression). Based on these findings, the authors speculated that transcription factors and target genes are not necessarily always highly expressed in the same cells.

Lastly, the authors have discovered a novel transcription factor belonging to the Lateral Organ Boundaries Domain (LBD) family known as CsLBD37 that can co-regulate the synthesis of theanine and the development of lateral roots. The authors observed that CsLBD37 is located within the nucleus and can repress the CsAlaDC promoter's activity. To investigate this mechanism further, the authors conducted experiments to determine whether CsLBD37 can inhibit CsAlaDC expression in vivo. They achieved this by creating transiently CsLBD37-silenced or over-expression tea seedlings through antisense oligonucleotide interference and generation of transgenic hairy roots. Based on their findings, the authors theorise that CsLBD37 regulates CsAlaDC expression to modulate the synthesis of ethylamine and theanine in tea roots. Apologies for the inadvertent mistake concerning glutamate and glutamine.

Strength:

The manuscript showcases significant dedication and hard work, resulting in valuable insights that are fundamental for generating knowledge. The authors skillfully integrated various tools available for this type of study and meticulously presented and illustrated every step involved in the survey. The overall quality of the work is exceptional, and it would be a valuable addition to any academic or professional setting.

Weaknesses:

The authors have effectively addressed the feedback and revised the manuscript, presenting their debatable conclusions as speculative. Consequently, I find the manuscript's current form free of any apparent weaknesses.

Reviewer #2 (Public review):

Summary:

In their manuscript, Lin et al. present a comprehensive single-cell analysis of tea plant roots. They measured the transcriptomes of 10,435 cells from tea plant root tips, leading to the identification and annotation of 8 distinct cell clusters using marker genes. Through this dataset, they delved into the cell-type-specific expression profiles of genes crucial for the biosynthesis, transport, and storage of theanine, revealing potential multicellular compartmentalization in theanine biosynthesis pathways. Furthermore, their findings highlight CsLBD37 as a novel transcription factor with dual regulatory roles in both theanine biosynthesis and lateral root development.

Strengths:

This manuscript provides the first single-cell dataset analysis of roots of the tea plants. It also enables detailed analysis of the specific expression patterns of the gene involved in theanine biosynthesis. Some of these gene expression patterns in roots were further validated through in-situ RT-PCR. Additionally, a novel TF gene CsLBD37's role in regulating theanine biosynthesis was identified through their analysis.

Weaknesses:

The revised manuscript has addressed the concerns raised during the initial review.

Reviewer #3 (Public review):

Summary:

Lin et al., performed a scRNA-seq-based study of tea roots, as an example, to elucidate the biosynthesis and regulatory processes for theanine, a root-specific secondary metabolite, and established the first map of tea roots comprised of 8 cell clusters. Their findings contribute to deepening our understanding of the regulation of the synthesis of important flavor substances in tea plant roots. They have presented some innovative ideas.

Comment on revised version:

The reviewer has addressed all my concerns and I have no further comments.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The study used root tips from semi-hydroponic tea seedlings. The strategy followed sequential steps to draw partial conclusions.

Initially, protoplasts obtained from root tips were processed for scRNA-seq using the 10x Genomics platform. The sequencing data underwent pre-filtering at both the cell and gene levels, leading to 10,435 cells. These cells were then classified into eight clusters using t-SNE algorithms. The present study scrutinised cell typification through protein sequence similarity analysis of homologs of cell type marker genes. The analysis was conducted to ensure accuracy using validated genes from previous scRNA-seq studies and the model plant Arabidopsis thaliana. The cluster cell annotation was confirmed using in situ RT-PCR analyses. This methodology provided a comprehensive insight into the cellular differentiation of the sample under study. The identified clusters, spanning 1 to 8, have been accurately classified as xylem, epidermal, stem cell niche, cortex/endodermal, root cap, cambium, phloem, and pericycle cells.

Then, the authors performed a pseudo-time analysis to validate the cell cluster annotation by examining the differentiation pathways of the root cells. Lastly, they created a differentiation heatmap from the xylem and epidermal cells and identified the biological functions associated with the highly expressed genes.

Upon thoroughly analysing the scRNA-seq data, the researchers delved into the cell heterogeneity of nitrate and ammonium uptake, transport, and nitrogen assimilation into amino acids. The scRNA-seq data was validated by in situ RT-PCR. It allows the localisation of glutamine and alanine biosynthetic enzymes along the cell clusters and confirms that both constituent the primary amino acid metabolism in the root. Such investigation was deemed necessary due to the paramount importance of these processes in theanine biosynthesis since this molecule is synthesised from glutamine and alanine-derived ethylamine.

Afterwards, the authors analysed the cell-specific expression patterns of the theanine biosynthesis genes, combining the same molecular tools. They concluded that theanine biosynthesis is more enriched in cluster 8 "pericycle cells" than glutamine biosynthesis (Lines 271-272). However, the statement made in Line 250 states that the highest expression levels of genes responsible for glutamine biosynthesis were observed in Clusters 1, 3, 4, 6, and 8, leading to an unclear conclusion.

Thank you for your interest in and feedback on the paper. We have made revisions to the manuscript as per your suggestions. We would like to emphasize that the precursors of theanine biosynthesis are alanine-derived ethylamine and glutamate, not glutamine. Furthermore, in terms of the intermediates, only ethylamine is specific to the theanine biosynthetic pathway, as glutamate is the primary product of nitrogen assimilation and serves as a precursor for the biosynthesis of amino acids, proteins, chlorophyll, and many secondary metabolites.

In this study, we observed a high expression of genes encoding enzymes involved in the glutamate biosynthetic pathway (CsGOGATs and CsGDHs) across all 8 clusters, with particularly strong expression in cluster 1, 3, 4, 6, and 8 (Figure 4D and 5B). However, the gene encoding CsTHSI responsible for catalyzing theanine biosynthesis from glutamate and ethylamine was determined to be more enriched in cluster 8 (Figure 5B and 5C). Therefore, we concluded that theanine biosynthesis was more enriched in cluster 8, whereas glutamate biosynthesis was more broadly active in clusters 1, 3, 4, 6 and 8.

The regulation of theanine biosynthesis by the MYB transcription factor family is well-established. In particular, CsMYB6, a transcription factor expressed specifically in roots, has been  to promote theanine biosynthesis by binding to the promoter of the TSI gene responsible for theanine synthesis. However, their findings indicate that CsMYB6 expression is present in Cluster 3 (SCN), Cluster 6 (cambium cells), and Cluster 1 (xylem cells) but not in Cluster 8 (pericycle cells), which is known for its high expression of CsTSI. Similarly, their scRNA-seq data indicated that CsMYB40 and CsHHO3, which activate and repress CsAlaDC expression, respectively, did not show high expression in Cluster 1 (the cell cluster with high CsAlaDC expression). Based on these findings, the authors hypothesised that transcription factors and target genes are not necessarily always highly expressed in the same cells. Nonetheless, additional evidence is essential to substantiate this presumption.

Thank you for your advice. We fully agree that additional evidence is essential to support the presumption that transcription factors and target genes are not always highly expressed in the same cells. Therefore, in this study, we identified another transcription factor, CsLBD37, which was characterized to negatively regulate CsAlaDC expression in response to nitrogen levels. Consistent with our presumption, the expression of CsLBD37 was not enriched in cluster 1, where the expression of CsAlaDC was primarily enriched (Figure 5B and 6D; Line 365).

To further identify supporting evidence, we also analyzed the expression of some transcription factors and their target genes in the model plant Arabidopsis, using published single cell RNA-seq data (Ryu et al., 2019; Wendrich et al., 2020; Zhang et al., 2019; Denyer et al., 2019; Jean-Baptiste et al. 2019; Shulse et al., 2019; Shahan et al., 2022) and database (Root Cell Atlas, https://rootcellatlas.org/; BAR, https://bar.utoronto.ca/#GeneExpressionAndProteinTools). Similar to the situation in tea plants, the regulators were not exactly the same as the cell types in which their target genes were highly expressed. For example, AtARF7 and AtARF19 were highly expressed in the cortex and stele, respectively, whereas their target genes AtLBD16 and AtLBD29 were highly expressed in endodermal cells (Okushima et al.,2007; Supplemental figure 8B and 8C; Line 312-325 and Line 525-526); AtPHR1 was highly expressed in root epidermal cells and pericyte cells, but its target gene AtF3’H was highly expressed in the cortex and AtRALF23 was highly expressed in xylem cells (Liu et al., 2022; Tang et al., 2022; Supplemental figure 8B and 8C; Line 322-327 and Line 527-530).

At the same time, we discussed that we cannot rule out the possibility of transcription factors regulating their target genes in the same cell type and both being highly expressed. One of the reasons is that these theanine-associated genes are promiscuous, having many target genes and regulate multiple biological processes in tea plants. We have only shown that high expression in the same cell type is not a necessary condition (Line 534-554). We strongly agree with the reviewer's opinion that more evidence is needed to illustrate this model in the future.

Reference:

Denyer, T. et al. (2019). Spatiotemporal developmental trajectories in the arabidopsis root revealed using high-throughput single-cell RNA sequencing. Dev Cell. 48:840-852.e5.

Liu, Z. et al. (2022). PHR1 positively regulates phosphate starvation-induced anthocyanin accumulation through direct upregulation of genes F3'H and LDOX in Arabidopsis. Planta. 256:42.

Okushima, Y. et al. (2007). ARF7 and ARF19 regulate lateral root formation via direct activation of LBD/ASL genes in Arabidopsis. Plant Cell. 19:118-30.

Ryu, K. H., Huang, L., Kang, H. M. & Schiefelbein, J. (2019). Single-cell RNA sequencing resolves molecular relationships among individual plant cells. Plant Physiol. 179:1444-1456.

Shahan, R. et al. (2022). A single-cell Arabidopsis root atlas reveals developmental trajectories in wild-type and cell identity mutants. Dev Cell. 57:543-560.e9.

Shulse, C. et al. (2019). High-throughput single-cell transcriptome profiling of plant cell types. Cell Rep. 27:2241-2247.e4.

Tang, J. et al. (2022). Plant immunity suppression via PHR1-RALF-FERONIA shapes the root microbiome to alleviate phosphate starvation. EMBO J. 41:e109102.

Wendrich, J.R., et al. (2020). Vascular transcription factors guide plant epidermal responses to limiting phosphate conditions. Science. 370:eaay4970.

Zhang, T. et al. (2019). A single-cell RNA sequencing profiles the developmental landscape of arabidopsis root. Mol Plant. 12:648-660.

Lastly, the authors have discovered a novel transcription factor belonging to the Lateral Organ Boundaries Domain (LBD) family known as CsLBD37 that can co-regulate the synthesis of theanine and the development of lateral roots. The authors observed that CsLBD37 is located within the nucleus and can repress the CsAlaDC promoter's activity. To investigate this mechanism further, the authors conducted experiments to determine whether CsLBD37 can inhibit CsAlaDC expression in vivo. They achieved this by creating transiently CsLBD37-silenced or over-expression tea seedlings through antisense oligonucleotide interference and generation of transgenic hairy roots. Based on their findings, the authors hypothesise that CsLBD37 regulates CsAlaDC expression to modulate the synthesis of ethylamine and theanine.

Additionally, the available literature suggests that the transcription factors belonging to the Lateral Organ Boundaries Domain (LBD) family play a crucial role in regulating the development of lateral roots and secondary root growth. Considering this, they confirmed that pericycle cells exhibit a higher expression of CsLBD37. A recent experiment revealed that overexpression of CsLBD37 in transgenic Arabidopsis thaliana plants led to fewer lateral roots than the wild type. From this observation, the researchers concluded that CsLBD37 regulates lateral root development in tea plants. I respectfully submit that the current conclusion may require additional research before it can be considered definitive.

Further efforts should be made to investigate the signalling mechanisms that govern CsLBD37 expression to arrive at a more comprehensive understanding of this process. In the context of Arabidopsis lateral root founder cells, the establishment of asymmetry is regulated by LBD16/ASL18 and other related LBD/ASL proteins, as well as the AUXIN RESPONSE FACTORs (ARF7 and ARF19). This is achieved by activating plant-specific transcriptional regulators such as LBD16/ASL18 (Go et al., 2012, https://doi.org/10.1242/dev.071928). On the other hand, other downstream homologues of LBD genes regulated by cytokinin signalling play a role in secondary root growth (Ye et al., 2021, https://doi.org/10.1016/j.cub.2021.05.036). It is imperative to shed light on the hormonal regulation of CsLBD37 expression in order to gain a comprehensive understanding of its involvement in the morphogenic process.

We are very grateful for your valuable suggestions and we fully agree with you. In an earlier study, we also observed a link between theanine metabolism, hormone metabolism and root development (Chen et al., 2022), but there is still insufficient evidence to fully characterize these links. In the current study, the focus was on the cell-specific theanine biosynthesis, transport and regulation, and we identified that CsLBD37 negatively regulates theanine biosynthesis. However, the upstream regulatory mechanism of CsLBD37 has not been addressed in this study. It is a pertinent question for future investigation as to how CsLBD37 is regulated in root development. We have included the following additional discussion in the revised manuscript: “Besides, it has been reported that LBD family TFs were regulated by, or interacted with, regulators of hormone pathways (e.g., ARFs) to regulate the process of root morphogenesis (Goh et al., 2012; Ye et al., 2021). Based on these findings, we speculated that CsLBD37 is likely regulated by, or interacts with, other proteins to form a complex to regulate root development or theanine biosynthesis.” (Line 573-576). At the same time, we revised the text “These results provided support for a model in which CsLBD37 plays a role in regulating lateral root development in tea plants” to “These findings suggested that CsLBD37 may play a role in regulating lateral root development in tea plant roots” (Line 401-402).

Reference:

Chen, T. et al. (2022). Theanine, a tea plant specific non-proteinogenic amino acid, is involved in the regulation of lateral root development in response to nitrogen status. Hortic. Res. 10:uhac267.

Goh, T., Joi, S., Mimura, T. & Fukaki, H. (2012). The establishment of asymmetry in Arabidopsis lateral root founder cells is regulated by LBD16/ASL18 and related LBD/ASL proteins. Development 139:883-893.

Ye, L. et al. (2021). Cytokinins initiate secondary growth in the Arabidopsis root through a set of LBD genes. Curr. Biol. 31:3365-3373.e3367.

Strength:

The manuscript showcases significant dedication and hard work, resulting in valuable insights that serve as a fundamental basis for generating knowledge. The authors skillfully integrated various tools available for this type of study and meticulously presented and illustrated every step involved in the survey. The overall quality of the work is exceptional, and it would be a valuable addition to any academic or professional setting.

Weaknesses:

In its current form, the article presents certain weaknesses that need to be addressed to improve its overall quality. Specifically, the authors' conclusions appear to have been drawn in haste without sufficient experimental data and a comprehensive discussion of the entire plant. It is strongly advised that the authors devote additional effort to resolving the abovementioned issues to bolster the article's credibility and dependability. This will ensure that the article is of the highest quality, providing readers with reliable and trustworthy information.

Thank you for your feedback. We acknowledge that our experiments and data require further improvement. Currently, the genetic transformation of the tea plant remains a challenge, making it difficult to obtain sufficient in vivo evidence. Despite this situation, we have made every effort to obtain support for our conclusions based on the current situation and available technology. Indeed, additional studies will be performed once the impediment associated with genetic transformation of the tea plant has been resolved.

Reviewer #2 (Public Review):

Summary:

In their manuscript, Lin et al. present a comprehensive single-cell analysis of tea plant roots. They measured the transcriptomes of 10,435 cells from tea plant root tips, leading to the identification and annotation of 8 distinct cell clusters using marker genes. Through this dataset, they delved into the cell-type-specific expression profiles of genes crucial for the biosynthesis, transport, and storage of theanine, revealing potential multicellular compartmentalization in theanine biosynthesis pathways. Furthermore, their findings highlight CsLBD37 as a novel transcription factor with dual regulatory roles in both theanine biosynthesis and lateral root development.

Strengths:

This manuscript provides the first single-cell dataset analysis of roots of the tea plants. It also enables detailed analysis of the specific expression patterns of the gene involved in theanine biosynthesis. Some of these gene expression patterns in roots were further validated through in-situ RT-PCR. Additionally, a novel TF gene CsLBD37's role in regulating theanine biosynthesis was identified through their analysis.

Weaknesses:

Several issues need to be addressed:<br /> (1) The annotation of single-cell clusters (1-8) in Figure 2 could benefit from further improvement. Currently, the authors utilize several key genes, such as CsAAP1, CsLHW, CsWAT1, CsIRX9, CsWOX5, CsGL3, and CsSCR, to annotate cell types. However, it is notable that some of these genes are expressed in only a limited number of cells within their respective clusters, such as CsAAP1, CsLHW, CsGL3, CsIRX9, and CsWOX5. It would be advisable to utilize other marker genes expressed in a higher percentage of cells or employ a combination of multiple marker genes for more accurate annotation.

Thank you for your comments. In this study, we first utilized classical marker genes, such as CsWAT1 and CsPP2, to annotate cell types. The expression patterns of these marker genes were confirmed using in situ RT-PCR. Additionally, a combination of multiple marker genes was employed for cell type annotation. We also analyzed the top 10 cluster-enriched genes, in each cluster, and their homologous expression in Arabidopsis, populus, etc., to serve as a reference for cluster annotation (Figure 2D; Supplemental Figures 2-6; Supplemental data 3). Subsequently, differentiation trajectories of root cells were analyzed based on pseudo-time analyses, which aligned well with cell type annotation and further supported the reliability of our annotations through these combined methods.

(2) Figure 3 could enhance clarity by displaying the trajectory of cell differentiation atop the UMAP, similar to the examples demonstrated by Monocle 3.

Thanks for this advice. We have supplied the trajectory of cell differentiation atop the UMAP in the revised supplemental figure 7 (Line 185).

(3) The identification of CsLBD37 primarily relies on bulk RNA-seq data. The manuscript could benefit from elaborating on the role of the single-cell dataset in this context.

Thanks for your comments. In this study, we determined that CsTSI was highly expressed in cluster 8, but its regulator CsMYB6 was highly expressed in cluster 3, cluster 6 and cluster 1 (Line 301-304). Thus, target genes and their regulators seem not to always be highly expressed in the same cell cluster. A similar situation was also observed in terms of CsAlaDC transcriptional regulation (Line 305-311). Based on these findings, we hypothesized that, for the regulation of theanine biosynthesis, it is not necessary for transcription factors and target genes to always be highly expressed in the same cells. Thus, taking the transcriptional regulation of CsAlaDC as an example, we next analyzed the TFs that were co-expressed with CsAlaDC to test this notion. We used scRNA-seq data to screen for genes that were not highly co-expressed with CsAlaDC, such as CsLBD37, to test our hypothesis (Line 338-340 and Line 365).

(4) The manuscript's conclusions predominantly rely on the expression patterns of key genes. This reliance might stem from the inherent challenges of tea research, which often faces limitations in exploring molecular mechanisms due to the lack of suitable genetic and molecular methods. The authors may consider discussing this point further in the discussion section.

Thanks for your suggestions and we totally agree. We discussed this point in the discussion section, “In some non-model plants, including tea, transgenic technologies are not currently available and, hence, we used in situ RNA hybridization to establish the location(s) for gene expression. In some studies, isolation of different cell types was combined with q-RT-PCR to detect cell-type marker gene expression (Wang et al., 2022). However, this approach has two limitations in that it cannot display the gene location directly and has only low resolution”, “After numerous trials, we were able to optimize in situ RT-PCR assays (detailed in the Methods), which enabled a cell-specific characterization of gene expression in tea plant root cells, prior to establishing a genetic transformation system for tea…we note the challenge associated with weak calling of homologous marker genes…” (Line 431-444).

Reviewer #3 (Public Review):

Summary:

Lin et al., performed a scRNA-seq-based study of tea roots, as an example, to elucidate the biosynthesis and regulatory processes for theanine, a root-specific secondary metabolite, and established the first map of tea roots comprised of 8 cell clusters. Their findings contribute to deepening our understanding of the regulation of the synthesis of important flavor substances in tea plant roots. They have presented some innovative ideas.

It is notable that the authors - based on single-cell analysis results - proposed that TFs and target genes are not necessarily always highly expressed in the same cells. Many of the important TFs they previously identified, along with their target genes (CsTSI or CsAlaDC), were not found in the same cell cluster. Therefore, they proposed a model in which the theanine biosynthesis pathway occurs via multicellular compartmentation and does not require high co-expression levels of transcription factors and their target genes within the same cell cluster. Since it is not known whether the theanine content is absolutely high in the cell cluster 1 containing a high CsAlaDC expression level (due to the lack of cell cluster theanine content determination, which may be a current technical challenge), it is difficult to determine whether this non-coexpressing cell cluster 1 is a precise regulatory mechanism for inhibiting theanine content in plants.

Thank you for your comments. We concur with your assessment that the accumulation level of the spatial distribution of theanine may affect the expression of these genes. However, as you said, due to some technical limitations, we are not currently in a position to verify this distribution of theanine at the root cell spatial level. The spatial distribution of theanine in the roots can be affected by transport processes. So, it is likely that the cell types in which theanine is distributed do not exactly correspond to the cell types in which theanine is being synthesized (Line 491-493). We will make efforts in this direction to characterize the spatial distribution of theanine using techniques such as spatial metabolome and mass spectrometry imaging in the future (Line 582-586).

In fact, there are a small number of cells where TFs and CsAlaDC are simultaneously highly expressed, but the quantity is insufficient to form a separate cluster. However, these few cells may be sufficient to meet the current demands for theanine synthesis. This possibility may better align with some previous experiments and validation results in this study. Moreover, I feel that under normal conditions, plants may not mobilize a large number of cells to synthesize a particular substance. Perhaps, cell cluster 1 is actually a type of cell that inhibits the synthesis of theanine, aiming to prevent excessive theanine production? I do not oppose the model proposed by the author, but I feel there is a possibility as I mentioned. If it seems reasonable, the author may consider adding it to an appropriate position in the discussion.

Thanks a lot for your suggestion. We agree that tea plant roots likely have mechanisms aiming to prevent excessive theanine production.We have improved our discussion according your suggestion. 

Theanine is the most abundant free amino acid in the tea plant, accounting for 1-2% of leaf dry weight (Line 62-63), and can even reach 4-6% in the root, accounting for more than 60%-80% of the total free amino acids (Yang et al., 2020). This means that theanine biosynthesis indeed requires the root cells to consume significant resources and energy. Thus, theanine biosynthesis needs to be controlled by a series of regulation mechanisms, which would function as a “brake”. In a previous study, we suggested that CsMYB40 and CsHHO3 bound to the CsAlaDC promoter to regulate theanine synthesis, at the transcription level, in “accelerator” or “brake” mode to maintain stable synthesis of theanines (Guo et al., 2022). At a posttranslational level, CsTSI and CsAlaDC are modified by ubiquitination, which is probably involved in the degradation of these proteins in response to N levels (Wang et al., 2021). In the current study, we discovered a novel “brake” in the form of spatial separation. The differential expression of AlaDC and TSI suggests that ethylamine and theanine are synthesized in separate different cell types, allowing cell compartmentalization of the synthetic precursor and the product to form multicellular compartmentation of metabolites (Line 270-280). On the one hand, compartmentalization may effectively prevent interference between secondary metabolic pathways, whereas compartmentalization could also be used as a way of metabolic regulation to avoid excessive, or inhibition of, theanine synthesis (Line 483-488).

Reference

Guo, J. et al. (2022). Potential “accelerator” and “brake” regulation of theanine biosynthesis in tea plant (Camellia sinensis). Hortic. Res. 9:uhac169.

Yang, T. et al. (2020). Transcriptional regulation of amino acid metabolism in response to nitrogen deficiency and nitrogen forms in tea plant root (Camellia sinensis L.). Sci. Rep. 10:6868.

Wang, Y. et al. (2021). Nitrogen-Regulated Theanine and Flavonoid Biosynthesis in Tea Plant Roots: Protein-Level Regulation Revealed by Multiomics Analyses. J Agric Food Chem. 69:10002-10016.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

(1) The dataset, including the raw sequencing data and processed files is *.Rdata and should be deposited in a public database for accessibility and reproducibility.

Thanks for your comments and advice. The raw data and processed files have been submitted to the Gene Expression Omnibus (https://www.ncbi.nlm.nih.gov/geo/) under accession number GSE267845 (Line 763-764).

(2) Providing the code for the primary analysis steps in a publicly accessible location would facilitate others in replicating the analysis.

Thank you for your comment. Unfortunately, we have been unable to obtain permission to publicly release a portion of the primary analysis code due to its intellectual property belonging to OE Corporation.

(3) Enhancements in the writing of the manuscript are recommended for improved clarity and coherence.

Thanks. We revised our writing to improve the manuscript clarity and coherence.

Reviewer #3 (Recommendations For The Authors):

Suggestions for revisions:

(1) Introduction and Discussion, there are too many paragraphs, even one sentence is a paragraph. I suggest that all the sentences in Introduction be merged into three big paragraphs. For example, lines 30-57 become the first paragraph, lines 58-87 become the second paragraph, lines 88-106 become the third paragraph, and the authors can merge them reasonably according to the content. The discussion part is also suggested to be divided into several paragraphs according to the focus, and perhaps it is more appropriate to give a title to each paragraph.

Thank you for your comments and suggestions. We have merged several paragraphs and added a title to each paragraph in the Discussion section (“Cell cluster annotation of non-transgenic plants” in line 428; “Nitrogen metabolism and transport of tea plant root at the single cell level” in line 445; “Multicellular compartmentation of theanine metabolism and transport” in line 469; “The regulation of theanine biosynthesis at the single cell level” in line 517; “Cross-talk between theanine metabolism and root development” in line 554).

(2) Tea is a food, while tea tree is a substance. It should be tea plant root instead of tea root, it is suggested to revise this issue in the whole text.

Thanks. We corrected “tea root” to “tea plant root” in this manuscript.

(3) Lines 35-43, this sentence is too long, suggest each example should be one sentence.

Thanks. We revised this sentence into short sentences. We changed this part to “Root-synthesized flavonoids regulate root tip growth through affecting auxin transport and metabolism (Santelia et al., 2008; Wan et al., 2018). Legume roots secrete flavonoids as signaling agents to attract symbiotic bacteria, such as Rhizobium for nitrogen fixation (Hartman et al., 2017). In Abies nordmanniana, volatile organic compounds (e.g., propanal, g-nonalactone, and dimethyl disulfide) function to recruit certain bacteria or fungi, such as Paenibacillus. Paenibacillus sp. S37 produces high quantities of indole-3-acetic acid that can then promote plant root growth (Garcia-Lemos et al., 2020; Schulz-Bohm et al., 2018).” (Line 35-42)

(4) Line 510 is missing a reference.

Thank you - we have added the reference in the revised manuscript (Line 549 and Line 840-842).

eLife assessment

The regulation of mitosis and the dynamics of the mitotic spindle in it are central to cell division with high fidelity and crucial for normal division and development and defects therein can lead to disease. A key component of ensuring the fidelity is the "spindle assembly checkpoint". This valuable study using convincing experimental approaches in fission yeast has revealed novel links between the MAP-kinase signalling pathway modulating the spindle assembly checkpoint.

Reviewer #1 (Public review):

Summary:

This manuscript addresses two main issues: (i) do MAPKs play an important role in SAC regulation in single cell organism such as S pombe? (ii) what is the nature of their involvement and what are their molecular targets?<br /> The authors have extensively used the cold-sensitive β-tubulin mutant to activate or inactivate SAC employing an arrest-release protocol. Localization of Cdc13 (cyclin B) to the SPBs is used as a readout for the SAC activation or inactivation. The roles of two major MAPK pathways i.e. stress activated pathway (SAP) and cell integrity pathway (CIP), have been explored in this context (with CIP more extensively than SAP). Sty1Δ or pmk1Δ mutants were used to inactivate the SAP or CIP pathways and wis1DD or pek1DD expression was utilized to constitutively activate these pathways, respectively. Lowering of Slp1Cdc20 abundance (by phosphorylation of Slp1-Thr 480) is revealed as the main function of MAPK to augment the robustness of spindle assembly checkpoint.

Strengths:

The experiments are generally well-conducted, and the results support the interpretations in various sections. The experimental data clearly support some of the key conclusions:<br /> (i) while inactivation of SAP and CIP compromises SAC-imposed arrest, their constitutive activation delays the release from the SAC-imposed arrest (ii) CIP signaling, but not SAP signaling, attenuates Slp1Cdc20 levels (iii) Pmk1 and Cdc20 physical interact and Pmk1-docking sequences in Slp1 (PDSS) is identifies and confirmed by mutational/substitution experiments (iv) Thr480 (and also S76) is identified as the residue phosphorylated by Pmk1. S28 and T31 are identified as Cdk1 phosphorylation sites. These are confirmed by mutational and other related analyses (v) Functional aspects of the phosphorylation sites have been elucidated to some extent: (a) Phosphorylation of Slp1-T480 by Pmk1 reduces its abundance thereby augmenting the SAC-induced arrest (b) S28, T31 (also S59) are phosphorylated by Cdk1 (v) K472 and K479 residues are involved in ubiquitylation of Slp1

Weaknesses:

(i) Cdc13 localization to SPBs has been used as a readout for SAC activation/inactivation throughout the manuscript. However, the only image showing such localization (Figure 1C) is of poor quality where the Cdc13 localization to SPBs barely visible. This should be replaced by a better image.

(ii) The overlapping error-bars in Cdc13-localization data in some figures (for instance Figure 3E and 4H) makes the effect of various mutations on SAC activation/inactivation rather marginal. In some of these cases, Western-blotting data support the author's conclusions better.

(iii) This specific point is not really a weakness but rather a loose end:<br /> One of the conclusions of this study is that MAPK (PMK1) contributes to the robustness of SAC-induced arrest by lowering the abundance of Slp1Cdc20. The authors have used pmk1Δ or constitutively activating the MAPK pathways (Pek1DD) and documenting their effect on SAC activation/inactivation dynamics. It is not clear if SAC activation also leads to activation of MAPK pathways for them to contribute to the SAC robustness. To tie this loose end, the author could have checked if MAPK pathway is also activated under the conditions when SAC is activated. Unless this is shown, one must assume that the authors are attributing the effect they observe to the basal activity of MAPKs.

(iv) This is also a loose end:<br /> The authors show that activation of stress pathways (by addition of KCL instance) causes phosphorylation-dependent Slp1Cdc20 downregulation (Figure 6) under SAC-activating conditions. Does activation of the stress pathway cause phosphorylation-dependent Slp1Cdc20 downregulation under non-SAC-activation conditions or does it occur only under SAC-activating conditions?

(v) Although the authors have gone to some length to identify S28, T31 (also S59) as phosphorylation sites for Cdk1, their functional significance in the context of MAPK involvement is not yet clear. Perhaps it is outside the scope of this study to dig deeper into this aspect more than the authors have.

(vi) In its current state, the Discussion section is quite disjointed. The first section "Involvement of MAPKs in cell cycle regulation" should be in the Introduction section (very briefly, if at all). It certainly does not belong to the Discussion section. In any case, the Discussion section should be more organized with better flow of arguments/interpretations.

Reviewer #2 (Public review):

Summary:

This study by Sun et al. presents a role for the S. pombe MAP kinase Pmk1 in the activation of the Spindle Assembly Checkpoint (SAC) via controlling the protein levels of APC/C activator Cdc20 (Slp1 in S. pombe). The data presented in the manuscript is thorough and convincing. The authors have shown that Pmk1 binds and phosphorylates Slp1, promoting its ubiquitination and subsequent degradation. Since Cdc20 is an activator of APC/C, which promotes anaphase entry, constitutive Pmk1 activation leads to an increased percentage of metaphase-arrested cells. The authors have used genetic and environmental stress conditions to modulate MAP kinase signalling and demonstrate their effect on APC/C activation. This work provides evidence for the role of MAP kinases in cell cycle regulation in S. pombe and opens avenues for exploration of similar regulation in other eukaryotes.

Strengths:

The authors have done a very comprehensive experimental analysis to support their hypothesis. The data is well represented, and including a model in every figure summarizes the data well.

Weaknesses:

As mentioned in the comments, the manuscript does not establish that MAP kinase activity leads to genome stability when cells are subjected to genotoxic stressors. That would establish the importance of this pathway for checkpoint activation.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This manuscript addresses two main issues:

(i) do MAPKs play an important role in SAC regulation in single-cell organism such as S. pombe?

(ii) what is the nature of their involvement and what are their molecular targets?

The authors have extensively used the cold-sensitive β-tubulin mutant to activate or inactivate SAC employing an arrest-release protocol. Localization of Cdc13 (cyclin B) to the SPBs is used as a readout for the SAC activation or inactivation. The roles of two major MAPK pathways i.e. stress-activated pathway (SAP) and cell integrity pathway (CIP), have been explored in this context (with CIP more extensively than SAP). sty1Δ or pmk1Δ mutants were used to inactivate the SAP or CIP pathways and wis1DD or pek1DD expression was utilized to constitutively activate these pathways, respectively. Lowering of Slp1Cdc20 abundance (by phosphorylation of Slp1-Thr 480) is revealed as the main function of MAPK to augment the robustness of the spindle assembly checkpoint.

Strengths:

The experiments are generally well-conducted, and the results support the interpretations in various sections. The experimental data clearly supports some of the key conclusions:

(1) While inactivation of SAP and CIP compromises SAC-imposed arrest, their constitutive activation delays the release from the SAC-imposed arrest.

(2) CIP signaling, but not SAP signaling, attenuates Slp1Cdc20 levels.

(3) Pmk1 and Cdc20 physically interact and Pmk1-docking sequences in Slp1 (PDSS) are identified and confirmed by mutational/substitution experiments.

(4) Thr480 (and also S76) is identified as the residue phosphorylated by Pmk1. S28 and T31 are identified as Cdk1 phosphorylation sites. These are confirmed by mutational and other related analyses.

(5) Functional aspects of the phosphorylation sites have been elucidated to some extent: (a) Phosphorylation of Slp1-T480 by Pmk1 reduces its abundance thereby augmenting the SAC-induced arrest; (b) S28, T31 (also S59) are phosphorylated by Cdk1; (c) K472 and K479 residues are involved in ubiquitylation of Slp1.

Weaknesses:

(1) Cdc13 localization to SPBs has been used as a readout for SAC activation/inactivation throughout the manuscript. However, the only image showing such localization (Figure 1C) is of poor quality where the Cdc13 localization to SPBs is barely visible. This should be replaced by a better image.

We have replaced those pictures with a new set of representative images, which show clear presence or absence of SPB-localized Cdc13-GFP.

(2) The overlapping error bars in Cdc13-localization data in some figures (for instance Figure 3E and 4H) make the effect of various mutations on SAC activation/inactivation rather marginal. In some of these cases, Western-blotting data support the authors' conclusions better.

We agree that the overlapping error bars may look ambiguous in most figures showing time course curves, this is due to the fact that all these data from a group of strains have to be better presented in a single graph to more directly compare the potential effects. We have been fully aware of the drawback of these figure representations, that is why we always presented the data corresponding two major time points (0 and 50 min after release) from all time course analyses in an alternative way, namely using individual histograms to represent the data from each strain with means of repeats, absolute values, error bars and p values clearly labeled. In particular, the data from time point 0 min can provide important information on the SAC activation efficiency. Generally, we placed those data and graphs in corresponding supplemental figures, such as: Figure 1-figure supplement 1C, Figure 1-figure supplement 2D, Figure 3-figure supplement 3, Figure 4-figure supplement 6B, Figure 5-figure supplement 1, and Figure 6-figure supplement 2.

In addition, as you have noticed, almost all time course data were backed up by our Western blotting data.

(3) This specific point is not really a weakness but rather a loose end:

One of the conclusions of this study is that MAPK (Pmk1) contributes to the robustness of SAC-induced arrest by lowering the abundance of Slp1Cdc20. The authors have used pmk1Δ or constitutively activating the MAPK pathways (Pek1DD) and documented their effect on SAC activation/inactivation dynamics. It is not clear if SAC activation also leads to activation of MAPK pathways for them to contribute to the SAC robustness. To tie this loose end, the author could have checked if the MAPK pathway is also activated under the conditions when SAC is activated. Unless this is shown, one must assume that the authors are attributing the effect they observe to the basal activity of MAPKs.

We agree with your concern. We have followed your suggestion and performed further experiments. Please see our more detailed response to your point #ii(a) in your “Recommendations for the authors”.

(4) This is also a loose end:

The authors show that activation of stress pathways (by addition of KCl for instance) causes phosphorylation-dependent Slp1Cdc20 downregulation (Figure 6) under the SAC-activating condition. Does activation of the stress pathway cause phosphorylation-dependent Slp1Cdc20 downregulation under the non-SAC-activation condition or does it occur only under the SAC-activating condition?

We agree with your concern. We have followed your suggestion and performed further experiments. Please see our more detailed response to your point #ii(b) in your “Recommendations for the authors”.

(5) Although the authors have gone to some length to identify S28 and T31 (also S59) as phosphorylation sites for Cdk1, their functional significance in the context of MAPK involvement is not yet clear. Perhaps it is outside the scope of this study to dig deeper into this aspect more than the authors have.

Based on our data from Mass spectrometry analysis, mutational analysis, in vitro and in vivo kinase assays using phosphorylation site-specific antibodies, we confirmed that at least S28 and T31 are Cdk1 phosphorylation sites. From our time course analysis of these phosphorylation-deficient mutants, it seems the mechanisms of Slp1 activity or protein abundance regulated by Cdk1 or MAPK are quite different. How these two or even more kinases coordinate to control Slp1 activity during APC/C activation is one very interesting issue to be investigated, however, as you have realized, it is indeed beyond the scope of our current study.

(6) In its current state, the Discussion section is quite disjointed. The first section "Involvement of MAPKs in cell cycle regulation" should be in the Introduction section (very briefly, if at all). It certainly does not belong to the Discussion section. In any case, the Discussion section should be more organized with a better flow of arguments/interpretations.

We have re-organized our “Discussion” section. Please see our more detailed response to your point #iii in your “Recommendations for the authors”.

Reviewer #2 (Public Review):

Summary:

This study by Sun et al. presents a role for the S. pombe MAP kinase Pmk1 in the activation of the Spindle Assembly Checkpoint (SAC) via controlling the protein levels of APC/C activator Cdc20 (Slp1 in S. pombe). The data presented in the manuscript is thorough and convincing. The authors have shown that Pmk1 binds and phosphorylates Slp1, promoting its ubiquitination and subsequent degradation. Since Cdc20 is an activator of APC/C, which promotes anaphase entry, constitutive Pmk1 activation leads to an increased percentage of metaphase-arrested cells. The authors have used genetic and environmental stress conditions to modulate MAP kinase signalling and demonstrate their effect on APC/C activation. This work provides evidence for the role of MAP kinases in cell cycle regulation in S. pombe and opens avenues for exploration of similar regulation in other eukaryotes.

Strengths:

The authors have done a very comprehensive experimental analysis to support their hypothesis. The data is well represented, and including a model in every figure summarizes the data well.

Weaknesses:

As mentioned in the comments, the manuscript does not establish that MAP kinase activity leads to genome stability when cells are subjected to genotoxic stressors. That would establish the importance of this pathway for checkpoint activation.

We understand your concern. We have followed your suggestion and performed further experiments to examine whether the absence of Pmk1 causes chromosome segregation defects. Please see our more detailed response to your point #5 in your “Recommendations for the authors”.

Recommendations for the authors:

Reviewing Editor

Please go through the reviews and recommendations and revise the paper accordingly. I think nearly everything is very straightforward and all issues raised by the two expert referees are fully justified. I look forward to seeing an appropriately revised manuscript.

Reviewer #1 (Recommendations For The Authors):<br /> (i) Cdc13 localization to SPBs has been used as a readout for SAC activation/inactivation throughout the manuscript. However, the only image showing such localization (Figure 1C) is of poor quality where the Cdc13 localization to SPBs is barely visible. This should be replaced by a better image.

We have replaced those pictures with a new set of representative images, which show clear presence or absence of SPB-localized Cdc13-GFP.

(ii) I reiterate the loose ends in this manuscript I have mentioned above. If the authors have already conducted these experiments, they should include the results in the manuscript to tighten the story further. (I am not suggesting that the authors must perform these experiments...if they have not).

(a) One of conclusions of this study is that MAPK (Pmk1) contributes to the robustness of SAC-induced arrest by lowering the abundance of Slp1Cdc20. The authors have used pmk1Δ or constitutively activating the MAPK pathways (pek1DD) and documented their effect on SAC activation/inactivation dynamics. It is not clear if SAC activation also leads to activation of MAPK pathways for them to contribute to the SAC robustness. To tie this loose end, the author could have checked if the MAPK pathway is also activated under the conditions when SAC is activated. Unless this is shown, one must assume that the authors are attributing the effect they observe to the basal activity of MAPKs.

Actually, our data shown in Figure 6B demonstrated that SAC activation per se cannot trigger activation of MAPK pathway CIP, because we did not observe any elevated Pmk1 phosphorylation (i.e. Pmk1-P detected by anti-phospho p42/44 antibodies) in nda3-arrested cells (Please see “control” samples in Figure 6B).

To corroborate this observation, we further examined the Pmk1 phosphorylation/activation in Mad2-overexpressing cells, and could not detect elevated Pmk1 phosphorylation. This data again lends support to the notion that SAC activation per se cannot trigger activation of CIP signaling.

We have added our newly obtained result in Figure 6-figure supplement 1 in our revised manuscript.

(b) The authors show that activation of stress pathways (by addition of KCL instance) causes phosphorylation-dependent Slp1Cdc20 downregulation (Figure 6) under the SAC-activating conditions. Does activation of the stress pathway cause phosphorylation-dependent Slp1Cdc20 downregulation under the non-SAC-activation conditions or does it occur only under the SAC-activating condition?

As you suggested, we have constructed cdc25-22 background strains with pmk1+ deleted or expressing Padh11-pek1DD to remove or constitutively activate CIP signaling, respectively. By immunoblotting, we followed the Slp1Cdc20 levels when cells went through mitosis after being released at 25 °C from G2/M-arrest at high temperature. We found that Slp1Cdc20 levels in pek1DD cells were only marginally reduced compared to wild-type cells, whereas we failed to observe any elevated Slp1Cdc20 levels in pmk1Δ cells. These results suggested that CIP signaling only plays a negligible role in influencing Slp1Cdc20 levels under the non-SAC-activation conditions.

We have presented our newly obtained result in Figure 2-figure supplement 1 in our revised manuscript.

(iii) The Discussion section is quite disjointed. The first section "Involvement of MAPKs in cell cycle regulation" should be in the Introduction section (very briefly, if at all). It certainly does not belong to the Discussion section. In any case, the Discussion section should be more organized with a better flow of arguments/interpretations.

Thank you for suggestion on the organization and flow for “Discussion”. We have reorganized our “Discussion” sections and moved the previous “Involvement of MAPKs in cell cycle regulation” to the section “Introduction” and rewrote the corresponding paragraph.

(iv) A minor point in this context:

In the cold-sensitive β-tubulin mutant, growth at 18C causes loss of kinetochore-microtubule attachments as well as the intra-kinetochore tension. Both perturbations individually can lead to the activation of SAC. This study does not distinguish whether MAPK involvement in SAC dynamics is relevant to one perturbation or another or both. It would be pertinent to briefly mention this point in the Discussion section.

As you suggested, we have added two sentences to briefly mention this point in our “Discussion” section.

Reviewer #2 (Recommendations For The Authors):

This study by Sun et al. presents a role for the S. pombe MAP kinase Pmk1 in the activation of the Spindle Assembly Checkpoint (SAC) via controlling the protein levels of APC/C activator Cdc20 (Slp1 in S. pombe). The data presented in the manuscript is thorough and convincing. The authors have shown that Pmk1 binds and phosphorylates Slp1, promoting its ubiquitination and subsequent degradation. Since Cdc20 is an activator of APC/C, which promotes anaphase entry, constitutive Pmk1 activation leads to an increased percentage of metaphase-arrested cells. The authors have used genetic and environmental stress conditions to modulate MAP kinase signalling and demonstrate their effect on APC/C activation. This work provides evidence for the role of MAP kinases in cell cycle regulation in S. pombe and opens avenues for exploration of similar regulation in other eukaryotes.

Although the data largely supports the conclusions, a major addition will be testing whether cells accumulate chromosomal or inheritance defects when MAPK Pmk1 is absent. It will be interesting to know that this mechanism of SAC activation contributes to genome integrity.

Some additions that can improve the manuscript are mentioned below:

(1) In Figure 1, the authors should also test the effect of constitutive activation of Spk1 to rule out the involvement of the PSP pathway.

To meet your curiosity and requirement, we have constructed yeast strains expressing constitutively active byr1DD alleles carrying S214D and T218D point mutations under the control of the adh21 or adh11 promoters (Padh21 or Padh11 in short), i.e. Padh21-6HA-byr1DD and Padh11-6HA-byr1DD, respectively. We examined the expression of these byr1DD alleles by Western blotting, and tested the TBZ sensitivity of these alleles and also checked whether they affect the efficiency of SAC activation or inactivation. Our results showed that constitutive activation of Spk1 by overexpressing Byr1DD does not cause yeast cells to be TBZ-sensitive or affect the efficiency of SAC activation or inactivation.

We have added these new data in Figure 1-figure supplement 2 in our revised manuscript.

(2) The number of analyzed cells (n) should be mentioned in the figure legends in Figure 1D, and all other figure panels should represent similar data in the consequent figures.

We have added the information on sample size for all experiments involving time course analyses.

(3) The authors should also use another arresting mechanism (e.g. nocodazole treatment) and corroborate the result in Figure 1C to rule out any effects due to the mutant.

Figure 1C in our manuscript actually shows our experimental design and not the result. We guess here you asked for alternative strategy to arrest cells at metaphase and confirm our results shown in Figure 1D.

We need to mention that, as a commonly used inhibitor of microtubule polymerization, Nocodazole is very effective in mammalian and human cells and also in budding yeast cells, but not effective at all in wild-type fission yeast cells. It has been found that Nocodazole is only active in fission yeast α- or β-tubulin mutants (please see Umesono, K., et al., J Mol Biol. 168 (2): 271-284 (1983); PMID: 6887245; DOI: 10.1016/s0022-2836(83)80018-7.) or multidrug resistance (MDR) transporter mutants (please see Kawashima, SA, et al., Chemistry & Biology 19, 893–901 (2012); PMID: 22840777; doi: 10.1016/j.chembiol.2012.06.008.). Therefore, this feature of Nocodazole has limited and restricted its routine use as a metaphase arrest or spindle checkpoint activation drug in fission yeast.

Instead, in order to achieve the spindle checkpoint activation and metaphase arrest, we took advantage of a metaphase-arresting mechanism involving Mad2 overexpression, which has been described and used previously (Please see He, X., et al., Proc Natl Acad Sci USA. 94 (15): 7965-70 (1997); PMID: 9223296; DOI: 10.1073/pnas.94.15.7965, and May, K.M., et al., Current Biology, 27(8):1221-1228 (2017); PMID: 28366744; DOI: 10.1016/j.cub.2017.03.013). With this strategy, we could analyze the metaphase-arresting and SAC-activation efficiency by counting cells with short spindles as judged by GFP-Atb2 signals. We compared the frequencies of cells with short spindles in wild-type, pmk1Δ, sty1-T97A, and spk1Δ backgrounds after Mad2 has been induced to overexpress for 18 hours, and found that SAC-activating efficiency was compromised in pmk1Δ and sty1-T97A cells, but not in spk1Δ cells. This data indeed corroborated our result shown in Figure 1D and ruled out possible effects due to the nda3-KM311 mutant.

We have added this new data in Figure 1-figure supplement 3 in our revised manuscript.

(4) It would also be helpful to assess SAC or APC/C activation with another cellular readout in addition to Cdc13-GFP accumulation on SPBs, at least for initial experiments.

Actually, Cdc13-GFP accumulation on SPBs has been routinely used as a reliable cellular readout for SAC or APC/C activation in the field. It was first developed and used by Kevin Hardwick lab in their paper (Vanoosthuyse V and Hardwick KG. Curr Biol. 2009, 19(14):1176-81. PMID: 19592249; doi: 10.1016/j.cub.2009.05.060.). This method was also used in a paper by Meadows JC, et al. (2011) (Dev Cell. 20(6):739-50. PMID: 21664573; doi: 10.1016/j.devcel.2011.05.008.).

In our previous study, we also employed a different strategy to assess SAC inactivation or APC/C activation, in which degradation of nuclear Cut2-GFP was used as a cellular readout (Please see S4 Fig in Bai S, et al., PLoS Genet 18(9): e1010397 (2022); PMID: 36108046; DOI: 10.1371/journal.pgen.1010397.). Cut2 is the securin homologue in S. pombe and therefore also a target of APC/C at anaphase. Our data in the above paper confirmed that the degradation of both nuclear Cut2-GFP and SPB-localized Cdc13-GFP shows similar dynamics when cells are released from metaphase-arrest.

As we described in our response to your comment #3, we employed short spindles visualized by GFP-Atb2 signals as an alternative readout for metaphase-arrest and SAC-activation in cells overexpressing Mad2. We confirmed that SAC-activation efficiency was compromised in pmk1Δ and sty1-T97A cells, but not in spk1Δ cells.

(5) The authors have shown a role for Pmk1 in controlling the activation of APC/C and, hence, cell cycle progression through metaphase to anaphase. One crucial experiment would be to check if pmk1Δ cells show an accumulation of chromosomal aberrations or unequal distribution when subjected to genotoxic stressors. That would implicate a direct importance on Pmk1's role in cell cycle arrest and genome maintenance.

As you suggested, we have constructed cdc25-22 GFP-atb2+ strains with pmk1+ present or deleted, and treated cells with 0.6 M KCl or 2 μg/mL caspofungin to activate MAPKs and checked whether the absence of pmk1 could cause defective chromosome segregation in anaphase cells. Indeed, we found that stressed pmk1Δ cells displayed greatly increased frequency of lagging chromosomes and chromosome mis-segregation at mitotic anaphase compared to similarly treated wild-type cells and also untreated pmk1Δ cells. This new data implicated a direct role for Pmk1 in cell cycle arrest and genome maintenance, especially when cells are exposed to adverse environment.

We have presented this new data as Figure 7 in our revised manuscript.

Typos:

(1) In line 406, "docking" is misspelled as "docing".

Thank you for pointing this out. We have corrected this mistake.

(2) In Figure 6, panel "F" is not marked in the figure.

We mistakenly mentioned and labeled “F” in Figure 6 legend. In our revised manuscript, we have added new results of protein levels of Pmk1 phosphorylation- and ubiquitylation-deficient Slp1Cdc20 mutants upon SAC activation detected by Western blotting in Figure 6-figure supplement 3.

(3) In Figure S1, panel "D" is not marked.

We apologize for our previous wording in our former Figure S1 legend, which was misleading. Actually, there was no panel “D” in Figure S1 (now Figure 1-figure supplement 1). We have rewritten the legend to avoid ambiguity.

eLife assessment

This valuable study characterises receptors for calcitonin-related peptides from a deuterostomian animal, the echinoderm Apostichopus japonicus, by a combination of heterologous expression, pharmacological experiments, and the quantification of gene-expression levels. The authors provide solid evidence for a functional calcitonin-related peptide system in the sea cucumber, but some of the phylogenetic and statistical analyses and the evidence of a physiological function are incomplete. This work should be of interest to scientists studying the signaling pathways, functions, and evolution of neuropeptides, and could be of relevance to improving the culture conditions of this economically key species.

Reviewer #1 (Public review):

Summary:

The manuscript characterizes a functional peptidergic system in the echinoderm Apostichopus japonicus that is related to the widely conserved family of calcitonin/diuretic hormone 31 (CT/DH31) peptides in bilaterian animals. In vitro analysis of receptor-ligand interactions, using multiple receptor activation assays, identifies three cognate receptors for two CT-like peptides in the sea cucumber, which stimulate cAMP, calcium, and ERK signaling. Only one of these receptors is closely related to the family of calcitonin and calcitonin-like receptors (CTR/CLR) in bilaterian animals, whereas two other receptors cluster with invertebrate pigment dispersing factor receptors (PDFRs). In addition, this study sheds light on the transcript expression and in vivo functions of CT-like peptides in A. japonicus, by quantitative real-time PCR, in situ hybridization, pharmacological experiments on body wall muscle and intestine preparations, and peptide injection and RNAi knockdown experiments. This reveals a conserved function of CT-like peptides as muscle relaxants and hints at a potential role as growth regulators in A. japonicus.

Strengths:

This work combines both in vitro and in vivo functional assays to identify a CT-like peptidergic system in an economically relevant echinoderm species, the sea cucumber A. japonicus. A major strength of the study is that it identifies three G protein-coupled receptors for AjCT-like peptides, one related to the CTR/CLR family and two related to the PDFR family. A similar finding was previously reported for the CT-related peptide DH31 in Drosophila melanogaster that activates both CT-type and PDF-type receptors. Here, the authors expand this observation to a deuterostomian animal, which suggests that receptor promiscuity is a more general feature of the CT/DH31 peptide family and that CT/DH31-like peptides may activate both CT-type and PDF-type receptors in other animals as well.

Besides the identification of receptor-ligand pairs, the downstream signaling pathways of AjCT receptors have been characterized, highlighting broad effects on cAMP, calcium, and ERK signaling. Functional characterization of the CT-related peptide system in heterologous cells is complemented with ex vivo and in vivo experiments. First, peptide injection and RNAi knockdown experiments establish transcriptional regulation of all three identified receptors in response to changing AjCT peptide levels. Second, ex vivo experiments reveal a conserved role for the two CT-like peptides as muscle relaxants, which have differential effects on body wall muscle and intestine preparations. Finally, peptide injection studies suggest a putative role for one of the two CT-like peptides (AjCT2) in growth regulation.

Weaknesses:

Analysis of transcript expression is limited to the CT-peptide encoding gene, while no gene expression analysis was attempted for the three identified receptors. Differences in the activation of downstream signaling pathways between the three receptors are also questionable due to unclarities in the statistical analysis and variation in the control and experimental data in heterologous assays. Together, this makes it difficult to propose a mechanism underlying differences in the functions of the two CT-like peptides in muscle control and growth regulation.

The authors also suggest a putative orexigenic role for the CT-like peptidergic system in feeding behavior. This effect is not well supported by the experimental data provided, as no detailed analysis of feeding behavior was carried out (only indirect measurements were performed that could be influenced by other peptidergic effects, such as on muscle relaxation) and no statistically significant differences were reported in these assays.

Overall, details regarding statistical analyses are not (clearly) specified in the manuscript, and there are several instances where statements are not supported by literature evidence.

Reviewer #2 (Public review):

Summary:

The authors show that A. japonicus calcitonins (AjCT1 and AjCT2) activate not only the calcitonin/calcitonin-like receptor but also activate the two PDF receptors, ex vivo. They also explore secondary messenger pathways that are recruited following receptor activation. They determine the source of CT1 and CT2 using qPCR and in situ hybridization and finally test the effects of these peptides on tissue contractions, feeding, and growth. This study provides solid evidence that CT1 and CT2 act as ligands for calcitonin receptors; however, evidence supporting cross-talk between CT peptides and PDF receptors is only based on ex vivo experiments.

Strengths:

This is the first study to report the pharmacological characterization of CT receptors in an echinoderm. Multiple lines of evidence in cell culture (receptor internalization and secondary messenger pathways) support this conclusion.

Weaknesses:

The authors claim that A. japonicus CTs activate "PDF" receptors and suggest that this cross-talk is evolutionarily ancient since a similar phenomenon also exists in the fly Drosophila melanogaster. These conclusions are not fully supported for several reasons. The authors perform phylogenetic analysis to show that the two "PDF" receptors form an independent clade. This clade is sister to the clade comprising CT receptors. This phylogenetic analysis suffers from several issues. Firstly, the phylogenies lack bootstrap support. Secondly, the resolution of the phylogeny is poor because representative members from diverse phyla have not been included. For instance, insect or other protostomian PDF receptors have not been included so how can the authors distinguish between "PDF" receptors or another group of CT receptors? Thirdly, no in vivo evidence has been presented to support that CT can activate "PDF" receptors in vivo.

The source of CT which mediates the effects on longitudinal muscles and intestine is unclear. Is it autocrine or paracrine signaling by CT from the same tissue or is it long-range hormonal signaling?

Pharmacology experiments showing the effects of CT1 and CT2 on ACh-induced contractions were performed. Sample traces have been provided but no traces with ACh alone have been included. How long do ACh-induced contractions persist? These controls are necessary to differentiate between the eventual decay of ACh effects and relaxation induced by CT1 and CT2. The traces also do not reflect the results portrayed in dose-response curves. For instance, in Figure 6B, maximum relaxation is reported for 10-6M. Yet, the trace hardly shows any difference before and after the addition of 10-6M peptide. The maximum effect in the trace appears to be after the addition of 10-8M peptide.

I am unsure how differences in wet mass indicate feeding and growth differences since no justification has been provided. Couldn't wet mass also be influenced by differences in osmotic balance, a key function of calcitonin-like peptides in protostomian invertebrates? The statistical comparisons have not been included in Figure 7B.

While the authors succeeded in knocking down CT, the physiological effects of reduced CT signaling were not examined.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The manuscript characterizes a functional peptidergic system in the echinoderm Apostichopus japonicus that is related to the widely conserved family of calcitonin/diuretic hormone 31 (CT/DH31) peptides in bilaterian animals. In vitro analysis of receptor-ligand interactions, using multiple receptor activation assays, identifies three cognate receptors for two CT-like peptides in the sea cucumber, which stimulate cAMP, calcium, and ERK signaling. Only one of these receptors is closely related to the family of calcitonin and calcitonin-like receptors (CTR/CLR) in bilaterian animals, whereas two other receptors cluster with invertebrate pigment dispersing factor receptors (PDFRs). In addition, this study sheds light on the transcript expression and in vivo functions of CT-like peptides in A. japonicus, by quantitative real-time PCR, in situ hybridization, pharmacological experiments on body wall muscle and intestine preparations, and peptide injection and RNAi knockdown experiments. This reveals a conserved function of CT-like peptides as muscle relaxants and hints at a potential role as growth regulators in A. japonicus.

Strengths:

This work combines both in vitro and in vivo functional assays to identify a CT-like peptidergic system in an economically relevant echinoderm species, the sea cucumber A. japonicus. A major strength of the study is that it identifies three G protein-coupled receptors for AjCT-like peptides, one related to the CTR/CLR family and two related to the PDFR family. A similar finding was previously reported for the CT-related peptide DH31 in Drosophila melanogaster that activates both CT-type and PDF-type receptors. Here, the authors expand this observation to a deuterostomian animal, which suggests that receptor promiscuity is a more general feature of the CT/DH31 peptide family and that CT/DH31-like peptides may activate both CT-type and PDF-type receptors in other animals as well.

Besides the identification of receptor-ligand pairs, the downstream signaling pathways of AjCT receptors have been characterized, highlighting broad effects on cAMP, calcium, and ERK signaling. Functional characterization of the CT-related peptide system in heterologous cells is complemented with ex vivo and in vivo experiments. First, peptide injection and RNAi knockdown experiments establish transcriptional regulation of all three identified receptors in response to changing AjCT peptide levels. Second, ex vivo experiments reveal a conserved role for the two CT-like peptides as muscle relaxants, which have differential effects on body wall muscle and intestine preparations. Finally, peptide injection studies suggest a putative role for one of the two CT-like peptides (AjCT2) in growth regulation.

Weaknesses:

(1) Analysis of transcript expression is limited to the CT-peptide encoding gene, while no gene expression analysis was attempted for the three identified receptors. Differences in the activation of downstream signaling pathways between the three receptors are also questionable due to unclarities in the statistical analysis and variation in the control and experimental data in heterologous assays. Together, this makes it difficult to propose a mechanism underlying differences in the functions of the two CT-like peptides in muscle control and growth regulation.

Thank you for the reviewer’s comment, we will supplement the expression analysis for the three identified receptors. Actually, we did all the statistical tests for all the experiments, and maybe the form of marking is a bit messy, so sorry for the confusion and we will uniform them and include all this information both in the figure legends and the methods section. And for the variation in the control and experimental data, because every control is transfected with different receptors or uses cells from different batches, that is why the control conditions in different experiments have little bit variation.

(2) The authors also suggest a putative orexigenic role for the CT-like peptidergic system in feeding behavior. This effect is not well supported by the experimental data provided, as no detailed analysis of feeding behavior was carried out (only indirect measurements were performed that could be influenced by other peptidergic effects, such as on muscle relaxation) and no statistically significant differences were reported in these assays.

Thank you for the reviewer’s comment. Actually, we did all the statistical tests for all the experiments, the mass of remaining bait and the excrement were added in Figure 7A-figure supplement 1 and we will conduct additional behavioral experiments to explore the changes in feeding behavior of A. japonicus after injection of CT-type neuropeptides to support the role of CT-like peptidergic system in the regulation of feeding behavior, as I mentioned above, maybe the form of marking is a bit messy, so sorry for the confusion and we will uniform them and include all this information both in the figure legends and the methods section. And also we will supplement the experiments to further support our claim by assessing the feeding and growth factors after knocking down the CTP encoding genes.

(3) Overall, details regarding statistical analyses are not (clearly) specified in the manuscript, and there are several instances where statements are not supported by literature evidence.

Again, actually, we did all the statistical tests for all the experiments, as I mentioned above, maybe the form of marking is a bit messy, so sorry for the confusion and we will uniform them and include all this information both in the figure legends and the methods section. And we will also supplement more experiments and add more literature evidence to support our statements.

Reviewer #2 (Public review):

Summary:

The authors show that A. japonicus calcitonins (AjCT1 and AjCT2) activate not only the calcitonin/calcitonin-like receptor but also activate the two PDF receptors, ex vivo. They also explore secondary messenger pathways that are recruited following receptor activation. They determine the source of CT1 and CT2 using qPCR and in situ hybridization and finally test the effects of these peptides on tissue contractions, feeding, and growth. This study provides solid evidence that CT1 and CT2 act as ligands for calcitonin receptors; however, evidence supporting cross-talk between CT peptides and PDF receptors is only based on ex vivo experiments.

Strengths:

This is the first study to report the pharmacological characterization of CT receptors in an echinoderm. Multiple lines of evidence in cell culture (receptor internalization and secondary messenger pathways) support this conclusion.

Weaknesses:

(1) The authors claim that A. japonicus CTs activate "PDF" receptors and suggest that this cross-talk is evolutionarily ancient since a similar phenomenon also exists in the fly Drosophila melanogaster. These conclusions are not fully supported for several reasons. The authors perform phylogenetic analysis to show that the two "PDF" receptors form an independent clade. This clade is sister to the clade comprising CT receptors. This phylogenetic analysis suffers from several issues. Firstly, the phylogenies lack bootstrap support. Secondly, the resolution of the phylogeny is poor because representative members from diverse phyla have not been included. For instance, insect or other protostomian PDF receptors have not been included so how can the authors distinguish between "PDF" receptors or another group of CT receptors? Thirdly, no in vivo evidence has been presented to support that CT can activate "PDF" receptors in vivo.

We do agree with the reviewer that the cross-talk between CTs and PDFRs is not so solid based on our current study.

So firstly, we will re-do the phylogenetic analyses as the reviewer suggested and mark the bootstrap value, then we will supplement more experiments (like PDFR knockdown) to further confirm that CT can activate “PDF” receptors in vivo.

(2) The source of CT which mediates the effects on longitudinal muscles and intestine is unclear. Is it autocrine or paracrine signaling by CT from the same tissue or is it long-range hormonal signaling?

Thank you for the reviewer’s comment, actually we have done in situ and immunohistochemical experiments for CTP and CT in different tissues, we just did not put them in our current manuscript, we will add them in the revised version.

(3) Pharmacology experiments showing the effects of CT1 and CT2 on ACh-induced contractions were performed. Sample traces have been provided but no traces with ACh alone have been included. How long do ACh-induced contractions persist? These controls are necessary to differentiate between the eventual decay of ACh effects and relaxation induced by CT1 and CT2. The traces also do not reflect the results portrayed in dose-response curves. For instance, in Figure 6B, maximum relaxation is reported for 10-6M. Yet, the trace hardly shows any difference before and after the addition of 10-6M peptide. The maximum effect in the trace appears to be after the addition of 10-8M peptide.

Thank you for the reviewer’s comment, we will provide the trace of contraction caused by ACh alone. In Figure 6B, the trace represents successive treatments of neuropeptides at different concentrations, which represents a cumulative effect. Therefore, the corresponding receptors may become desensitized when high concentration of peptide is finally applied. Actually, we examined the pharmacological effects of CT2 at 10-6M concentrations, which exhibited the maximum relaxation, and we will provide this trace.

(4) I am unsure how differences in wet mass indicate feeding and growth differences since no justification has been provided. Couldn't wet mass also be influenced by differences in osmotic balance, a key function of calcitonin-like peptides in protostomian invertebrates? The statistical comparisons have not been included in Figure 7B.

Thank you for the reviewer’s comment, we will analyze the weight gain rate, growth rate and feeding rate of A. japonicus to explain the difference of feeding and growth between injection group and control group. And we can confirm that wet mass is not influenced by differences in osmotic balance, we will put our supporting evidence in supplementary files in revised manuscript and we did not find the key function of calcitonin-like peptides observed in protostomian invertebrates. And we will include the statistical comparisons in Figure 7B.

(5) While the authors succeeded in knocking down CT, the physiological effects of reduced CT signaling were not examined.

Thank you for the reviewer’s insightful suggestion, we will supplement the experiments about the physiological effects after knocking down CT.

eLife assessment

This valuable paper uses the ChEC-seq2 technique to investigate RNA polymerase II (RNAPII) binding patterns in yeast and demonstrates that this technique is a complementary method for investigating transcription mechanisms, especially slow steps at the initiation and termination regions. The authors use ChEC-seq2 data to investigate RNAPII kinetics and obtain solid data providing new insights into transcription regulation. This study highlights the importance of careful methodological comparisons in understanding RNAPII dynamics.

Reviewer #1 (Public review):

Summary:

In this study, the authors use ChEC-seq, an MNase-based method to map yeast RNA pol II. Part of the reasoning for this study is that earlier biochemical work suggested pol II initiation and termination should involve slow steps at the UAS/promoter and termination regions that are not well visualized by formaldehyde-based ChIP methods. Here the authors find that pol II ChIP and ChEC give complementary patterns. Pol II ChIP signals are strongest in the coding region (where ChIP signal correlates well with transcription (rho = 0.62)). In contrast, pol II ChEC signals are strongest at promoters (rho = 0.52) and terminator regions. Weaker upstream ChEC signals are also observed at the STM class genes where biochemical studies have suggested a form of Pol (and maybe other general factors) is recruited to UAS sites. ChEC of TFIIA and TFIIE give promoter-specific ChEC signals as expected. Extending this work to elongation factors Ctk1 and Spt5 unexpectedly give strong signals near the PIC location and little signals over the coding region. This, and mapping CTD S2 and S5 phosphorylation by ChEC suggests to me that, for some reason, ChEC isn't optimal for detecting components of the elongation complex over coding regions.

Examples are also presented where perturbations of transcription can be measured by ChEC. Modeling studies are shown where adjustment of kinetic parameters agree well with ChEC data and that these models can be used to estimate which steps in transcription are affected by various perturbations. No tests were performed to see if the predictions could be validated by other means. Finally, the role of nuclear pore binding by Gcn4 is explored, although the results do not seem convincing. Overall, the authors show that pol II ChEC is a valuable and complementary method for investigating transcription mechanisms and slow steps at the initiation and termination regions.

Reviewer #2 (Public review):

Summary:

The study by VanBelzen et. al. compares chromatin immunoprecipitation (ChIP-seq) and chromatin endogenous cleavage sequencing (ChEC-seq2) to examine RNA polymerase II (RNAPII) binding patterns in yeast. While ChIP-seq shows RNAPII enrichment mainly over transcribed regions, ChEC-seq2 highlights RNAPII binding at promoters and upstream activating sequences (UASs), suggesting it captures distinct RNAPII populations that the authors speculate are linked more tightly to active transcription. The authors develop a stochastic model for RNAPII kinetics using ChEC-seq2 data, revealing insights into transcription regulation and the role of the nuclear pore complex in stabilizing promoter-associated RNAPII. The study suggests that ChEC-seq2 identifies regulatory events that ChIP-seq may overlook.

Strengths:

(1) This is a carefully crafted study that adds significantly to existing literature in this area. Transgenic MNase fusions with endogenous Rpb1 and Rpb3 subunits were carefully performed, and complemented by fusions with several additional proteins that help the authors to dissect the transcription cycle. Both the S. cerevisiae lines and the sequencing data are likely to be of significant use to the community.

(2) The validation of ChEC-seq2 and its comparison with ChIP-seq is highly valuable technical information for the community.

(3) The kinetic modeling appears to be thoughtfully done.

Weaknesses:

(1) The term "nascent transcription" is all too often used interchangeably for NET-seq, PRO-seq, 4sU-seq, and other assays that often provide different types of information. The authors should make it clear their use of the term refers to SLAM-seq data.

(2) The authors do not perform any comparison to run-on (PRO-seq) data. My impression is that the distribution of PRO-seq signal in S. cerevisiae agrees better with the distribution the authors observe by ChIP-seq. PRO-seq only captures RNAPII that is engaged and actively transcribing. If PRO-seq does indeed provide a similar profile as ChIP-seq, wouldn't this indicate that the high frequency of association between RNAPII and either the promoter or UAS reflects RNAPII that has not yet started transcription elongation? Perhaps this could help sort out what types of activities are occurring at the UAS (which does not appear to require a full PIC) or at the promoter (which does)?

Author response:

Response to Reviewer #1:

We agree with the reviewer that ChIP is much better than ChEC at recovering RNA polymerase II and elongation factors associated with the transcribed regions.  We believe that this is due to cross-linking, which enriches for these interactions.  However, as we highlight in the manuscript, cross-linking may not accurately report on the occupancy of RNA polymerase II and elongation factors over all regions.  Although, by ChEC, we observe elongation factors upstream of the transcribed region, compared with total RNA polymerase II, the relative enrichment of elongation factors or phosphorylated RNA polymerase II is significantly higher over transcribed regions, with a bias to the 3’ end (Figure 4B & C). This is consistent with these proteins and modifications functioning in elongation.  

Regarding how convincing the results with the gcn4-pd mutant are, we would highlight that the phenotype of this mutant is a quantitative decrease in transcription and this leads to a quantitative decrease, rather than qualitative loss, of RNA polymerase II over the promoter, without impacting the association of RNA polymerase II over the UAS region.  This effect was small but statistically significant (p = 4e-5). Obviously, more mechanistic studies will need to be performed, but this result supports a role for the interaction with the nuclear pore complex in either enhancing the transfer of RNA polymerase II from the enhancer to the promoter or in preventing its dissociation from the promoter.

Response to Reviewer #2:

Thank you for your supportive comments and suggestions.  We will clarify our use of Nascent RNA in the text.  We agree that the stronger enrichment of the transcribed region from Rpb1 ChIP-seq experiments should correlate well with actively transcribing RNA polymerase II observed by PRO-seq; enrichment by PRO-seq reported in a paper from John Lis’ lab strongly favors transcribed regions with a modest peak over the terminator (PMID: 27197211, Figure 2A).  ChEC reveals functionally important forms of RNA polymerase II that are not engaged in transcription.  This manuscripts highlights the potential utility of ChEC-seq2 in measuring these interactions - suggested by the recent work from Buratowski and Gelles’ single molecule studies - globally.

eLife assessment

The manuscript by Li and coworkers analyzed astrocytic differentiation of midbrain floor plate-patterned neural cells originating from human iPS cells, with a LMX1A reporter. This valuable work identifies transcriptomic differences at the single-cell level, between astrocytes generated from LMX1A reporter positive or negative cells, as well as non-patterned astrocytes and neurons. The evidence is solid, but the paper can be strengthened by further analyses of the transcriptomic data, and astrocytic morphology; also, searching for some of the differentially expressed genes by immunohistochemistry in different regions of the mammalian brain, or in human specimens, would be very informative.

Reviewer #1 (Public Review):

Summary:

In a previous study, the authors developed a human iPS cell line which expresses Cre under the control of the Lmx1a promoter in order to track, select for, and differentiate human dopamine neurons. In the manuscript under review, the authors are using methods which they have modified to generate astrocytes from the same cell line. The authors are interested in examining astrocytes which are derived from regionalized, floor plate progenitors.

The fundamental weakness of this paper is that the authors are making arguments about regional identity but their work is limited to experiments in vitro. Some of the claims that the authors make should be tested in vivo - ie, in sections, at least. Are floor plate markers or other ventral markers ever expressed in astrocytes or glial progenitors in the mammalian fetus? When do astrocytes emerge in the floor plate? All of the data here are based on an overly simplified in vitro platform.

Lmx1a expression is not limited to the ventral midbrain; it is also expressed in other parts of the developing, ventral CNS and in the roof plate and dorsal CNS (Millonig et al, Nature 2000). Indeed, many of the phenotypes of the Lmx1a mutant mouse (dreher) have little to do with the ventral midbrain. The authors are making an assumption that regional identity is fixed when they begin their astrocyte differentiation protocol - not necessarily true. After astrocytic differentiation is initiated, the authors have done little to demonstrate that floor plate identity is maintained even in selected cells; in fact, the transcriptomic data suggests that the cells are released from a floor plate fate. The authors seem to realize this but do not make any attempt to prove their thesis. If regional identity is not maintained, the authors need a better experiment.

If regional identity is not maintained, so what? Don't we already know that this can happen? The authors acknowledge that this is known in the discussion.

The authors have done transcriptomics studies to follow the changes in these cells but they have not told us very much that is meaningful. It would be useful to validate some of the new astrocytic markers that they have identified - Pax and Irx genes (Welle et al., Glia 2021) come quickly to mind. What about genes related to Shh and Wnt signaling that are prevalent in the floor plate? In particular, a lot of work has been done examining the role of Shh on the properties and lineage of astrocytes (Farmer et al., Science 2016; Hill et al., eLife 2019; Gingrich et al., Neural Dev 2022; Xie et al., Cell Rep 2022). There are a lot of stones which remain unturned, here, and the authors could actually tell us much more without doing an immense amount of work. These suggestions and criticisms are described in far greater detail in the confidential comments to the authors.

Work Cited:

Chizhikov et al., Mamm Genome 2006. https://pubmed.ncbi.nlm.nih.gov/17019651/

Chizhikov et al., Development 2004. https://journals.biologists.com/dev/article/131/11/2693/42269/Control-of-roof-plate-formation-by-Lmx1a-in-the

Chizhikov et al., PNAS 2010. https://pubmed.ncbi.nlm.nih.gov/20498066/

Emsley and Macklis. Neuron Glia Biol 2007. https://www.ncbi.nlm.nih.gov/pmc/articles/PMC1820889/

Farmer et al., Science 2016. https://pubmed.ncbi.nlm.nih.gov/26912893/

Gross et al., Development 2016. https://www.ncbi.nlm.nih.gov/pmc/articles/PMC4958331/

Hill et al., eLife 2019. https://pubmed.ncbi.nlm.nih.gov/31194676/

Gingrich et al., Neural Dev 2022. https://pubmed.ncbi.nlm.nih.gov/35027088/

Iskusnykh et al., eLife 2023. https://elifesciences.org/articles/84095

Millonig et al, Nature 2000. https://pubmed.ncbi.nlm.nih.gov/10693804/

Welle et al. Glia 2021. https://pubmed.ncbi.nlm.nih.gov/36342840/

Xie et al., Cell Rep 2022. https://pubmed.ncbi.nlm.nih.gov/35196485/

Reviewer #2 (Public Review):

In the current manuscript Li et al., study the preservation of the regional identity during the process of astrocyte generation from pluripotent stem cells. More precisely, this work investigates if neural progenitor cells patterned for the ventral midbrain give rise to astrocytes with conserved regional specification, which could reflect the astrocytic heterogeneity in the brain. To this end, the authors utilized a previously generated reporter iPSC line in which the expression of introduced blue fluorescence protein (BFP) is subjacent to the activation of LMXA1, a ventral midbrain floor plate marker. The study reports that following a defined patterning protocol based on SHH and FGF8, over 90% of d19 cells, corresponding to a neural progenitor stage, acquired the midbrain floor plate identity. However, during the subsequent astrogenic induction and glial progenitor expansion, this identity is gradually lost, supposedly due to the growth advantage of cells deriving from the residual LMX1A- neural progenitors. Contrariwise, if the LMX1A+ progenitors were purified, regional identity would be maintained throughout the astrocytic generation and incur an early astrogenic switch and maturation of derived astrocytes. By using single-cell RNA sequencing, the authors further identified distinct transcriptomic signatures on the astrocytic progeny of LMX1A- and LMX1A- progenitors.

Strengths and weaknesses:

(1) The main model utilized was engineered from the KOLF2 human iPSC line into an elegant LMX1A-reporter line based on the expression of BFP. This results in an attractive model for studies tracing the fate of LMX1A cells. However, consideration should be given to the fact that the parental line, exhibits a splice disruption in the COL3A1 gene encoding type III collagen (Pantazis 2022, doi:10.1016/j.stem.2022.11.004 ), which has been identified as being enriched in certain ventral astrocytic populations (Bradley 2019, doi:10.1242/dev.170910).

(2) The authors argue that the depletion of BFP seen in the unsorted population immediately after the onset of astrogenic induction is due to the growth advantage of the derivatives of the residual LMX1A- population. However, no objective data supporting this idea is provided, and one could also hypothesize that the residual LMX1A- cells could affect the overall LMX1A expression in the culture through negative paracrine regulation. Therefore, cell cycle or proliferation studies of these cells are needed to prove the authors' assumption. Furthermore, on line 124 it is stated that: "Interestingly, the sorted BFP+ cells exhibited similar population growth rate to that of unsorted cultures...". In the face of the suggested growth disadvantage of those cells, this statement needs clarification.

(3) Regarding the fidelity of the model system, it is not clear to me how the TagBFP expression was detected in the BFP+ population supposedly in d87 and d136 pooled astrocytes (Fig S6C) while no LMX1A expression was observed in the same cells (Fig S6F).

(4) The generated single-cell RNASeq dataset is extremely valuable. However, given the number of conditions included in this study (i.e. early vs late astrocytes, BFP+ vs BFP-, sorted vs unsorted, plus non-patterned and neuronal samples) the resulting analysis lacks detail. For instance, from a developmental perspective and to better grasp the functional significance of astrocytic heterogeneity, it would be interesting to map the identified clusters to early vs late populations and to the BFP status. Moreover, although comprehensive, Figure S7 is complex to understand given that citations rather than the reference populations are depicted.

(5) Do the authors have any consideration regarding the morphology of the astrocytes obtained in this study? None of the late astrocyte images depict a prototypical stellate morphology, which is reported in many other studies involving the generation of iPSC-derived astrocytes and which is associated with the maturity status of the cell.

Author response:

(1) Rationale of the study and key finding

We respectively disagree with Reviewer #1’s comments on ‘the fundamental weakness of this paper … about regional identity ...’. We believe that they misunderstood the rationale and key message of the paper.

The rationale of the study stems from the increasing recognition of the importance of generating ‘regional-specific’ astrocytes from iPSCs for disease modelling, due to astrocyte heterogeneity and their region-specific involvement in disease pathology. Regional astrocytes are typically differentiated from neural progenitors (NPCs) that are ‘patterned’ to the desired fate during iPSC neural induction. While the efficiency is not 100%, it is nevertheless assumed that the initial lineage composition (%) of patterned NPCs is preserved during the course of astrocyte differentiation and hence that the derived astrocytes represent the intended regional fate.

We questioned this approach using genetic lineage tracing with ventral midbrain-patterned neural progenitors as an example. By monitoring astrocytic induction of purified BFP+ NPCs and unsorted ventral midbrain-patterned NPC (referred to as BFP- in the paper, line 154 submitted PDF), we demonstrate that despite BFP+ NPCs being the vast majority (>90% LMX1A+ and FOXA2+) at the onset of astrocytic induction, their derivatives were lost in the final astrocyte product unless BFP+ NPCs were purified prior to astrocytic induction and differentiation. 

Our findings demonstrate that iPSC-derived astrocytes may not faithfully represent the antecedent neural progenitor pool in terms of lineage, and that the regionality of PSC-derived astrocytes should not be assumed based on the (dominant) NPC identity. We believe that this finding is important for iPSC disease modelling research, especially where disease pathophysiology concerns astrocytes of specific brain regions.

Reviewer #1 raised several interesting questions concerning floor plate marker expression during astrocytic induction and astrocyte differentiation in normal development. These are important outstanding questions in developmental neurobiology, but they are outside the scope of this in vitro study. Indeed, the approach taken by published PSC-astrocyte studies - such as assigning regional identity of PSC-derived astrocytes based on the starting NPC fate or validating PSC-astrocyte using regional markers defined in the developing embryo - is partly due to our limited knowledge about the developing and mature astrocytes in different brain regions. This knowledge gap consequently restricts a thorough characterisation of the regional identity of PSC-astrocytes in such cases.

(2) LMX1A expression in the brain and LMX1A-BFP lineage tracer line

We thank Reviewer #1 for highlighting the wider expression of LMX1A. We are fully aware of this consideration and hence the thorough examination of PSC-derived ventral midbrain-patterned NPCs by immunostaining and single cell RNA-sequencing in this and a previous study (PMID: 38132179). All LMX1A+ cells produced in our protocol exhibit ventral midbrain progenitor gene expression profiles when compared to dataset obtained from human fetal ventral midbrain.

Some of the comments give us the impression that there might be some confusion regarding the lineage tracing system used in this study. The LMX1A-Cre/AAVS1-BFP line is not a classic reporter line that mark LMX1A-expressing cells in real time. Instead, it was designed as a tracer line that expresses BFP in the derivatives of LMX1A+ cells as well as cells expressing LMX1A at the time of analysis.  

(3) Is regional identity fixed?

We feel that Reviewer #1 misunderstood the paper in their comments ‘The authors are making an assumption that regional identity is fixed when they begin their astrocyte differentiation protocol - not necessarily true…’.  We in fact pointed out in the paper that expression of LMX1A and FOXA2, a signature of midbrain floor plate progenitors, is lost in our BFP+ astrocytes. In this paper, ‘regional identity’ was loosely used to also refer to lineage identity and genetic traits, not just gene expression. We will consider alternative wording during revision to avoid potential confusion.  

(4) Splice disruption in the COL3A1 gene and potential effect on astrocyte differentiation of Kolf2 iPSCs

We thank Reviewer #2 for highlighting the variations in KOLF2C1 hiPSCs and the study by Bradley et al. (2019) on differential COL3A1 expression in some ventral astrocytes. We noted that the progenitors produced by Bradley et al. were NKX2.1+ ventral forebrain cells, rather than the LMX1A+ ventral midbrain progenitors investigated in our study. Our scRNAseq data show that all three populations of astrocytes exhibit low levels of COL3A1 expression. While we will continue to examine astrocyte COL3A1 expression in publicly available gene expression datasets, we feel that a selective impairment in astrocyte differentiation of BFP+ cells is unlikely.

(5) Additional data analysis and validation of potential new markers

We will carefully consider the reviewers’ suggestions on further analysis of our single-cell RNA sequencing dada during revision. Regarding eLife’s assessment of validating differential gene expression in different brain regions, it is worth noting that both BFP+ and BFP- cells mapped to the published midbrain scRNAseq data set (La Manno et al, Cell 2016, PMID: 27716510), supporting their midbrain fate. We agree in principle that all single-cell RNA sequencing findings should be validated by immunostaining. It would be beneficial to experimentally verify that our candidate BFP+ differentially expressed genes indeed mark astrocytes derived from LMX1A+ NPCs in vivo, as opposed to other midbrain NPCs. However, this verification cannot be realistically performed in a human setting, but only in an analogous mouse tracer line.

The current eLife assessment nicely summarised part of our findings, in a sense secondary output of this work. We would appreciate a revised eLife assessment that include the message that iPSC-derived astrocytes, in terms of genetic lineage, can deviate greatly from the starting progenitor pool.  We would be very happy to provide further information or clarification if it would be helpful. We are committed to doing our best as authors to enhance reader experience and support the continued success of eLife.

eLife assessment

In this valuable study, García-Vázquez et al. provide solid evidence suggesting that G2 and S phases expressed protein 1 (GTSE1), is a previously unappreciated non-pocket substrate of cyclin D1-CDK4/6 kinases. To this end, this study holds a promise to significantly contribute to an improved understanding of the mechanisms underpinning cell cycle progression. Notwithstanding these clear strengths of the article, it was thought that the study may benefit from establishing the precise role of cyclin D1-CDK4/6 kinase-dependent GTSE1 phosphorylation in the context of cell cycle progression, obtaining more direct evidence that cyclin D1-CDK4/6 kinase phosphorylate indicated sites on GTSE1 (e.g., S454) and mapping a degron in GTSE1 whose function may be blocked by cyclin D1-CDK4/6 kinase-dependent phosphorylation.

Reviewer #1 (Public review):

Summary:

García-Vázquez et al. identify GTSE1 as a novel target of the cyclin D1-CDK4/6 kinases. The authors show that GTSE1 is phosphorylated at four distinct serine residues and that this phosphorylation stabilizes GTSE1 protein levels to promote proliferation.

Strengths:

The authors support their findings with several previously published results, including databases. In addition, the authors perform a wide range of experiments to support their findings.

Weaknesses:

I feel that important controls and considerations in the context of the cell cycle are missing. Cyclin D1 overexpression, Palbociclib treatment and apparently also AMBRA1 depletion can lead to major changes in cell cycle distribution, which could strongly influence many of the observed effects on the cell cycle protein GTSE1. It is therefore important that the authors assess such changes and normalize their results accordingly.

Reviewer #2 (Public review):

Summary:

The manuscript by García-Vázquez et al identifies the G2 and S phases expressed protein 1(GTSE1) as a substrate of the CycD-CDK4/6 complex. CycD-CDK4/6 is a key regulator of the G1/S cell cycle restriction point, which commits cells to enter a new cell cycle. This kinase is also an important therapeutic cancer target by approved drugs including Palbocyclib. Identification of substrates of CycD-CDK4/6 can therefore provide insights into cell cycle regulation and the mechanism of action of cancer therapeutics. A previous study identified GTSE1 as a target of CycB-Cdk1 but this appears to be the first study to address the phosphorylation of the protein by Cdk4/6.

The authors identified GTSE1 by mining an existing proteomic dataset that is elevated in AMBRA1 knockout cells. The AMBRA1 complex normally targets D cyclins for degradation. From this list, they then identified proteins that contain a CDK4/6 consensus phosphorylation site and were responsive to treatment with Palbocyclib.

The authors show CycD-CDK4/6 overexpression induces a shift in GTSE1 on phostag gels that can be reversed by Palbocyclib. In vitro kinase assays also showed phosphorylation by CDK4. The phosphorylation sites were then identified by mutagenizing the predicted sites and phostag got to see which eliminated the shift.

The authors go on to show that phosphorylation of GTSE1 affects the steady state level of the protein. Moreover, they show that expression and phosphorylation of GTSE1 confer a growth advantage on tumor cells and correlate with poor prognosis in patients.

Strengths:

The biochemical and mutagenesis evidence presented convincingly show that the GTSE1 protein is indeed a target of the CycD-CDK4 kinase. The follow-up experiments begin to show that the phosphorylation state of the protein affects function and has an impact on patient outcomes.

Weaknesses:

It is not clear at which stage in the cell cycle GTSE1 is being phosphorylated and how this is affecting the cell cycle. Considering that the protein is also phosphorylated during mitosis by CycB-Cdk1, it is unclear which phosphorylation events may be regulating the protein.

Reviewer #3 (Public review):

Summary:

This paper identifies GTSE1 as a potential substrate of cyclin D1-CDK4/6 and shows that GTSE1 correlates with cancer prognosis, probably through an effect on cell proliferation. The main problem is that the phosphorylation analysis relies on the over-expression of cyclin D1. It is unclear if the endogenous cyclin D1 is responsible for any phosphorylation of GTSE1 in vivo, and what, if anything, this moderate amount of GTSE1 phosphorylation does to drive proliferation.

Strengths:

There are few bonafide cyclin D1-Cdk4/6 substrates identified to be important in vivo so GTSE1 represents a potentially important finding for the field. Currently, the only cyclin D1 substrates involved in proliferation are the Rb family proteins.

Weaknesses:

The main weakness is that it is unclear if the endogenous cyclin D1 is responsible for phosphorylating GTSE1 in the G1 phase. For example, in Figure 2G there doesn't seem to be a higher band in the phos-tag gel in the early time points for the parental cells. This experiment could be redone with the addition of palbociclib to the parental to see if there is a reduction in GTSE1 phosphorylation and an increase in the amount in the G1 phase as predicted by the authors' model.

The experiments involving palbociclib do not disentangle cell cycle effects. Adding Cdk4 inhibitors will progressively arrest more and more cells in the G1 phase and so there will be a reduction not just in Cdk4 activity but also in Cdk2 and Cdk1 activity. More experiments, like the serum starvation/release in Figure 2G, with synchronized populations of cells would be needed to disentangle the cell cycle effects of palbociclib treatment.

It is unclear if GTSE1 drives the G1/S transition. Presumably, this is part of the authors' model and should be tested.

The proliferation assays need to be more quantitative. Figure 4B should be plotted on a log scale so that the slope can be used to infer the proliferation rate of an exponentially increasing population of cells. Figure 4c should be done with more replicates and error analysis since the effects shown in the lower right-hand panel are modest.

Author response:

Reviewer #1:

Summary:

García-Vázquez et al. identify GTSE1 as a novel target of the cyclin D1-CDK4/6 kinases. The authors show that GTSE1 is phosphorylated at four distinct serine residues and that this phosphorylation stabilizes GTSE1 protein levels to promote proliferation.

Strengths:

The authors support their Kindings with several previously published results, including databases. In addition, the authors perform a wide range of experiments to support their Kindings.

Weaknesses:

I feel that important controls and considerations in the context of the cell cycle are missing. Cyclin D1 overexpression, Palbociclib treatment and apparently also AMBRA1 depletion can lead to major changes in cell cycle distribution, which could strongly inKluence many of the observed effects on the cell cycle protein GTSE1. It is therefore important that the authors assess such changes and normalize their results accordingly.

We have approached the question of GTSE1 phosphorylation to account for potential cell cycle effects from multiple angles:  

(i) We conducted in vitro experiments with puriIied, recombinant proteins and shown that GTSE1 is phosphorylated by cyclin D1-CDK4 in a cell-free system (Figure 2A-C). This experiment provides direct evidence of GTSE1 phosphorylation by cyclin D1-CDK4 without the inIluence of any other cell cycle effectors.  

(ii) We present data using synchronized AMBRA1 KO cells (Figure 2G and Supplementary Figure 3B).  As shown previously (Simoneschi et al., Nature 2021, PMC8875297), AMBRA1 KO cells progress faster in the cell cycle but they are still synchronized as shown, for example by the mitotic phosphorylation of Histone H3. Under these conditions we observed that while phosphorylation of GTSE1 in parental cells peaks at the G2/M transition, AMBRA1 KO cells exhibited sustained phosphorylation of GTSE1 across all cell cycle phases.  This is evident when using Phos-tag gels as in the current top panel of Figure 2G. We now re-run one the biological triplicates of the synchronized cells using higher concentration of Zn+2-Phos-tag reagent and lower voltage to allow better separation.  Under these conditions, GTSE1 phosphorylation is more apparent. In the new version of the paper, we will either show both blots or substitute the old panel with the new one. This experiment provides evidence that high levels of cyclin D1 in AMBRA1 KO cells affect GTSE1 independently of the speciIic points in the cell cycle.  

(iii) The relative short half-life of GTSE1 (<4 hours) makes its levels sensitive to acute treatments such as Palbococlib or AMBRA1 depletion. The effects of these treatments on GTSE1 levels are measurable within a time frame too short to affect cell cycle progression in a meaningful way. For example, we used cells with fusion of endogenous AMBRA1 to a mini-Auxin Inducible Degron (mAID) at the N-terminus. This system allows for rapid and inducible degradation of AMBRA1 upon addition of auxin, thereby minimizing compensatory cellular rewiring. Again, we observed an increase in GTSE1 levels upon acute ablation of AMBRA1 (i.e., in 8 hours) (Figure 3B), when no signiIicant effects on cell cycle distribution are observed (please see Simoneschi et al., Nature 2021, PMC8875297 and Rona et al., Mol. Cell 2024, PMC10997477). 

All together, these lines of evidence support our conclusion that GTSE1 is a target of cyclin D1-CDK4, independent of cell cycle effects. In conclusion, as stated in the Discussion section, GTSE1 has been established as a substrate of mitotic cyclins, but we observed that overexpression of cyclin D1-CDK4 induce GTSE1 phosphorylation at any point of the cell cycle. Thus, we propose that GTSE1 is phosphorylated by CDK4 and CDK6 particularly in pathological states, such as cancers displaying overexpression of D-type cyclins beyond the G1 phase. In turn, GTSE1 phosphorylation induces its stabilization, leading to increased levels that, as expected based on the existing literature, contribute to enhanced cell proliferation. So, the cyclin D1-CDK4/6 kinase-dependent phosphorylation of GTSE1 induces its stabilization independently of the cell cycle.  

Reviewer #2:

Summary:

The manuscript by García-Vázquez et al identifies the G2 and S phases expressed protein

1(GTSE1) as a substrate of the CycD-CDK4/6 complex. CycD-CDK4/6 is a key regulator of the G1/S cell cycle restriction point, which commits cells to enter a new cell cycle. This kinase is also an important therapeutic cancer target by approved drugs including Palbocyclib. Identification of substrates of CycD-CDK4/6 can therefore provide insights into cell cycle regulation and the mechanism of action of cancer therapeutics. A previous study identified GTSE1 as a target of CycB-Cdk1 but this appears to be the first study to address the phosphorylation of the protein by Cdk4/6.

The authors identified GTSE1 by mining an existing proteomic dataset that is elevated in AMBRA1 knockout cells. The AMBRA1 complex normally targets D cyclins for degradation. From this list, they then identified proteins that contain a CDK4/6 consensus phosphorylation site and were responsive to treatment with Palbocyclib. 

The authors show CycD-CDK4/6 overexpression induces a shift in GTSE1 on phostag gels that can be reversed by Palbocyclib. In vitro kinase assays also showed phosphorylation by CDK4. The phosphorylation sites were then identified by mutagenizing the predicted sites and phostag got to see which eliminated the shift. 

The authors go on to show that phosphorylation of GTSE1 affects the steady state level of the protein. Moreover, they show that expression and phosphorylation of GTSE1 confer a growth advantage on tumor cells and correlate with poor prognosis in patients.

Strengths:

The biochemical and mutagenesis evidence presented convincingly show that the GTSE1 protein is indeed a target of the CycD-CDK4 kinase. The follow-up experiments begin to show that the phosphorylation state of the protein affects function and has an impact on patient outcomes. 

Weaknesses:

It is not clear at which stage in the cell cycle GTSE1 is being phosphorylated and how this is affecting the cell cycle. Considering that the protein is also phosphorylated during mitosis by CycB-Cdk1, it is unclear which phosphorylation events may be regulating the protein.

In cells that do not overexpress cyclin D1, GTSE1 is phosphorylated at the G2/M transition, consistent with the known cyclin B1-CDK1-mediated phosphorylation of this protein. However, AMBRA1 KO cells exhibited high levels of cyclin D1 throughout the cell cycle and sustained phosphorylation of GTSE1 across all cell cycle points (Figure 2G and Supplementary Figure 3B). Please see also answer to Reviewer #1.  Moreover, we show that, compared to the amino acids phosphorylated by cyclin D1-CDK4, cyclin B1-CDK1 phosphorylates GTSE1 on either additional residues or different sites (Figure 2H). Finally, we show that expression of a phospho-mimicking GTSE1 mutant leads to accelerated growth and an increase in the cell proliferative index (Figure 4C).  However, we have not evaluated how phosphorylation affects the cell cycle distribution.  We will perform FACS analyses and include them in the new version. 

Reviewer #3:

Summary:

This paper identifies GTSE1 as a potential substrate of cyclin D1-CDK4/6 and shows that GTSE1 correlates with cancer prognosis, probably through an effect on cell proliferation. The main problem is that the phosphorylation analysis relies on the over-expression of cyclin D1. It is unclear if the endogenous cyclin D1 is responsible for any phosphorylation of GTSE1 in vivo, and what, if anything, this moderate amount of GTSE1 phosphorylation does to drive proliferation.

Strengths: 

There are few bonafide cyclin D1-Cdk4/6 substrates identified to be important in vivo so GTSE1 represents a potentially important finding for the field. Currently, the only cyclin D1 substrates involved in proliferation are the Rb family proteins.

Weaknesses:

The main weakness is that it is unclear if the endogenous cyclin D1 is responsible for phosphorylating GTSE1 in the G1 phase. For example, in Figure 2G there doesn't seem to be a higher band in the phos-tag gel in the early time points for the parental cells. This experiment could be redone with the addition of palbociclib to the parental to see if there is a reduction in GTSE1 phosphorylation and an increase in the amount in the G1 phase as predicted by the authors' model. The experiments involving palbociclib do not disentangle cell cycle effects. Adding Cdk4 inhibitors will progressively arrest more and more cells in the G1 phase and so there will be a reduction not just in Cdk4 activity but also in Cdk2 and Cdk1 activity. More experiments, like the serum starvation/release in Figure 2G, with synchronized populations of cells would be needed to disentangle the cell cycle effects of palbociclib treatment.    

In normal cells, GTSE1 is phosphorylated at the G2/M transition in a cyclin B1-CDK1dependent manner.  During G1, when the levels of cyclin D1 peak, GTSE1 is not phosphorylated. This could be due to a higher affinity between GTSE1 and mitotic cyclins as compared to G1 cyclins or to a higher concentration of mitotic cyclins compared to G1 cyclins.  We show that higher levels of cyclin D1 induce GTSE1 phosphorylation during interphase, but we do not rely only on the overexpression of exogenous cyclin D1. In fact, we observe similar effect when we deplete endogenous AMBRA1, resulting in the stabilization of endogenous cyclin D1.  As mentioned in the Discussion section, we propose that GTSE1 is phosphorylated by CDK4 and CDK6 particularly in pathological states, such as cancers displaying overexpression of D-type cyclins (i.e., the overexpression appears to overcome the lower afIinity of the cyclin D1-GTSE1 complex). In sum, our study suggests that overexpression of cyclin D1, which is often observed in cancers cells beyond the G1 phase, induces phosphorylation of GTSE1 at all points in the cell cycle displaying high levels of cyclin D1.  Please see also response to Reviewer #1.  Concerning the experiments involving palbociclib, we limited confounding effects on the cell cycle by treating cells with palbociclib for only 4-6 hours. Under these conditions, there is simply not enough time for the cells to arrest in G1.

It is unclear if GTSE1 drives the G1/S transition. Presumably, this is part of the authors' model and should be tested.

We are not claiming that GTSE1 drives the G1/S transition.  GTSE1 is known to promote cell proliferation, but how it performs this task is not well understood.  Our experiments indicate that, when overexpressed, cyclin D1 promotes GTSE1 phosphorylation and its consequent stabilization.  In agreement with the literature, we show that higher levels of GTSE1 promote cell proliferation.  To measure cell cycle distribution upon expressing various forms of GTSE1, we will now perform FACS analyses and include them in the new version. 

The proliferation assays need to be more quantitative. Figure 4B should be plotted on a log scale so that the slope can be used to infer the proliferation rate of an exponentially increasing population of cells. Figure 4c should be done with more replicates and error analysis since the effects shown in the lower right-hand panel are modest.

In Figure 4B, we plotted data in a linear scale as done in the past (Donato et al. Nature Cell Biol. 2017, PMC5376241) to better represent the changes in total cell number overtime.  The experiments in Figure 4C were performed in triplicate. Error analysis was not included for simplicity, given the complexity of the data. We will include the other two sets of experiments in the revised version.  While the effects shown in the lower right-hand panel of Figure 4C are modest, they demonstrate the same trend as those observed in the AMBRA KO cells (Figure 4C and Simoneschi et al., Nature 2021, PMC8875297). It's important to note that this effect is achieved through the stable expression of a single phosphomimicking protein, whereas AMBRA KO cells exhibit changes in numerous cell cycle regulators.

We appreciate the constructive comments and suggestions made by the reviewers, and we believe that the resulting additions and changes will improve the clarity and message of our study.

Author response:

Reviewer #1 (Public Review):

(1) All the figure legends need to expand significantly, so it is clear what is being presented. All experiments showing data quantification need the numbers of independent biological replicates to be added, plus an indication of what the P-values are associated with the asterisks (and the tests used).

Thank you for your valuable suggestions. We will significantly expand the figure legends to provide a clear and detailed description of the data presented in each figure. Additionally, we will include dot plots in the bar graphs to illustrate the number of independent biological replicates for each experiment. Furthermore, we will specify the statistical tests used for each analysis and include the corresponding P-values associated with the asterisks in the figure legends.

(2) All the Related to point 1, the description of the data in the text needs to expand significantly, so the figure panels are interpretable. Examples are given below but this is not an exhaustive list.

We appreciate your feedback on the clarity of the data description in the text. In response to your suggestion, we will significantly expand the descriptions throughout the manuscript to ensure that each figure panel is fully interpretable. The revised text will provide a more detailed and comprehensive explanation of the data presented.

(3) All the The addition of "super-enhancer-driven" to the title is a distraction. This is the starting point but the finding is portrayed by the last part of the title. Moreover, it is not clear why this is a super enhancer rather than just a typical enhancer as only one seems to be relevant and functional. I suggest avoiding this term after initial characterisations.

Thank you for your thoughtful comment. In this study, the key molecule ZFP36L1 was identified as a target gene through the characterization of the super-enhancer ZFP36L1-SE. The enrichment of H3K27ac at this site meets the threshold defined by the ROSE algorithm, and transcription of ZFP36L1 is regulated by BRD4, making it susceptible to inhibition by the super-enhancer inhibitor JQ1. Although we were unable to directly observe the effects of knocking out the ZFP36L1-SE via Cas9 due to experimental constraints, we believe that the indirect evidence we have gathered is sufficient to demonstrate the super-enhancer's driving role. This approach is consistent with the conventions of previous studies on super-enhancers.

(4) The descriptions of Figures 1B, C, and D are very poor. How for example do you go from nearly 2000 SE peaks to a couple of hundred target genes? What are the other 90% doing? What is the definition of a target gene? This whole start section needs a complete overhaul to make it understandable and this is important as is what leads us to ZFP36L1 in the first place.

We appreciate your feedback and apologize for the confusion caused by the initial descriptions. As described in the manuscript, the function of SE peaks depends on their location. Figure 1C shows the distribution of these peaks, where "Over 50% of these peaks were located in the non-coding regions such as exons and introns, and their predicted target genes were transcribed to produce non-coding RNAs; the peaks distributed in transcription start and termination sites activated the promoters and directly drove the transcription of protein-coding genes". Our research focuses on protein-coding genes, and we apologize for any misunderstanding due to the inadequate description. We will provide additional clarification to make this distinction clear.

(5) It is impossible to work out what Figures 1F, H, and I are from the accompanying text. The same applies to supplementary Figure S1D. Figure 1G is not described in the results.

Thank you for pointing out these issues. We will make the necessary revisions to provide additional explanations for Figures 1F, H, I, G, and supplementary Figure S1D.

(6) What is Figure 2A? There is no axis label or description.

Thank you for bringing this to our attention. We will add the missing axis labels and provide a detailed description for Figure 2A to ensure clarity and accurate interpretation.

(7) Why is CD274 discussed in the text from Figure 2E but none of the other genes? The rationale needs expanding.

CD274 (also known as PD-L1) is a key focus of our subsequent research. The other immune checkpoints are not expressed on tumor cells but rather on immune cells. We will provide additional explanation in the text to clarify this distinction.

(8) Figure 2G needs zooming in more over the putative SE region and the two enhancers labelling. This looks very strange at the moment and does not show typical peak shapes for histone acetylation at enhancers.

We appreciate your feedback. Our intention with Figure 2G was to present the position of ZFP36L1-SE at a macro level rather than focusing on specific details. This broader view is meant to provide context for the SE region in relation to the surrounding genomic landscape.

(9) The use of JQ1 does not prove something is a super enhancer, just that it is BRD4 regulated and might be a typical enhancer.

Thank you for your comment. The role of JQ1 as a super-enhancer inhibitor has been widely reported and recognized in the literature. Its use in experimental studies targeting super-enhancers is a well-established practice. We acknowledge that while JQ1 inhibition indicates BRD4 regulation, it is consistent with the identification of super-enhancers as well.

(10) An explanation of how the motifs were identified in E1 is needed. Enrichment over what? Were they purposefully looking for multiple motifs per enhancer? Otherwise what it all comes down to later in the figure is a single motif, and how can that be "enriched"?

Thank you for your feedback. We used the MEME-ChIP online tool for motif identification, which is a widely recognized method in transcription factor research. MEME-ChIP applies established algorithms to identify known motifs within DNA sequences. For detailed information on the tool's working principles and algorithms, please refer to the reference provided and the URL included in the Materials and Methods section of our manuscript. MEME-ChIP: https://meme-suite.org/meme/tools/meme.

(11) A major missing experiment is to deplete rather than over-express SPI1 for the various assays in Figure 4.

We apologize for this oversight and acknowledge that the depletion of SPI1, in addition to over-expression, would have provided a more comprehensive analysis. Due to experimental constraints, we are unable to include this depletion experiment in the current study. We appreciate your understanding and will consider this suggestion for future research.

(12) The authors start jumping around cell lines, sometimes with little justification. Why is MGC803 used in Figure 4I rather than MKN45? This might be due to more endogenous SPI1. However, this does not make sense in Figure 5M, where ZFP36L is overexpressed in this line rather than MKN45. If SPI1 is already high in MGC803, then the prediction is that ZFP36L1 should already be high. Is this the case?

Thank you for your feedback. We want to clarify that we are not arbitrarily jumping between cell lines. Each experiment was validated in two different cell lines. We aimed to present representative results within the constraints of the manuscript, but if more detailed results from additional cell lines are needed, we can provide them upon request. Regarding your concern, results from the MKN45 cell line are consistent with those observed in MGC803, and these findings are not influenced by SPI1 or ZFP36L1 expression levels.

(13) In Figure 5, HDAC3 should also be depleted to show opposite effects to over-expression (as the latter could be artefactual). Also, direct involvement should be proven by ChIP.

We appreciate your feedback. We acknowledge that depleting HDAC3, in addition to overexpressing it, would provide a more comprehensive analysis. Unfortunately, due to experimental constraints, we are unable to include this depletion experiment in the current study. We recognize these limitations and appreciate your understanding. We will consider these aspects for future research. Additionally, we would like to clarify that HDAC3 is a histone deacetylase and not a transcription factor, so it does not directly bind to DNA and therefore is not suitable for ChIP analysis.

(14) Figure 5G and H are not discussed in the text.

Thank you for pointing this out. We will include a discussion of Figures 5G and H in the revised manuscript. The additional details should provide the necessary context and interpretation for these figures.

(15) Figure 6C needs explaining. Why are three patients selected here? Are these supposed to be illustrative of the whole cohort? What sub-type of GC are these?

Thank you for your comment. The three patients with infiltrative GC shown in Figure 6C were selected as representative images based on prior reviewer suggestions.

(16) Figure 6E onwards, they switch to MFC cell line. They provide a rationale but the key regulatory axis should be sown to also be operational in these cells to use this as a model system.

Thank you for your comment. We would like to clarify that we used the MC38 cell line, which is a colon cancer cell line, rather than MFC. Our focus was on demonstrating the role of ZFP36L1 in vivo, rather than specifically discussing the regulatory axis in this context. We chose MC38 cells instead of MFC cells due to practical considerations. Specifically, MFC cells were shown in our experiments to be unable to form tumors in wild-type mice, despite previous reports suggesting their tumorigenicity. We will provide a rationale for this choice in the manuscript. We acknowledge that validating the entire regulatory axis in the MC38 cell line would enhance the study's depth. However, due to experimental constraints, we are unable to complete this additional validation. We appreciate your understanding and will consider this aspect for future research.

Reviewer #2( Public Review):

(17) The difference in H3K27ac over the ZFP36L1 locus and SE between the expanding and infiltrative GC is marginal (Figure 2G). Although the authors establish that ZFP36L1 is upregulated in GC, particularly in the infiltrative subtype, no direct proof is provided that the identified SE is the source of this observation. CRISPR-Cas9 should be employed to delete the identified SE to prove that it is causatively linked to the expression of ZFP36L1.

Thank you for your thoughtful comment. In this study, the key molecule ZFP36L1 was identified as a target gene through the characterization of the super-enhancer ZFP36L1-SE. The enrichment of H3K27ac at this site meets the threshold defined by the ROSE algorithm, and transcription of ZFP36L1 is regulated by BRD4, making it susceptible to inhibition by the super-enhancer inhibitor JQ1. Although we were unable to directly observe the effects of knocking out the ZFP36L1-SE via Cas9 due to experimental constraints, we believe that the indirect evidence we have gathered is sufficient to demonstrate the super-enhancer's driving role. This approach is consistent with the conventions of previous studies on super-enhancers.

(18) In Figure 3C the impact of shZFP36L1 on PD-L1 expression is marginal and it is observed in the context of IFNg stimulation. Moreover, in XGC-1 cell line the shZFP36L1 failed to knock down protein expression thus the small decrease in PD-L1 level is likely independent of ZFP36L1. The same is the case in Figure 3D where forced expression of ZFP36L1 does not upregulate the expression of PDL1 and even in the context of IFNg stimulation the effect is marginal.

Thank you for your detailed observations. In our study, the regulatory effect of ZFP36L1 on PD-L1 was validated at the mRNA level, protein level, and through flow cytometry, with each experiment being repeated multiple times. The results of the Western blot were quantitatively assessed using densitometry rather than relying solely on visual inspection. It is important to note that interferon-gamma (IFNγ) stimulation significantly enhances PD-L1 expression, which under the same exposure conditions, may make the baseline expression of PD-L1 appear unchanged. This could explain the marginal effect observed under IFNγ stimulation.

(19) In Figure 4, it is unclear why ELF1 and E2F1 that bind ZFP36L1-SE do not upregulate its expression and only SPI1 does. In Figure 4D the impact of SPI overexpression on ZFP36L1 in MKN45 cells is marginal. Likewise, the forced expression of SPI did not upregulate PD-L1 which contradicts the model. Only in the context of IFNg PD-L1 is expressed suggesting that whatever role, if any, ZFP36L1-SPI1 axis plays is secondary.

Thank you for your insightful comments. First, ELF1, E2F1, and SPI1 were predicted transcription factors, and experimental validation is crucial. Our results specifically demonstrate that only SPI1 binds to ZFP36L1-SE, while ELF1 and E2F1 do not, confirming the specificity of SPI1. Second, Second, as mentioned in point (18), experimental results, such as those from western blot, should not be evaluated by eye alone. Our findings are quantitatively assessed, and the regulatory relationships have been confirmed through repeated experiments. This finding is supported by multiple experimental validations, including mRNA, protein, and flow cytometry analyses. Furthermore, using IFNγ to study the regulation of PD-L1 is a common and widely accepted approach in this field. Many studies adopt this model, and it should not be concluded that the axis is secondary simply because PD-L1 expression is observed primarily under IFNγ stimulation. Similarly, other popular research areas, such as ferroptosis and autophagy, also use specific inducers, but this does not diminish the significance of the pathways being studied.

(20) The data presented in Figure 6 are not convincing. First, there is no difference in the tumor growth (Figure 6E). IHC in Figure 6I for CD8a is misleading. Can the authors provide insets to point CD8a cells? This figure also needs quantification and review from a pathologist.

Regarding this observation, we will provide an explanation in the discussion section: "Several studies have proposed that reducing PD-L1 expression enhances the tumor-killing effect of cytotoxic T lymphocytes in vitro and reduces primary tumor foci in vivo. Conversely, findings from this study suggest that PD-L1 expression is associated with immune evasion in metastatic foci." We are unsure why those studies concluded that PD-L1 expression levels would impact the size of the primary tumor. We are more inclined to support the perspective of John et al.Klement JD, Redd PS, Lu C, et al. Tumor PD-L1 engages myeloid PD-1 to suppress type I interferon to impair cytotoxic T lymphocyte recruitment. Cancer Cell. 2023;41(3):620-636.e9. doi:10.1016/j.ccell.2023.02.005

Reviewer #1 (Recommendations For The Authors):

(21) Supplementary Figure 1 lacks a legend.

We will add the legend for Supplementary Figure 1.

(22) Figure 1E, data from "expanding" GC samples is not discussed.

We will add a discussion of the "expanding" GC samples in the manuscript.

(23) How are "high" and "low" defined in Figure 2A, right?

Thank you for your question. In Figure 2A, the "high" and "low" categories on the x-axis are derived from the Friends analysis. This analysis is designed to compare the similarity between different genes or gene sets based on semantic similarity metrics from Gene Ontology (GO). The x-axis represents the semantic similarity score, which reflects how closely related the functions of the genes or gene sets are. This helps in identifying the most significant genes or those related to specific pathways or cell types of interest.

GOSemSim[2.22.0]

Yu G, Li F, Qin Y, Bo X, Wu Y, Wang S. GOSemSim: an R package for measuring semantic similarity among GO terms and gene products. Bioinformatics. 2010;26(7):976-978. doi:10.1093/bioinformatics/btq064

(24) Font sizes in multiple figures need to increase. For example, Figure 2C (but many other places).

The font sizes in the figures, including Figure 2C, will be increased as requested.

(25) Figure 4K assays TE activity, not SE as stated in the text.

SEs are composed of multiple TEs. ZFP36L1-E1 is a core element of the ZFP36L1-SE. Due to the excessive length of the ZFP36L1-SE sequence, it was not feasible to insert the entire SE into a dual-luciferase reporter plasmid. It is a common practice to validate such experiments by inserting the typical enhancer elements instead.

(26) In Figure 6I, why is CD8 shown? What is the reason for choosing this?

CD8α is primarily used to assess immune evasion by tumor cells against T-cell cytotoxicity. CD8α is typically negatively correlated with PD-L1 expression and serves as an indicator of T-cell infiltration.

(27) The discussion should be more focussed. The majority of this is general stuff about either super enhancers or PD-L1 regulation. This should be curtailed and more pertinent things retained.

We will revise the discussion to be more focused. The content will be streamlined to emphasize the most pertinent points related to our study.

Reviewer #2 (Recommendations For The Authors):

(28) In Figure 1H various immune cell populations differ between the two types of GC. Unclear what is the biological significance in the context of ZFP36L1.

The results in Figure 1H provide insight into the SE-driven immune escape signatures of infiltrative gastric cancer (GC). These findings help to contextualize the role of ZFP36L1 in modulating the tumor microenvironment, particularly in relation to immune cell infiltration and immune evasion mechanisms.

(29) A bivalent profile for H3K27ac is also observed in expanding gastric cancer (Figure 1B), not only in infiltrating GC as the authors claim.

We did not intend to imply that bivalent H3K27ac enrichment is exclusive to infiltrating gastric cancer. In fact, super-enhancers were identified in both expanding and infiltrative GC. Our point was to highlight that the bivalent enrichment profile is more pronounced in infiltrative GC.

(30) There is a typo in line 81.

The typo in line 81 will be corrected. Thank you for pointing it out.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The individual roles of both cosolvents and intrinsically disordered proteins (IDPs) in desiccation have been well established, but few studies have tried to elucidate how these two factors may contribute synergistically. The authors quantify the synergy for the model and true IDPs involved with desiccation and find that only the true IDPs have strong desiccation tolerance and synergy with cosolvents. Using these as model systems, they quantify the local (secondary structure vis-a-vi CD spectroscopy) and global dimensions (vis-a-vi the Rg of SAXS experiments) and find no obvious changes with the co-solvents. Instead, they focus on the gelation of one of the IDPs and, using theory and experiments, suggest that the co-solvents may enable desiccation tolerance, an interesting hypothesis to guide future in vivo desiccation studies. A few minor points that remain unclear to this reviewer are noted.

Strengths:

This paper is quite extensive and has significant strengths worth highlighting. Notably, the number and type of methods employed to study IDPs are quite unusual, employing CD spectroscopy, SAXS measurements, and DSC. The use of the TFE is an exciting integration of the physical chemistry of cosolvents into the desiccation field is a nice approach and a clever way of addressing the gap of the lack of conformational changes depending on the cosolvents. Furthermore, I think this is a major point and strength of the paper; the underlying synergy of cosolvents and IDPs may lie in the thermodynamics of the dehydration process.

Figure S6A is very useful. I encourage readers who are confused about the DSC analysis, interpretation, and calculation to refer to it.

Weaknesses:

Overall, the paper is sound and employs strong experimental design and analysis. However, I wish to point out a few minor weaknesses.

Perhaps the largest, in terms of reader comprehension, focuses on the transition between the model peptides and real IDPs in Figures 1 and 2. Notably, little is discussed with respect to the structure of the IDPs and what is known. Notably, I was confused to find out when looking at Table 1 that many of the IDPs are predicted to be largely unordered, which seemed to contrast with some of the CD spectroscopy data. I wonder if the disorder plots are misleading for readers. Can the authors comment more on this confusion? What are these IDPs structurally?

We apologize for the confusion caused here and thank the reviewer for this astute observation. Our CD spectroscopy data suggests all LEA proteins are almost entirely disordered under aqueous conditions, with a single major minimum at 200 nm, although most have a small inflection around 220 nm, indicating a small proportion of helicity (Fig. 3A). The notable exception here is CAHS D, which – in line with our work and the work of many others – possesses a substantial degree of transient helicity in the linker region (residues 100-200), giving rise to a more pronounced minimum at 220 nm. These conclusions are consistent with our SAXS data (Fig. 4), which predict a radius of gyration far larger than a globular folded protein of the same number of residues should have (15-20 Å). The structural predictions (both Metapredict and AlphaFold2), however, imply several of the proteins to be ordered; AvLEA1C and HeLEA68614 are both predicted to have large folded regions based on metapredict disorder scores. We believe this is an erroneous prediction driven by these regions' propensity to acquire helicity in the context of desiccation (Fig 3B) and/or when interacting with clients. As such, our computational analysis is at odds with the experimental data because these proteins are all poised to undergo a coil-to-helix transition, an effect our parallel work has proposed is important for their function (see Biswas et al. Prot. Sci. 2024). The ability of AlphaFold2 to predict bound-state or transient helices has been previously documented (Alderson et al PNAS 2023)

To address this discrepancy, the caption for Table 1 reads: “We note that the reason many of these profiles contain large folded regions is because the amphipathic LEA and CAHS proteins are predicted to form helices, which metapredict infers and incorrectly highlights these regions as ‘folded’ when really they are disordered in isolation”. We have also added additional context and information to the caption for Fig. S9 “We note that the structural predictions from AlphaFold2 contain largely ordered structures. We believe this is due to the propensity of these proteins to form helices in the context of drying or when interacting with a client. This has been shown in cases where an IDR contains residual helicity or is folded upon binding [70].”

Related to the above thoughts, the alpha fold structures for the LEA proteins are predicted (unconfidently) as being alpha-helical in contrast to the CD data. Does this complicate the TFE studies and eliminate the correlation for the LEA proteins?

AlphaFold2 predicted helicity in disordered regions is commonly observed, and thought to indicate a possible “bound” helical state (Alderson et al. PNAS 2023). As shown by the CD data, in aqueous conditions no secondary structure exists. It is only in the desiccated state - the path to which requires proteins to reach excessively high concentrations - that this secondary structure appears. Underlying our TFE model is that the AlphaFold2 predicted secondary structure is indicative of the state the proteins are in at high abundance, which occurs as cells ramp up protectant expression and as water is removed from the system. Under these assumptions, the CD data is in agreement with the AlphaFold2 predictions, and our analysis holds. This is explained in the methods under “Transfer Free Energy (TFE) Calculations” - but we have now also added an additional sentence to this effect in the main text: “Using a similar AlphaFold2-based approach for LEA proteins and for BSA, we can make correlations between the Gtr of the disorder-to-order transition and synergy (Fig. S8F-K). Interestingly, AlphaFold2 predictions of our LEA proteins were broadly helical, which is in contrast to our experimental characterization of these proteins in aqueous solutions. However, this is not unusual for AlphaFold2 predictions and could possibly represent a “bound” conformation for the proteins [70].”

Additionally, the notation that the LEA and BSA proteins do not correlate is unclear to this reviewer, aren't many of the correlations significant, having both a large R^2 and significant p-value?

We thank the reviewer for pointing this out. While BSA and some LEA proteins have values that correlate with synergy, there’s more to consider in assessing the relevance of these correlations. For example, we cannot claim that the value is physiologically relevant without observing an actual structural change in the protein. Furthermore, several of these proteins (BSA and AvLEA1C) were found to be not significantly synergistic in the LDH assay, and any correlation should, therefore, also be considered non-significant. We have added a sentence to the results to clarify this: “For a subset of these proteins, we see a statistically significant correlation between G and synergy. However, this data is purely computational. For CAHS D, we saw our predictions recapitulated in changes in the protein structure, and for the LEA proteins we do not. Thus, we conclude that cosolutes do not induce synergy in our LEA proteins through a change in folding.”

The calculation of synergy seems too simplistic or even problematic to me. While I am not familiar with the standards in the desiccation field, I think the approach as presented may be problematic due to the potential for higher initial values of protection to have lower synergies (two 50%s for example, could not yield higher than 100%).

We acknowledge the reviewer’s concern about our synergy calculation. We would like to highlight the use of sub-optimal protective concentrations in our synergy assays similar to studies previously reported in the desiccation field (Nguyen et al. 2022; Kim et al. 2018).

As the reviewer pointed out, we agree that there is a theoretical 100% threshold in our experiments which if we hit, we cannot distinguish between individual additive vs synergistic effects. To avoid the situation of reaching the near maximal protection levels (~100%), we intentionally select a sub-optimal concentration of the protectants that are below the maximum efficacy level for individual protectants to use in our assays. This limits the potential for initial higher values of the protectants so that their combined effect is not maximized, and there is always the potential for synergy. We would also like to point out that we never actually hit that 100% threshold in any of our synergy experiments, which warrants that any observed increase in protection is attributed to a true synergistic effect between the protectants.

Instead, I would think one would need to really think of it as an apparent equilibrium constant between functional and non-functional LDH (Kapp = [Func]/[Not Func] and frac = Kapp/(1+Kapp) or Kapp = frac/(1-frac) ) Then after getting the apparent equilibrium constants for the IDP and cosolvent (KappIDP and KappCS), the expected additive effect would be frac = (KappIDP+KappCS)/(1+KappIDP+KappCS).

Consequently, the extent of synergy could be instead calculated as KappBOTH-KappIDP-KappCS. Maybe this reviewer is misunderstanding. It is recommended that the authors clarify why the synergy calculation in the manuscript is reasonable.

We thank the reviewer for this suggestion. In the desiccation field, the synergy calculations that we used is the standard method that people use, so that’s what we present in our main manuscript. However, we have now quantified synergy through two new approaches: one, as suggested by the reviewer, using the equilibrium constant (Kapp) as a metric, and the other using the Bliss Independent model, which is a common approach for calculating synergy in drug combination studies. We see minimal differences in terms of the synergy scores using these different methods. We have included the results for these additional methods in supplemental figure S3.

Related to the above, the authors should discuss the utility of using molar concentration instead of volume fraction or mass concentration. Notably, when trehalose is used in concentration, the volume fraction of trehalose is much smaller compared to the IDPs used in Figure 2 or some in Figure 1. Would switching to a different weighted unit impact the results of the study, or is it robust to such (potentially) arbitrary units?

We thank the reviewer for this comment. Indeed, in studies of cosolute effect, concentration units can alter the conclusions of the study (Auton and Bolen 2004). In our case, the relevant figures where we use a concentration scale (1B and 2B) are not germane to the main conclusions: The only use of these PD50 values is to determine a sub-optimal concentration at which ~30% of the LDH is protected. While it is true that the number for the concentration of e.g., trehalose will be dramatically different if we were to use mass fraction units, the rest of the work and all our conclusions would be exactly the same.

Additionally, our use of a molar ratio when discussing synergy is a direct result of the way we think about such synergy: Since the concentration of both protein and cosolute can change by orders of magnitude during drying, it is the copy numbers of both proteins and cosolute that are conserved in this process, and it is this unit that we think is important to the protective effect (rather than the partial molar volume, for example, which would be changing as the system dries).

Reviewer #2 (Public Review):

Summary:

The paper aims to investigate the synergies between desiccation chaperones and small molecule cosolutes, and describe its mechanistic basis. The paper reports that IDP chaperones have stronger synergies with the cosolutes they coexist with, and in one case suggests that this is related to oligomerization propensity of the IDP.

Strengths:

The study uses a lot of orthogonal methods and the experiments are technically well done. They are addressing a new question that has not really been addressed previously.

Weaknesses:

The conclusions are based on a few examples and only partial correlations. While the data support mechanistic conclusions about the individual proteins studied, it is not clear that the conclusions can be generalized to the extent proposed by the authors due to small effect sizes, small numbers of proteins, and only partial correlations.

Thank you for bringing this up. We agree that we should not generalize our results to other systems based on the evidence we have for the proteins used in our study. We have altered our discussion to highlight that this may apply to other IDPs, and that future experiments must be done to support this: “Additionally, we want to point out that our results cannot necessarily be generalized to all desiccation-related IDPs. More experiments will be needed to assess the relevance of cosolute effects to functional synergy and IDP folding in the context of desiccation and beyond. This remains an important future direction for the field.”

The authors pose relevant questions and try to answer them through a systematic series of experiments that are all technically well-conducted. The data points are generally interpreted appropriately in isolation, however, I am a little concerned about a tendency to over-generalize their findings. Many of the experiments give negative or non-conclusive results (not a problem in itself), which means that the overall storyline is often based on single examples.

We agree with the reviewer’s point. As mentioned earlier, we have modified our manuscript to reflect that our findings are based on the six proteins that we studied, and we can only speculate about other desiccation-related IDPs based on our results.

For example, the central conclusion that IDPs interact synergistically with their endogenous co-solute (Figure 2E) is largely driven by one outlier from Arabidopsis. The rest are relatively close to the diagonal, and one could equally well suggest that the cosolutes affect the IDPs equally (which is also the conclusion in 1F).

We appreciate the reviewer’s concern regarding our conclusion in Figures 2E and 1F. We would like to highlight that our conclusions that IDPs interact synergistically with their endogenous cosolute are based on statistical analysis. Our data shows that full-length proteins that were synergistic with both cosolutes are always significantly more synergistic with the endogenous cosolute (Fig. 2E, Fig. S2C-E). For example, the nematode protein is synergistic with both trehalose and sucrose, but is significantly more synergistic with trehalose, the endogenous nematode cosolute, than with sucrose (Fig S2D).

This is not the case in 1F. In Fig. 1F, it is to note that not only are the points close to the diagonal, but most points are close to zero along both axes indicating no synergy. In fact, many points have negative synergy (antagonistic effect).

We do recognize that our conclusions are based on the study of a specific set of six IDPs, and we do not want to overreach in our conclusions. To acknowledge this, we have now added text to emphasize that our conclusion is based on the six proteins that we tested, and we speculate it might apply to other systems: “Our data shows that these six IDPs synergize best with their endogenous cosolute to promote desiccation tolerance and we speculate that this may apply to other desiccation-related IDPs”.

Similarly, the mechanistic explanations tend to be based on single examples. This is somewhat unavoidable as biophysical studies cannot be done on thousands of proteins, but the text should be toned down to reflect the strength of the conclusions.

We acknowledge the reviewer’s concern. We have modified our manuscript accordingly to reflect that the mechanistic insights we gained are for the six proteins we tested empirically. These changes can be found throughout the manuscript. None of our experiments rule out the possibility that other LEA proteins or CAHS proteins may show different structural transitions, or that other IDPs may take on structural changes in response to the cosolutes.

The central hypothesis revolves around the interplay between cosolutes and IDP chaperones comparing chaperones from species with different complements of cosolutes. In Table 1, it is mentioned that Arabidopsis uses both trehalose and sucrose as a cosolute, yet experiments are only done with either of these cosolutes and Arabidopsis is counted in the sucrose column. While it makes sense to compare them separately from a biophysical point of view, the ability to test the co-evolution of these systems is somewhat diminished by this. At least it should be discussed clearly.

We appreciate the reviewer’s comment. As is mentioned in Table 1, Arabidopsis uses both trehalose and sucrose as cosolute. As such, we would predict that the Arabidopsis proteins would respond positively to both cosolutes. We would like to point out that Arabidopsis is counted in both trehalose and sucrose columns.

We would also like to emphasize that multiple osmolytes exist in all organisms as a desiccation response and a simple IDP-cosolute system is far from a true recapitulation of a desiccating system. We have touched on this in the discussion and explicitly addressed the presence of both cosolutes in Arabidopsis and the need for further experiments to test for synergistic interactions using both or multiple mediators to illustrate synergy in multiple cosolute systems: “It is important to note that desiccation-tolerant organisms employ multiple cosolutes to counteract the effects of desiccation. The use of a single cosolute-IDP system in our in vitro experiments does not accurately mirror the diverse cosolute changes in desiccating systems. For instance, Arabidopsis seeds enrich both trehalose and sucrose, among other cosolutes. This demands the necessity of future experiments that incorporate both or multiple cosolutes and assess their synergistic effects, thus elucidating the intricate synergy in multi-cosolute systems.”

It would be helpful if the authors could spell out the theoretical basis of how they quantify synergy. I understand what they are doing - and maybe there are no better ways to do it - but it seems like an approach with limitations. The authors identify one in that the calculation only works far from 100%, but to me, it seems there would be an equally strict requirement to be significantly above 0%. This would suggest that it is used wrongly in Figure 6H, where there is no effect of betaine (at least as far as the color scheme allows one to distinguish the different bars). In this case, the authors cannot really conclude synergy or not, it could be a straight non-synergistic inhibition by betaine.

We appreciate the reviewer’s concern about the theoretical basis of how we quantify synergy. We do acknowledge the limitation of our LDH protection/synergy assay only produces interpretable data when our protectant/mixture yields protection levels within the range 0 and below 100%. Betaine was not protective in any of the concentrations we tested in this study. In line with the reviewer’s comment, we also acknowledge that within our experimental procedures, the inhibitory effects of betaine cannot be accurately captured, considering that LDH activity is ~0% without protectants. However, in our positive control in which LDH is co-incubated with betaine or betaine and CAHS D overnight in the hydrated state, we do not see a loss of enzymatic function of LDH nullifying a direct inhibition by betaine. We have added this text in our manuscript: “Glycine betaine on its own is not protective to LDH during drying nor does it inhibit LDH activity (Fig. S8E)”.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

The conclusion in lines 195-196 seems overstated as the length dependence could be strongly changed in non-tested concentrations or those that are not possible experimentally. Notably, the IDPs in Figure 2 are around 200AA and only transition in the ranges tested for these peptides. Some other conclusions around this point seem a little overstated.

We acknowledge the reviewer’s concern about the potential variability of the length dependence of the motifs at concentrations beyond those tested. However, we would like to highlight that higher concentrations of the tandem repeats (At22 and At44) inactivated LDH during the incubation period, as was seen with  the 11-mer motifs. This meant we could not evaluate protection by these motifs at concentrations beyond those plotted in Fig. 1A. This behavior was not observed for the full-length proteins. Regardless, we have toned down the conclusion in lines 195-196 to only reflect our results for the 2X and 4X repeats of At11 which now reads “We synthesized 2X (At22) and 4X (At44) tandem repeats of the A. thaliana 11-mer LEA_4 motif (At11). At22 and At44 show minimal potency in preserving in vitro LDH function during drying (Fig. 1A, Fig. S1A).”

Reviewer #2 (Recommendations For The Authors):

Figure 3: The focus on the ratio 222/210 seems inappropriate. That would indeed be useful for telling apart e.g. an alpha-to-beta transition, or formation of coiled coils. However, for a helix-to-coil equilibrium, which is likely to dominate here, it will not be especially sensitive as demonstrated e.g. by BSA in the dry state.

We thank the reviewer for this comment. The use of ratios to measure structural transition is primarily to eliminate the effects of concentrations on the graph. It is clear from Fig. 3A and Fig. 3B that a structural transition occurs between the aqueous and the desiccated state. This is also very clear from the 222/210 ratio that we use (Fig. 3C), for every construct other than BSA - which indeed does not seem to undergo a dramatic structural change in the desiccated state. We have clarified this now in the description of the results: “Using this metric, all LEAs and CAHS D display a clear increase in helical propensity upon being desiccated (Fig. 3C). On the other hand, the helical propensity of BSA remains very similar to its hydrated state, indicating that no dramatic structural change took place (Fig. 3C).

Minor comments:

Figure 1F is not mentioned in the text.

We have included Fig. 1F in the text.

Some technical details missing for SAXS experiments.

We thank the reviewer for pointing this out. We’ve added additional technical details to the main text, and directed readers to the methods for more information.

It is well known that BSA is in a monomer-dimer equilibrium and this is normally taken into account in data analysis as this is often a calibration sample.

We’ve calculated for BSA, and correlated the resulting data with synergy. This can be found in figure S7M and figure S8I.

Line 247: "BSA, which comes from cows, which of course have no capacity for anhydrobiosis" - This seems like a rather strong statement without a reference. Did the authors consider reanimating beef jerky by soaking it in water? ;-)

This is a great idea, and we hope to assign this project to our next rotation student.

Minor suggestions for figures (that are generally very well done):

Figure 1-4: Consider using the color scheme to indicate what the endogenous cosolutes are. Even though this info is in table one, it would still improve readability.

We have added the colored organismal icons for all figures in which the plain black ones were previously used, including supplementals.

Figure 4: consider adding some white space between the two concentration series of solutes to avoid being read as a single concentration series.

We have updated this figure to clearly separate each sample by osmolyte.

Figure 6H: Consider changing the colors for Betaine and CAHS D, so they are easier to distinguish. They are hard to tell apart on a printout.

We have adjusted the colors for betaine and CAHS D.

eLife assessment

This important study investigates the sensitivity to endogenous cosolvents of three families of intrinsically disordered proteins involved with desiccation. The findings, drawn from well-designed experiments and calculations, suggest a functional synergy between sensitivity to small molecule solutes and convergent desiccation protection strategy. The evidence is found to be convincing, and the authors provide appropriate caveats since the study's conclusions are based on a small number of proteins. This work will be of interest to biochemists and biophysicists interested in the conformation-function relationship of intrinsically disordered proteins.

Reviewer #1 (Public Review):

The individual roles of both cosolvents and intrinsically disordered proteins (IDPs) in desiccation have been well established, but few studies have tried to elucidate how these two factors may contribute synergistically. The authors quantify the synergy for the model and true IDPs involved with desiccation and find that only the true IDPs have strong desiccation tolerance and synergy with cosolvents. Using these as model systems, they quantify the local (secondary structure vis-a-vi CD spectroscopy) and global dimensions (vis-a-vi the Rg of SAXS experiments) and find no obvious changes with the co-solvents. Instead, they focus on the gelation of one of the IDPs and, using theory and experiments, suggest that the co-solvents may enable desiccation tolerance, an interesting hypothesis to guide future in vivo desiccation studies. A few minor points that remained unclear to this reviewer and that were noted previously have been reasonably addressed in this revision.

Strengths:

This paper is quite extensive and has significant strengths worth highlighting. Notably, the number and type of methods employed to study IDPs are quite unusual, employing CD spectroscopy, SAXS measurements, and DSC. The use of the TFE is an exciting integration of the physical chemistry of cosolvents into the desiccation field is a nice approach and a clever way of addressing the gap of the lack of conformational changes depending on the cosolvents. Furthermore, I think this is a major point and strength of the paper; the underlying synergy of cosolvents and IDPs may lie in the thermodynamics of the dehydration process.

Figure S6A is very useful. I encourage readers who are confused about the DSC analysis, interpretation, and calculation to refer to it.

Weaknesses:

All minor weaknesses were addressed in this revision.

Reviewer #2 (Public Review):

Summary:

The paper aims to investigate the synergies between desiccation chaperones and small molecule cosolutes, and describe its mechanistic basis. The paper reports that IDP chaperones have stronger synergies with the cosolutes they coexist with, and in one case suggests that this is related to oligomerization propensity of the IDP.

Strengths:

The authors have done a good job improving the paper. The study uses a lot of orthogonal methods and the experiments are technically well done. They are addressing a new question that has not really been addressed previously.

Weaknesses:

The conclusions are still based on a few examples and only partial correlations. However, this is now acknowledged by the authors and the conclusions are presented with appropriate caveats.

eLife assessment

This study presents a valuable optimization algorithm to identify polymer models that best fit population-averaged chromosome contact data that will be of interest to physicists and biologists working on chromatin organization. The conclusions are supported by solid evidence.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors of this study aim to use an optimization algorithm approach, based on the established NelderMead method, to infer polymer models that best match input bulk Hi-C contact data. The procedure infers the best parameters of a generic polymer model that combines loop-extrusion (LE) dynamics and compartmentalization of chromatin types driven by weak biochemical affinities. Using this and DNA FISH, the authors investigate the chromatin structure of the MYC locus in leukemia cells, showing that loop extrusion alone cannot explain local pathogenic chromatin rearrangements. Finally, they study the locus single-cell heterogeneity and time dynamics.

Strengths:

- The optimization method provides a fast computational tool that speeds up the parameter search of complex chromatin polymer models and is a good technical advancement.

- The method is not restricted to short genomic regions, as in principle it can be applied genome-wide to any input Hi-C dataset, and could be potentially useful for testing predictions on chromatin structure.

Weaknesses:

(1) The optimization is based on the iterative comparison of simulated and Hi-C contact matrices using the Spearman correlation. However, the inferred set of the best-fit simulation parameters could sensitively depend on such a specific metric choice, questioning the robustness of the output polymer models. How do results change by using different correlation coefficients?

This is an important question. We have tested several metrics in the process of building the fitting procedure. We now showcase side-by-side comparisons of the fitting results obtained using these different metrics in supplementary figure 2.

(2) The best-fit contact threshold of 420nm seems a quite large value, considering that contact probabilities of pairs of loci at the mega-base scale are defined within 150nm (see, e.g., (Bintu et al. 2018) and  (Takei et al. 2021)).

This is a good point. Unfortunately, there is no established standard distance cutoff to map distances to Hi-C contact frequency data. Indeed, previous publications have used anywhere between 120 nm to 500 nm (see e.g. (Cardozo Gizzi et al. 2019), (Cattoni et al. 2017) , (Mateo et al. 2019), (Hafner et al. 2022), (Murphy and Boettiger 2022), (Takei et al. 2021), (Fudenberg and Imakaev 2017) , (Wang et al. 2016), (Su et al. 2020), (Chen et al. 2022), (Finn et al. 2019)). 

We have included a supplementary table in the revised preprint (supplementary table 3) listing these values to demonstrate the lack of consensus. This large variation could reflect different chromatin compaction levels across distinct model systems, and different spatial resolutions in DNA FISH experiments performed by different labs. The variance in the threshold choice is also likely partially explained by Hi-C experimental details, e.g. the enzyme used for digestion, which biases the effective length scale of interactions detected (Akgol Oksuz et al. 2021). Among commonly used restriction enzymes, HindIII has a relatively low cutting frequency which results in a lower sensitivity to short-range interactions; on the other hand, MboI has a higher cutting frequency which results in a higher sensitivity to short-range interactions (Akgol Oksuz et al. 2021). Because the Hi-C data we used for the Myc locus in (Kloetgen et al. 2020) was generated using HindIII, we chose a distance cutoff close to the larger end of published values (420 nm). 

(3) In their model, the authors consider the presence of LE anchor sites at Hi-C TAD boundaries. Do they correspond to real, experimentally found CTCF sites located at genomic positions, or they are just assumed? A track of CTCF peaks of the considered chromatin loci would be needed.

We apologize this was not clear. The LE anchor sites in the simulation model were chosen because they correspond to experimental CTCF sites and ChIP-seq peaks located at the corresponding genomic positions. Representative CTCF ChIP-seq tracks from (Kloetgen et al. 2020) have been added to figure 2A in the revised preprint version to emphasize this point.

(4) In the model, each TAD is assigned a specific energy affinity value. Do the different domain types (i.e., different colors) have a mutually attractive energy? If so, what is its value and how is it determined? The simulated contact maps (e.g., Figure 2C) seem to allow attractions between different blocks, yet this is unclear.

Sorry this was not explicit. The attraction energy between a pair of monomers in the simulation is determined using the geometric mean of the affinities of the two monomers. This applies to both monomers within the same domain and in different domains. This detail has been clarified in the Methods section: “To optimize the simulation duration to streamline the parameter search (Supp. Fig. 1 B), we computed the autocorrelation function of the TAD2-TAD4 inter-TAD distance using the initial guess simulation parameters of the MYC locus in CUTLL. The simulation was saved every 5 simulation blocks.”

(5) To substantiate the claim that the simulations can predict heterogeneity across single cells, the authors should perform additional analyses. For instance, they could plot the histograms (models vs. experiments) of the TAD2-TAD4 distance distributions and check whether the models can recapitulate the FISH-observed variance or standard deviation. They could also add other testable predictions, e.g., on gyration radius distributions, kurtosis, all-against-all comparison of single-molecule distance matrices, etc,.

We agree that heterogeneity prediction is a key advantage of the simulations. We do note that the histograms (models vs. experiments) of the TAD2-TAD4 distance distributions measured by FISH were plotted in Fig. 3C as empirical cumulative probability distributions (as is standard in the field), side by side with the simulation predictions. Simulations indeed recapitulate the variance observed by FISH. We also had emphasized this important point in the main text: “Importantly, not just the average distances, but the shape of the distance distribution across individual cells closely matches the predictions of the simulations in both cell types, further confirming that the simulations can predict heterogeneity across cells.”

(6) The authors state that loop extrusion is crucial for enhancer function only at large distances. How does that reconcile, e.g., with Mach et al. Nature Gen. (2022) where LE is found to constrain the dynamics of genomically close (150kb) chromatin loci?

This is an interesting question. In (Mach et al. 2022), the authors tracked the physical distance between two fluorescent labels positioned next to either anchor of a ~150 kb engineered topological domain using live-cell imaging. They found that abrogation of the loop anchors by ablation of the CTCF binding motifs, or knock-down of the cohesin subunit Rad21 resulted in increased physical distance between the loci. HMM Modeling of the distance over time traces suggests that the increased distance resulted from rarer and shorter contacts between the anchors. While this might seem at odds with the results of Fig. 4L, we note a key difference between the loci. While (Mach et al. 2022) observed the dynamics of the distance separating two CTCF loop anchors, in our model only the MYC promoter is proximal to a loop anchor, while the position of the second locus is varied, but remains far from the other anchor. The deletion of the CTCF sites at both anchors in (Mach et al. 2022) indeed results in a lowered sensitivity of the physical distance to Rad21 knock-down, reminiscent of the results of Fig. 4L in our work. This result demonstrates that loop extrusion disruption disproportionately impacts distances between loci close to loop anchors, consistent with Hi-C results (Rao et al. 2017; Nora et al. 2017). We therefore believe that the models in our work and (Mach et al. 2022) are not at odds, but simply reflect that loop extrusion perturbations impact distances between loop anchors the most.  Enhancer-Promoter loops are generally distinct from CTCF-mediated loops (Hsieh et al. 2020, 2022). While (Mach et al. 2022) represents a landmark study in our understanding of the dynamics of genomic folding by loop extrusion, we therefore believe that the locus we chose here - which matches the endogenous MYC architecture - may more accurately represent Enhancer-Promoter dynamics than a synthetic CTCF loop.  To better articulate the similarities between model predictions and differences between the two loci, we have simulated a synthetic locus matching that of (Mach et al. 2022) in the revised preprint. Our simulation recapitulates the results obtained by Mach et al, including the sensitivity of contact frequency and duration to in silico cohesin knock-down (supplementary figure 6). We have updated the Results section accordingly: “The dependence of contact dynamics on loop extrusion in our simulations of MYC differs from that previously observed for two TAD boundaries (45). To check whether the different results are the product of different simulation models, we simulated contact dynamics across two TAD boundaries matching the locus of (45). Our simulations recapitulate the distance distribution and loop extrusion dependence previously observed (Supp. Fig. 6), establishing that the differences between the two systems are biological. While loop extrusion controls both the frequency and duration of contacts at TAD boundaries, it exerts a more nuanced effect on the frequency of contacts in loci pairs like the MYC locus that might better reflect typical enhancer-promoter pairs.”

Reviewer #2 (Public Review):

Summary:

The authors Fu et al., developed polymer models that combine loop extrusion with attractive interactions to best describe Hi-C population average data. They analyzed Hi-C data of the MYC locus as an example and developed an optimization strategy to extract the parameters that best fit this average Hi-C data.

Strengths:

The model has an intuitive nature and the authors masterfully fitted the model to predict relevant biology/Hi-C methodology parameters. This includes loop extrusion parameters, the need for self-interaction with specific energies, and the time and distance parameters expected for Hi-C capture.

Weaknesses:

(1) We are no longer in the age in which the community only has access to population average Hi-C. Why was only the population average Hi-C used in this study?

Can single-cell data: i.e. single-cell Hi-C/Dip-C data or chromatin tracing data (i.e. see Tan et al Science 2018 - for Dip-C, Bintu et al Science 2018, Su et al Cell 2020 for chromatin tracing, etc.) or even 2 color DNA FISH data (used here only as validation) better constrain these models? At the very least the simulations themselves could be used to answer this essential question.

I am expecting that the single-cell variance and overall distributions of distances between loci might better constrain the models, and the authors should at least comment on it.

We agree that it is possible to recapitulate single-cell Hi-C or chromatin tracing data with simulations, and that these data modalities have a superior potential to constrain polymer models because they provide an ensemble of single allele structures rather than population-averaged contact frequencies. However, these data remain out of reach for most labs compared to Hi-C. Our goal with this work was to provide an approachable method that anyone interested could deploy on their locus of choice, and reasoned that Hi-C currently remains the data modality available to most. We envision this strategy will help reach labs beyond the small number of groups expert in single cell chromatin architecture, and thus hopefully broaden the impact of polymer simulations in the chromatin organization field. 

Nevertheless, we do agree that the comparison of single-cell chromatin architectures to simulations is a fertile ground for future studies, and have modified the preprint accordingly (Discussion):

“Future work extending this framework to single cell readouts out chromatin architecture (e.g. single-cell Hi-C or chromatin tracing) holds promise to further constrain chromatin models.”

(2) The authors claimed "Our parameter optimization can be adapted to build biophysical models of any locus of interest. Despite the model's simplicity, the best-fit simulations are sufficient to predict the contribution of loop extrusion and domain interactions, as well as single-cell variability from Hi-C data. Modeling dynamics enables testing mechanistic relationships between chromatin dynamics and transcription regulation. As more experimental results emerge to define simulation parameters, updates to the model should further increase its power." The focus on the Myc locus in this study is too narrow for this claim. I am expecting at least one more locus for testing the generality of this model.

We note that we used two distinct loci in the initial version of our study, the MYC locus in leukemia vs T cells (Figs. 2-3) and a representative locus in experiments comparing WT CTCF with a mutant that leads to loss of a subset of CTCF binding sites (Fig. 1L). To further demonstrate generality, we have added to the revised preprint a demonstration of the simulation fitting to other loci acquired in different cell types (supplementary figure 3).

Recommendations for the authors:.

Reviewer #1 (Recommendations For The Authors):

(1) The Methods part of the imaging analysis lacks some quantitative details that could be useful for the readers: what is the frequency of double detections? How "small" is the 3D region around the centroid? How many cells with no spots or more than four spots are excluded?

We have clarified these important analysis parameters in the revised version of the preprint (Methods), including supplementary Table 2, listing the statistics of excluded cells:

“We then cropped out a small 3D region (20x20x10 pixels) around each approximate centroid, and subtracted the surrounding background intensity.”

“Cells with no spots or more than four spots were excluded from the cell cycle analysis (statistics in Supp. Table 2).”

(2) How is the autocorrelation function of chromatin structures computed?

We computed the autocorrelation function of the TAD2-TAD4 inter-TAD distance using the initial guess simulation parameters (Eattr, boundary permeabilities) of the MYC locus in CUTLL. All other simulation parameters are the same as other simulations in the preprint. The structure of the locus was saved every 5 simulation blocks. These structures were used to compute the TAD2-TAD4 inter-TAD distance as a function of time, which was used to calculate the autocorrelation function. This has been clarified in the revised version of the preprint (Methods):

“To optimize the simulation duration to streamline the parameter search (Supp. Fig. 1 B), we computed the autocorrelation function of the TAD2-TAD4 inter-TAD distance using the initial guess simulation parameters of the MYC locus in CUTLL. The simulation was saved every 5 simulation blocks.”

(3) How is the monomer length (35nm) chosen to best compare FISH data?

Because monomer length is difficult to derive from first principles, the standard in the field is to convert the size of a simulated monomer into a physical distance using a reference measurement in the system of choice. Similar to the Hi-C distance threshold, values for monomer size vary throughout the literature, e.g. 53 nm per 3 kbp monomer (Giorgetti et al. 2014), 50 nm per 2.5 kbp monomer (Nuebler et al. 2018), or from 36 to 60 nm per 3 kbp monomer, depending on the cell line or model details (Conte et al. 2022; Conte et al. 2020). 

Here we used the mean of the median TAD2-TAD4 distances in T Cells and CUTLL as our length reference, and converted simulation distances into nm by matching this value. We obtained 35 nm per 2.5 kbp monomer, a value well within the range of the literature values (see above).

Using this simple conversion, the simulated distance distributions recapitulate two independent metrics accessible by DNA FISH: the shift in median distances between T cell and CUTLL, and the width of each distribution. This agreement indicates that simulations recapitulate both the differences between the two cell types, and the single cell heterogeneity within each cell type. 

(4) The main text does not make clear the "known" biophysical parameters that establish the model ground truth.

In the initial validation of the fitting procedure, by “known biophysical parameters”, we meant that we generated simulated Hi-C maps in which we set the left/right permeabilities at each boundary, and Eattr values within each TAD to known values. We then assessed how well the fitting could recover these known ground truth values by trying to match the simulated representative Hi-C map. The specific values chosen are plotted for each set of simulations in Fig.1 F, H, J. The main text has been made more explicit in the revised preprint version (Results):

“We first validated the optimization method using ground truth maps built from simulation runs with known values of StallL, StallR, Eattr for each boundary/domainbiophysical parameters.”

(5) What are the correlation coefficients between experimental and model contact maps in Figure 1L?

We apologize for the oversight. The missing coefficient values have been added in the revised version of the manuscript (Results):

“As expected, the simulation predicted a significant drop of 0.13 in boundary permeability in CTCFmut compared to WT (Fig. 1 L; Spearman Correlation: 0.85±0.02 for CTCFmut, 0.82±0.01 for WT).”

(6) Figure 2A, B: Contact matrices look oversaturated. Next, why do model contact maps have negative values?

We apologize this was not clear. Figure 2 A,B plotted the log value of the contact matrices, thus the negative values. This has been made explicit in the revised version of the preprint (Fig. 2 Legend). 

(7) For model reproducibility, the authors could report the coordinates of the Hi-C TAD boundaries employed for the model.

We have included in the revised version of the preprint an explicit mention of all genomic coordinates of the loci simulated in the Methods section:

“The model used to fit into MYC Hi-C data consists of 1920 monomers representing chr8:126,720,000131,680,000, with the TAD boundaries located at monomer 456 (chr8: 127,840,000 - 127,880,001), monomer

808 (chr8: 128,720,000 - 128,760,001), monomer 1178 (chr8: 130,160,000 - 130,200,001) and monomer 1592 (chr8: 130,680,000 - 130,720,001).”

(8) What is the shaded area in Figure 3C?

The shaded area in Figure 3C is the standard deviation calculated from three independent DNA FISH or simulation replicates for each bin of the histogram. This detail has been clarified in the revised preprint (Figure 3 legend). 

(9) In the Discussion, I suggest changing as follows: "the time- and distance-gated model proposed here recapitulates several observations" -> "the time- and distance-gated model proposed here could recapitulate several observations", as they are speculations.

The sentence has been changed accordingly in the revised preprint (Discussion). Thank you for the suggestion. 

Reviewer #2 (Recommendations For The Authors):

Suggest analyzing the ability of single-cell data to better constrain dynamical models.

While we agree that modeling single-cell distributions is a worthwhile endeavor to be explored in future work, we believe that the tool presented here serves a slightly different purpose: enabling labs that only have access to the most widespread technique at present to perform simulations to interrogate the forces that shape the organization of an arbitrary locus in their model of choice. Analyzing single-cell data is in principle very powerful, but would by necessity be limited to the small number of systems where these cutting-edge techniques have been deployed. 

Suggest selecting another locus other than MYC to demonstrate generality.

We note that we used two distinct loci in the study, the MYC locus in leukemia vs. T cells (Figs. 2-3) and a representative locus in experiments comparing WT CTCF with a mutant that leads to loss of a subset of CTCF binding sites (Fig. 1L). To further demonstrate generality, we have added to the revised preprint a demonstration of the simulation fitting to other loci acquired in different cell types (supplementary figure 3).

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Reviewer #1 (Public review):

Summary:

The authors of this study use an optimization algorithm approach, based on the established Nelder-Mead method, to infer polymer models that best match input bulk Hi-C contact data. The procedure infers the best parameters of a generic polymer model that combines loop-extrusion (LE) dynamics and compartmentalisation of chromatin types driven by weak biochemical affinities. Using this and DNA FISH, the authors investigate the chromatin structure of the MYC locus in leukaemia cells, showing that loop extrusion alone cannot explain local pathogenic chromatin rearrangements. Finally, they study the locus single-cell heterogeneity and time dynamics.

In the revised manuscript the authors have adequately addressed my questions and comments. The exception concerns point #5 of my original review:

(5) Besides cumulative probability distributions, I asked the authors to show the TAD2-TAD4 (model vs. exp) distances in Fig. 3c as relative frequency histograms. This allows readers to more accurately evaluate whether model and experimental distributions have same shape and variance.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This study by Wang et al. identifies a new type of deacetylase, CobQ, in Aeromonas hydrophila. Notably, the identification of this deacetylase reveals a lack of homology with eukaryotic counterparts, thus underscoring its unique evolutionary trajectory within the bacterial domain.

Strengths:

The manuscript convincingly illustrates CobQ's deacetylase activity through robust in vitro experiments, establishing its distinctiveness from known prokaryotic deacetylases. Additionally, the authors elucidate CobQ's potential cooperation with other deacetylases in vivo to regulate bacterial cellular processes. Furthermore, the study highlights CobQ's significance in the regulation of acetylation within prokaryotic cells.

Weaknesses:

While the manuscript is generally well-structured, some clarification and some minor corrections are needed.

Reviewer #2 (Public Review):

In recent years, lots of researchers have tried to explore the existence of new acetyltransferase and deacetylase by using specific antibody enrichment technologies and high-resolution mass spectrometry. This study adds to this effort. The authors studied a novel Zn2+- and NAD+-independent KDAC protein, AhCobQ, in Aeromonas hydrophila. They studied the biological function of AhCobQ by using a biochemistry method and used MS identification technology to confirm it. The results extend our understanding of the regulatory mechanism of bacterial lysine acetylation modifications. However, I find their conclusion to be a little speculative, and unfortunately, it also doesn't totally support the conclusion that the authors provided. In addition, regarding the figure arrangement, lots of the supplementary figures are not mentioned, and tables are not all placed in context.

Major concerns:

- In the opinion of this reviewer, is a little arbitrary to come to the title "Aeromonas hydrophila CobQ is a new type of NAD+- and Zn2+-independent protein lysine deacetylase in prokaryotes." This should be modified to delete the "in the prokaryotes", unless the authors get new or more evidence in the other prokaryotes for the existence of the AhCobQ.

Thanks for your suggestions. " in the prokaryotes " has been deleted in the revised manuscript.

- I was confused about the arrangement of the supplementary results. There are no citations for Figures S9-S19.

Thank you very much for your suggestion. We have made revisions and highlighted in the undated manuscript.

- No data are included for Tables S1-S6.;

Dear reviewer, sorry to confuse you. We have included the Supplementary Tables in the undated manuscript.

- The load control is not all integrated. All of the load controls with whole PAGE gel or whole membrane western blot results should be provided. Without these whole results, it is not convincing to come to the conclusion that the authors have.

Dear reviewer, thanks for your suggestion. We have meticulously incorporated the complete PVDF membranes from our Western blot experiments into Supplementary Material 1. Furthermore, we have included the Coomassie Blue R-350 staining outcomes of these PVDF membranes, post-Western blot detection, as a loading control in accordance with the protocol outlined in the reference by Charlotte et al. (Journal of Proteome Research, 2011, 10:1416–1419).

- The materials & methods section should be thoroughly reviewed. It is unclear to me what exactly the authors are describing in the method. All the experimental designs and protocols should be described in detail, including growth conditions, assay conditions, purification conditions, etc.

Dear reviewer, thanks for your valuable comments. We have carefully reviewed the entire manuscript and made revisions, highlighted in red.

- Relevant information should be included about the experiments performed in the figure legends, such as experimental conditions, replicates, etc. Often it is not clear what was done based on the figure legend description.

Thank you very much for your suggestion. We have made revisions and highlighted in red.

Reviewer #3 (Public Review):

Summary:

This study reports on a novel NAD+ and Zn2+-independent protein lysine deacetylase (KDAC) in Aeromonas hydrophila, termed AhCobQ (AHA_1389). This protein is annotated as a CobQ/CobB/MinD/ParA family protein and does not show similarity with known NAD+-dependent or Zn2+-dependent KDACs. The authors show that AhCobQ has NAD+ and Zn2+-independent deacetylase activity with acetylated BSA by western blot and MS analyses. They also provide evidence that the 195-245 aa region of AhCobQ is responsible for the deacetylase activity, which is conserved in some marine prokaryotes and has no similarity with eukaryotic proteins. They identified target proteins of AhCobQ deacetylase by proteomic analysis and verified the deacetylase activity using site-specific acetyllysine-incorporated target proteins. Finally, they show that AhCobQ activates isocitrate dehydrogenase by deacetylation at K388.

Strengths:

The finding of a new type of KDAC has a valuable impact on the field of protein acetylation. The characters (NAD+ and Zn2+-independent deacetylase activity in an unknown domain) shown in this study are very unexpected.

Weaknesses:

(1) As the characters of AhCobQ are very unexpected, to convince readers, MSMS data would be needed to exactly detect deacetylation at the target site in deacetylase activity assays. The authors show the MSMS data in assays with acetylated BSA, but other assays only rely on western blot.

(2) They prepared site-specific Kac proteins and used them in deacetylase activity assays. The incorporation of acetyllysine at the target site needs to be confirmed by MSMS and shown as supplementary data.

(3) The authors imply that the 195-245 aa region of AhCobQ may represent a new domain responsible for deacetylase activity. The feature of the region would be of interest but is not sufficiently described in Figure 5. The amino acid sequence alignments with representative proteins with conserved residues would be informative. It would be also informative if the modeled structure predicted by AlphaFold is shown and the structural similarity with known deacetylases is discussed.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) The protein molecules of AhCobB and AhCobQ are greater than 45 kDa. But the gene sequences don't seem to match. Please explain.

We are sorry to confuse you. The vector used for the purification of CobB and CobQ in the manuscript is pET-32a, which carries the TrxA fusion protein and is approximately 20kDa in size. Therefore, the final molecular weight of recombinant AhCobB and AhCobQ is 48.3(28.3+ ~20kDa) and 49.8 (29.8+ ~20kDa), respectively.

(2) Figure 7: The gels look very smeary. Please explain.

Dear esteemed reviewer, in our study, we have meticulously crafted recombinant site-specific Kac proteins utilizing an innovative two-plasmid system, grounded on the seminal work published in Nature Chemical Biology (2017, 13(12): 1253-1260), which introduced the genetic encoding of Nᵋ-acetyllysine into recombinant proteins. However, we have encountered a prevalent challenge—the occurrence of protein truncation due to premature translation termination at the reassigned codon. This phenomenon not only diminishes protein yields, as highlighted in ChemBioChem (2017, 18(20): 1973-1983), but also plagues many recombinant proteins with a troublesome backdrop in Western Blot (WB) outcomes.

Despite our rigorous approach, involving at least two independent repetitions for WB analysis of site-specific Kac proteins, yielding consistent results, we acknowledge that the overall quality of these WB assays remains suboptimal. This variability is inherently tied to the intrinsic properties of the target proteins themselves. Illustratively, the WB outcomes for proteins such as ENO and ICD exhibit notable differences in quality across biological replicates, emphasizing the complexity and nuances involved in this process.

Thus, while our methodology remains robust and reproducible, we are mindful of the limitations imposed by the nature of the proteins under investigation and strive to continually refine our approaches to mitigate these challenges.

(3) To ensure that the phenotype shown in Figure 1 is not due to polar effects, results of supplementing complementary strains should be provided.

Thank you for your suggestion. We have constructed a complement strain and tested the bacterial migration ability. As shown in the Figure S1, the complement strain does not affect the physiological phenotype mentioned above.

(4) The caption to Figure 8 includes * and *** to indicate significance levels, but only *** appears in the picture.

Thank you for your suggestion. It has been modified and highlighted in red.

(5) Has the mechanistic role of lysine 388 in ICD been characterized?

Thank you for your invaluable professional insights. Indeed, the acetylation sites of ICD have been established to exert a significant influence on its enzymatic activity. Sumana Venkat et al., in their seminal work published in the Journal of Molecular Biology (2018, 430(13): 1901-1911), convincingly demonstrated that the acetylation of specific lysine residues—K100, K230, K55, and K350—in ICD proteins from E. coli serves as a negative regulatory mechanism for enzyme activity. Intriguingly, the functional implications of the Kac modification on K387 (corresponding to the K388 site in ICD from A. hydrophila ATCC 7966, as featured in this manuscript) remain an uncharted territory.

Our experimental endeavors have illuminated that the K388 site of ICD in A. hydrophila holds the potential to modulate enzymatic activity and is under the regulatory influence of AhCobQ.

(6) The format of the references is not uniform enough, for example, some journal names are abbreviated, and some are not, please check and correct.

Thank you for your suggestion. It has been modified and highlighted in red.

(7) Page 23, line 13, gene not expressed in italics, please correct.

Thank you for your suggestion. It has been modified and highlighted in red.

(8) Figure S8 does not appear to match the gene size.

We are sorry to confuse you. The vector used for the purification of recombinant protein in the manuscript is pET-32a, which carries the TrxA fusion protein and is approximately 20kDa in size. Therefore, the final molecular weight of recombinant protein is 25.5(5.5+ ~20kDa).

(9) The format of the two figures in Figure S10 is not uniform.

Thank you for your suggestion. It has been modified and highlighted in red.

Reviewer #2 (Recommendations For The Authors):

Minor concerns:

L147, L177 - Please arrange the results as they are shown in the content sequentially. For example, rename Figure S2 with Figure S1.

Thank you for your suggestion. It has been modified and highlighted in red.

L174 Figure 2D - There is no big change in the acetylation between the wild type and ahcobQ mutant from Figure 2D, but the ahcobB mutant is.

I am extremely grateful for your insightful comment. As clearly depicted in the right panel of Figure 2D, the overall Kac protein levels in both the ahcobQ and ahcobB knockout strains exhibit a marked elevation compared to the wild-type strain, despite equivalent loading of total cellular proteins (the left panel of Figure 2D). Notably, this increase is particularly pronounced among proteins with a molecular weight below 35 kDa. We wholeheartedly concur with your perspective that the deletion of ahcobB leads to a more substantial enhancement in Kac protein levels, suggesting CobB may play a pivotal role in regulating a broader spectrum of acetylated proteins or Kac sites. This hypothesis is further strengthened by subsequent mass spectrometry analyses, which lend additional credence to our shared understanding.

L174-187, L795 - Please show the whole membrane (or PAGE gel) of the loading control of CobB, and CobQ, except for the Kac-BSA.

Dear esteemed reviewer, we have thoroughly revised our submission to include the full western blot (WB) membrane for all figures and supplementary figures within the updated Supplementary Material 1. Additionally, we would like to clarify a few crucial points to ensure transparency and accuracy.

Firstly, in Figure 2D, we present WB results solely pertaining to whole-cell samples from cobB or cobQ mutant strains. Consequently, these findings do not directly correlate with recombinant CobB or CobQ proteins.

Secondly, the objective of Figure 2 is to validate the lysine deacetylase activity of AhCobQ protein through a qualitative, rather than quantitative, experimental approach. Hence, the crucial loading control lies in the amount of Kac-BSA, rather than CobB or CobQ. Prior to conducting the in vitro deacetylase assay, we ensured equal protein concentrations of purified CobB or CobQ using BCA assay, adhering to the protocol's specified deacetylase-to-Kac-BSA loading ratio of 1:5. However, this ratio renders the deacetylase (CobB or CobQ) undetectable on Coomassie Blue R-350-stained blots or WB membranes (as detailed in the whole WB membrane in Supplementary Material 1).

To reinforce our observations, we reiterated the analysis of protein samples by subjecting them once again to SDS-PAGE, maintaining the same loading quantity as utilized in the preceding western blotting experiment shown in Figure 2E. As Author response image 1 clearly illustrates, the CobB/CobQ bands are indeed discernible, albeit they exhibit significantly fainter intensities when compared to the Kac-BSA bands. Notably, upon reviewing the full strained PVDF membrane presented in Supplementary Material 1, we find that the CobB/CobQ bands are not readily visible. This observation can be attributed to the potential loss of proteins during the transfer process from SDS-PAGE to the PVDF membrane.

Author response image 1.

The SDS-PAGE gel displayed the loading amounts of Kac-BSA and CobB/CobQ.

Furthermore, recognizing the potential for confusion given the similar molecular weights of CobB (257aa) and CobQ (264aa, excluding fusion tags), we conducted a comparative analysis of deacetylase activity between His-tagged and GST-fused recombinant CobQ proteins. Encouragingly, both variants exhibited deacetylase activity (as presented in Figure S5 of the revised manuscript), thereby excluding any influence from nonspecific proteins that might have contaminated the purification process.

We hope these clarifications and additions to our submission address your concerns and enhance the overall quality of our work. Thank you for your valuable time and consideration.

- Could you provide the raw data of these anti-acetylation western blot results?

Thank you very much for your suggestion. The raw results have been uploaded in the supplementary materials.

- According to the loading control, the protein quantity of BSA is very big, however, why is the acetylation of Kac-BSA relatively low? Is it consistent between the western blot and loading control?

Thank you very much for your suggestion, first of all, all the western blot and loading control in the manuscript are the same membrane, and the specific method is described in "Western blot". Therefore, there is no possibility that the western blot and loading control do not correspond. Secondly, not every site of BSA has acetylation modifications, and the amount of modifications at each site is also different, so there will be a large amount of protein but a small amount of acetylation.

Figure 2C - Could the Dot blot experiment be described in detail in the Methods part?

Thank you for your suggestion. It has been added and highlighted in red.

Figure 2C&2D - Please provide the anti-acetylation antibody information.

Thank you for your suggestion. It has been added and highlighted in red.

Figure 2E - It is confusing why the acetylation of Kac-BSA is higher than adding NAD+ with CobB? But only CobB can deacetylate the Kac-BSA without NAD+?

We are sorry to confuse you. The information in the figure is incorrect. For somehow, we provided the uncorrected version, and we have revised it in the undated manuscript.

Figure 2F - The control of this experiment should include the NAM, CobB, and NAM+CobB. Similar to 2E, it also should include NAD, CobB, and NAD+CobB, respectively. Same with 2H.

We are sorry to confuse you. The intent of Figure 2F is to further confirm that AhCobQ is different from AhCobQ and can remove the acetylation modification of BSA without relying on NAD+, so NAD+ was added to this group of experiments. We have revised the manuscript to add details about the experiments.

L178 Figure S1C - One question about the protein AhAcuC. From the PCR results, it is larger than ahcobB and ahcobQ, however, why is the protein AhAcuC smaller than them?

We are sorry to confuse you. The images in the original manuscript may have had some errors in protein size due to different PAGE gels. We have re-run the gels and replaced them in the manuscript in the Supplementary Figure S3 in revised manuscript.

- All the proteins are expressed and purified from E.coli BL21(DE3). How did you avoid the pollution of the deacetylase from the E.coli? There is no control over it in your experiment. Without this control, it is not easy to come to the conclusion that the deacetylation is from the AhCobQ but not from the pollution from the protein purification.

In response to your inquiry, we have conducted a meticulous comparative analysis of the deacetylase activity exhibited by both His-tagged and GST-fused recombinant AhCobQ proteins. Reassuringly, our findings reveal that both variants possess robust deacetylase activity, as clearly demonstrated in Figure S5 of the revised manuscript. Furthermore, to ensure the rigor of our experiments, we employed GST protein purified from E.coli strains as a negative control in Figure S8. The Western blot (WB) results conclusively demonstrate that GST protein alone lacks deacetylase activity, thereby reinforcing the authenticity of our findings and effectively mitigating any concerns regarding potential interference from nonspecific proteins during the purification process.

L190 - Could you provide the raw data for Table S1?

Thank you very much for your suggestion. The raw MS data were deposited in the public ProteomeXchange Consortium via the PRIDE partner repository with the dataset identifier PXD038735 or IPX0005366000(iProx database). We also uploaded the analysis results in Table S1 and Supplementary material 2.

- I am not an expert on MS. I have one question about the MS results. Why there is no peak for the CobB or CobQ as they add to the reaction system?

Thank you for your insightful question. To clarify, the Kac peptides identified from Kac-BSA, as presented in Table S1, were meticulously selected for the purpose of enhancing their display and facilitating interpretation. The comprehensive raw mass spectrometry (MS) data, along with detailed analytical outcomes, have been diligently deposited within the ProteomeXchange Consortium, specifically through the PRIDE partner repository, under the dataset identifier PXD038735 or alternatively accessible via the iProx database under IPX0005366000. The analysis results also included in the Table S1 and Supplementary material 2.

Furthermore, it is crucial to note that in this study, we utilized Bovine serum albumin (BSA) as the foundational database for our MS searches. Consequently, the absence of CobB or CobQ proteins in our MS results stems from the inherent focus on BSA and the specific experimental design, which did not encompass the detection of these particular proteins.

We appreciate your attention to these details and hope this clarification addresses your query.

L189-L206 - Based on the results here, the function of CobB and CobQ overlaps on the same STDKac peptides.

Dear esteemed reviewer, our mass spectrometry (MS) analysis has revealed an intriguing finding: CobB and CobQ indeed function on the same STDKac peptide, suggesting a potential collaboration among distinct deacetylases in regulating protein function. This observation is further corroborated by our subsequent quantitative Kac proteomics results, which were obtained from three deacetylase mutants. These results underscore the possibility that CobB, CobQ, and AcuC possess both unique and overlapping protein substrates, reinforcing our hypothesis that multiple deacetylases work in concert to modulate protein activity.

- Do you assay the Km and Kcat about the CobQ by using Kac-BAS as the substrate by comparing with AhCobB?

Dear reviewer, thanks for your professional suggestion. In accordance with your guidance, we diligently attempted to analyze the Km or Kcat values of CobQ during its incubation with the substrate Kac-BSA using LC-MS/MS, repeating the process twice. However, to our disappointment, our current experimental platform has been unable to detect any discernible metabolites. We suspect that this may stem from operational proficiency challenges, as even our positive control experiment involving CobB incubation has failed to yield satisfactory results.

Given our uncertainty regarding the root cause of these issues, coupled with the suggestion from experts that the LC column might be a contributing factor except for skill, we have decided against repeating the experiments at this juncture. Nonetheless, we would like to assure you that we have rigorously validated the deacetylase activity of CobQ proteins through mass spectrometry, as detailed in our manuscript.

Furthermore, I am delighted to share that our preliminary findings have sparked interest among other research teams. In fact, one such group, upon reading our preprint, has independently tested the activity of CobQ and uncovered an additional intriguing function. We are actively exploring the possibility of collaborating with this team to delve deeper into the research and, hopefully, in the future, conduct a more refined analysis of the Km and Kcat of CobQ.

L214- Same question with Figures 2E-2H. Could you provide the whole page gel about the loading control? I want to know the quantity of the AhCobQ in this experiment except for the Kac-BSA. To tell the truth, the quantity of BSA is too much in the deacetylation reaction system to be able to tell its deacetylation activity in vitro.

Thank you very much for your suggestion. The raw data has been uploaded in the supplementary materials and the clarification is similar with above mentioned.

L217 - There might be a wrong citation of Figure S2 here.

Thank you for your suggestion. It has been corrected.

L244-250, Figure 6A - Are there 47, not 46 Kac proteins?

Thank you for your suggestion. It has been corrected.

- Are there nineteen, not nine increased Kac peptides common between the ΔahcobQ and ΔahacuC strains?

Thank you for your suggestion. It has been corrected.

- Are there ten, not six increased Kac peptides common between the ΔahcobQ and ΔahcobB strains?

Thank you for your suggestion. It has been corrected.

- Are there 69, not 65 increased Kac peptides common between the ΔahcobB and ΔahacuC strains?

Thank you for your suggestion. It has been corrected.

- Where is the raw data for Table S2?

Thank you very much for your suggestion. The raw data has been uploaded in the supplementary materials.

Figure 6B - Are there 52, not 51 Kac peptides?

Thank you for your suggestion. It has been corrected.

L272 - Why do you choose these 11 target proteins? There is no description of this background in the context.

We have opted to prioritize these proteins for subsequent validation, as their Kac levels exhibit a notable upregulation in the ΔahcobQ strain, potentially indicating their role as protein substrates for AhCobQ. We will incorporate this clarification into the revised manuscript to ensure clarity and comprehensiveness.

L277 - Figure S6 - Please show the whole PAGE gel about the loading control.

Dear esteemed reviewer, we sincerely apologize for any confusion our previous presentation may have caused. We would like to clarify that the bottom panel of Figure S6 depicts a Coomassie Blue R-350 stained whole PVDF membrane, rather than a PAGE gel, as may have been mistakenly inferred. To facilitate a comprehensive understanding, we have included the entire stained PVDF membranes in Supplementary Material 1.

As we have previously elaborated, the recombinant His-tagged or GST-fused AhCobQ proteins were not as discernible on the PVDF membrane due to a relatively lower loading amount compared to that of Kac-BSA.

-There might be a wrong citation in Figure S6. As you mentioned in the context, you expressed and purified 11 proteins and then tested their acetylation background.

Thank you for your suggestion. It has been corrected.

L280 - Figure S7 -The label of the Figure should be modified for the ATP.

Thank you for your suggestion. It has been modified.

- How did you do the experiment for 0h of ATP? There is no description of it in the Methods.

Thank you for your suggestion. It has been added.

- Please show the whole PAGE gel about the loading control.

Thank you very much for your suggestion. The whole PAGE gel has been uploaded in the supplementary materials.

L282 - Figure 7 - Please show the whole PAGE gel about the loading control.

Dear esteemed reviewer, we sincerely apologize for any confusion our previous presentation may have caused. We would like to clarify that the bottom panel of Figure S6 depicts a Coomassie Blue R-350 stained whole PVDF membrane, rather than a PAGE gel, as may have been mistakenly inferred. To facilitate a comprehensive understanding, we have included the entire stained PVDF membranes in Supplementary Material 1.

- Please adjust the font size of "A" and "B".

Thank you for your suggestion. It has been adjusted.

Figure 7A - The anti-acetylation Western blot here does not look good. All the western blots here should be re-done.

Dear reviewer, the recombinant site-specific Kac proteins were constructed by two-plasmid system based on genetically encoding Nᵋ-acetyllysine in recombinant proteins in this study (Nature chemical biology, 2017, 13(12): 1253-1260). However, a common problem experienced is protein truncation arising from translation termination at the reassigned codon, lowering protein yields (ChemBioChem, 2017, 18(20): 1973-1983), and leading to a dirty background of WB results in many recombinant proteins. Although we did perform at least two times independent repeats for site-specific Kac protein WB and got similar results, the WB quality of site-specific Kac proteins are general poor and that depend on the properties of target proteins. For example, the WB results of ENO and ICD can display considerable qualities in different biological repeats.

- Why did you choose the PAGE gel but not the anti-His Western blot as the loading control?

Thank you very much for your suggestion. Labeling antibodies is a very effective loading control. However, in order to ensure the accuracy of the data, both the experimental data and loading control in this manuscript are required to be reflected on the same membrane. If His tags are used, the membrane will be washed repeatedly for secondary color development. Based on the fact that acetylation modification is already difficult for color development, this will greatly affect the quality of the results presented. Meanwhile, while ensuring consistent protein levels, we believe that changes in acetylation modifications can also explain the issue. Therefore, you choose the PAGE gel but not the anti-His Western blot as the loading control.

L278 - Where are the results of the site-specific lysine acetylation of the target protein by using two-plasmid-based system of genetically encoded Nε-acetyllysine. Usually, there will be a shift when it is full acetylated by compared with the wild-type protein.

Sorry for the confusion caused. As the size of the acetyl group is only about 40.6Da, which is thousands of times smaller than the size of the protein, the changes in size of the protein before and after modification cannot be seen with the naked eye.

L287 - Where is Figure 7C?

We are sorry to confuse you. It has been corrected.

- Here the citation might be Figure 7A but not Figure 7B.

Thank you for your suggestion. It has been corrected.

L290 - It is difficult to read here, please rearrange this Figure S8. There is no useful label.

Thank you for your suggestion. It has been corrected.

- The citation of Figure S8 is wrong.

Thank you for your suggestion. It has been corrected.

- For Figure S8, please add the label on the figure. And add anti-GST western blot as well. Because the GST is about 26KD, why are the purified recombinant truncated proteins (GST-fusion) so small?

Sorry for the inconvenience caused. The truncated fragment used for recombinant purification in Figure S8 is very small, and when converted to protein, it is approximately between 1-5kDa. Therefore, the resulting protein is also very small.

- Why there are two Figure S8 in the supplemental materials?

We are sorry to confuse you. It has been corrected.

L293 - Where is Figure 7D?

We are sorry to confuse you. It has been corrected.

L297-313 - Please provide the MS result of the ICDK388?

Author response image 2.

The mass spectrum of Kac modification on ICD protein at K388 site.

Dear reviewer, we are pleased to present the mass spectrum data pertaining to the Kac modification at the K388 site of the ICD protein in Δ_ahcobQ_ strain in Figure2 in this responding letter. It is important to clarify that, while we have not directly validated the Kac status of site-specific lysine acetylation at the recombinant ICD K388 site through mass spectrometry (MS) in this particular study, we have strong reasons to believe in its specificity.

Firstly, our confidence stems from the well-established and rigorously validated two-plasmid system methodology for site-directed acetylation modification. This approach has been successfully employed in modifying diverse and specific sites across various proteins, as evidenced by the pioneering work of David et al. in Nature Chemical Biology (2017, 13(12), 1253-1260).

Secondly, we have taken meticulous measures to ensure the accuracy and reliability of our findings. This includes double-checking our PCR primers and DNA sequencing for the genetic code expansion technology employed. Furthermore, we have included control experiments utilizing proteins that were not subjected to site-directed acetylation (ICD), as detailed in Figure 8A in revised manuscript, thereby providing an additional layer of validation and reinforcing the robustness of our results.

We believe that these two lines of evidence, combined with our rigorous experimental design and execution, provide a solid foundation for our conclusion regarding the specific acetylation of the K388 site in ICD.

- Please provide the whole PAGE gel of loading control. Or other anti-His results?

Dear esteemed reviewer, we sincerely apologize for any confusion our previous presentation may have caused. We would like to clarify that the bottom panel of Figure S6 depicts a Coomassie Blue R-350 stained whole PVDF membrane, rather than a PAGE gel, as may have been mistakenly inferred. To facilitate a comprehensive understanding, we have included the entire stained PVDF membranes in Supplementary Material 1.

- Do you have site-specific antibody of ICDK388? It should be better to identify the ICDK388 with site-specific anti-acetylation antibody.

Thank you for your insightful suggestion. We fully concur that a site-specific antibody targeting ICDK388 would be an optimal tool to elucidate the impact of CobQ on the acetylation status (Kac) of this protein. Unfortunately, we are currently without such an antibody due to the intricate and time-consuming process of its production, which also requires rigorous validation to ensure specificity. Furthermore, the cost associated with its development is considerable.

To address this limitation, in the present manuscript, we have innovatively employed a two-plasmid system for site-directed acetylation modification of ICDK388. This method, which has been extensively validated and utilized in modifying diverse specific sites (David et al., Nature Chemical Biology, 2017, 13(12), 1253-1260), allowed us to precisely manipulate the acetylation status of our target protein. Additionally, we incorporated control experiments using proteins that were not subjected to site-directed acetylation, as depicted in Figure 8A in revised manuscript, thereby reinforcing the robustness and reliability of our findings.

- Please give some background information about K388 site of ICD in the context.

Thank you for your suggestion. It has been added.

L484 - Could you provide the reference for this assay method "Protein deacetylation assay in vitro"?

Thank you for your suggestion. The work published in science 327, 1004 (2010) and Nat. Protoc.5, 1583-1595.

L490 - There is no detailed information about the growh condition for the quantitative acetylome analysis. Without these information, the proportion of the Kac peptides doesn't make any sense.

Thank you for your suggestion. It has been added.

L531 - Insert one line before the paragraph of Western blot.

Thank you for your suggestion. It has been inserted.

Reviewer #3 (Recommendations For The Authors):

Tables S1 and S2 are missing. I could not fully understand the manuscript without them.

We are sorry to confuse you.The data has been uploaded in the supplementary materials.

Line 130. The gene IDs of AhCobB and AhAcuC should be presented.

Thank you for your suggestion. It has been presented.

Line 285. What is different between ArcA and ArcA-2? Please clarify.

Thank you for your suggestion. ArcA is aerobic respiration control protein ArcA, gene name AHA_3026 (https://www.uniprot.org/uniprotkb/A0KMM9/entry). ArcA-2 is arginine deiminase, which gene name is AHA_4093  (https://www.uniprot.org/uniprotkb/A0KQG6/entry). Therefore, they are different proteins according to Uniport annotation.

Line 303. 8further, a bug?

We are sorry to confuse you. It has been corrected.

Line 412-416. The related papers on ICD acetylation in E. coli should be cited.

We are sorry to confuse you. It has been added.

Line 478. Not in vivo but in vitro?

Sorry to confuse you. It should be in vitro. We have revised in the updated manuscript.

Figure 3C and 3D. The image resolution is bad. The figures should be improved so that readers to know easily that Kac is exactly incorporated at the target site.

Thank you for your suggestion. It has been corrected.

Figure 4B. The amino acid residues of the whole AhCobB should be 1-264 aa.

Thank you for your suggestion. It has been corrected.

Figure 8. It would be better to use the same colors between panels C and D. It should be shown the significance between ICD-Kac388 and ICD-Kac388+AhCobB to support the authors' conclusion that AhCobQ activates ICD by deacetylation at K388.

Thank you for your suggestion. It has been adjusted.

eLife assessment

In this valuable study, the authors studied a novel Zn2+- and NAD+-independent KDAC protein, AhCobQ, in Aeromonas hydrophila, which lacks homology with eukaryotic counterparts, thus underscoring its unique evolutionary trajectory within the bacterial domain. They attempt to demonstrate deacetylase activity, however, assays to detect this are still incomplete and require further refinement. The work will be of interest to microbiologists studying metabolism and post-translational modifications.

Reviewer #1 (Public review):

Summary:

This study by Wang et al. identifies a new type of deacetylase, CobQ, in Aeromonas hydrophila. Notably, the identification of this deacetylase reveals a lack of homology with eukaryotic counterparts, thus underscoring its unique evolutionary trajectory within the bacterial domain.

Strengths:

The manuscript convincingly illustrates CobQ's deacetylase activity through robust in vitro experiments, establishing its distinctiveness from known prokaryotic deacetylases. Additionally, the authors elucidate CobQ's potential cooperation with other deacetylases in vivo to regulate bacterial cellular processes. Furthermore, the study highlights CobQ's significance in the regulation of acetylation within prokaryotic cells.

Weaknesses:

The problem I raised has been well resolved. I have no further questions.

Reviewer #2 (Public review):

In recent years, lots of researchers tried to explore the existence of new acetyltransferase and deacetylase by using specific antibody enrichment technologies and high resolution mass spectrometry. Here is an example for this effort. Yuqian Wang et al. studied a novel Zn2+- and NAD+-independent KDAC protein, AhCobQ, in Aeromonas hydrophila. They studied the biological function of AhCobQ by using biochemistry method and MS identification technology to confirm it. These results extended our understanding of the regulatory mechanism of bacterial lysine acetylation modifications. However, I find this conclusion is a little speculative, and unfortunately, it also doesn't totally support the conclusion as the authors provided.

Reviewer #3 (Public review):

Summary:

This study reports on a novel NAD+ and Zn2+-independent protein lysine deacetylase (KDAC) in Aeromonas hydrophila, termed as AhCobQ (AHA_1389). This protein is annotated as a CobQ/CobB/MinD/ParA family protein and does not show similarity with known NAD+-dependent or Zn2+-dependent KDACs. The authors showed that AhCobQ has NAD+ and Zn2+-independent deacetylase activity with acetylated BSA by western blot and MS analyses. They also provided evidence that the 195-245 aa region of AhCobQ is responsible for the deacetylase activity, which is conserved in some marine prokaryotes and has no similarity with eukaryotic proteins. They identified target proteins of AhCobQ deacetylase by proteomic analysis and verified the deacetylase activity using site-specific Kac proteins. Finally, they showed that AhCobQ activates isocitrate dehydrogenase by deacetylation at K388.

Strengths:

The finding of a new type of KDAC has a valuable impact on the field of protein acetylation. The characters (NAD+ and Zn2+-independent deacetylase activity in an unknown domain) shown in this study are very unexpected.

Weaknesses:

(1) The characters (NAD+ and Zn2+-independent deacetylase activity in an unknown domain) shown in this study are very unexpected. To convince readers, MSMS data must be necessary to accurately detect (de)acetylation at the target site in the deacetylase activity assay. The authors showed the MSMS data in assays with acetylated BSA, but other assays only rely on western blot.

(2) They prepared site-specific Kac proteins and used them in deacetylase activity assays. Incorporation of acetyllysine at the target site should be confirmed by MSMS and shown as supplementary data.

(3) The authors imply that the 195-245 aa region of AhCobQ may represent a new domain responsible for deacetylase activity. The feature of the region would be of interest but is not sufficiently described in Figure 5. The amino acid sequence alignments with representative proteins with conserved residues would be informative. It would be also informative if the modeled structure predicted by AlphaFold is shown and the structural similarity with known deacetylases is discussed.

eLife assessment

This valuable study has characterized the unique expression of Schlemm's canal endothelial cells (SECs) using FACS-sorted specific cell bulk RNA-Seq and scRNA-/snRNA-Seq of mouse SECs. The compelling study identified novel biomarkers for SECs and molecular markers for two inner wall SEC states and outwall SECs in mouse eyes. Significant gene networks and pathways were elucidated for their potential contribution to glaucoma pathogenesis, providing targets for further research in relation to glaucoma.

Reviewer #1 (Public review):<br /> <br /> Summary:

Balasubramanian et al. characterized the cell types comprising mouse Schlemm's canal (SC) using bulk and single cell RNA sequencing (scRNA-seq). The results identify expression patterns the delineate the SC inner and outer wall cells and two inner wall 'states'. Further analysis demonstrates expression patterns of glaucoma associated genes and receptor ligand pairs between SEC's and neighboring trabecular meshwork.

Strengths:

While mouse SC has been profiled in previous scRNA-seq studies (van Zyl et al 2020, Thomson et al 2021), these data provide higher resolution of SC cell types, particularly endothelial cell (SEC) populations. SC is an important regulator of anterior chamber outflow and has important consequences for glaucoma.

Comments on the latest version:

The authors have addressed my primary concerns with the first version of the manuscript. This study represents a valuable resource in the molecular characterization of mouse Schlemm's canal cell types.

Reviewer #2 (Public review):

Summary:

This revised article has characterized the mouse Schlemm's canal expression profile using a comprehensive approach based on sorted SEC, LEC, and BEC total RNA-Seq, scRNA-Seq, and snRNA-Seq to enrich the selection of SECs. The revised study has successfully profiled genome-wide gene expression using sorted SECs, demonstrating that SECs have a closer similarity to LECs than BECs. The combined scRNA- and snRNA-Seq data with deep coverage of gene expression led to the successful identification of many novel biomarkers for inner wall SECs, outer wall SECs, collector channel ECs, and pericytes. In addition, the study also identified two novel states of inner wall SECs separated by new markers. The study provides significant novel information about the biology and expression profile of SECs in the inner and outer walls. It is of great significance to have this novel, convincing, and comprehensive study led by leading researchers published in this journal. The revision has improved the clarity and significance of the study with more details.

Strengths:

This is a comprehensive study using various data to support the expression characterization of mouse SECs. First, the study profiled genome-wide expression using sorted SECs, LECs, and BECs from the same tissue/organ to identify the similarities and differences among the three types of cells. Second, snRNA-Seq was applied to enrich the number of SECs from mouse ocular tissues significantly. Increased sampling of SECs and other cells led to more comprehensive coverage and characterization of cells, including pericytes. Third, the combined scRNA- and snRNA-Seq data analyses increase the power to further characterize the subtle differences within SECs, leading to identifying the expression markers of Inner and Outer wall SECs, collector channel ECs, and distal region cells. Fourth, the identified unique markers were validated for RNA and protein expression in mouse ocular tissues. Fifth, the study explored how the IOP- and glaucoma-associated genes are expressed in the ScRNA- and snRNA-Seq data, providing potential connections of these GWAS genes with IOP and glaucoma. Sixth, the initial pathway and network analyses generated exciting hypotheses that could be tested in other independent studies.

Weaknesses:

The authors have addressed most of the previous comments by adding more details about the protocol and additional discussions. Several comments requiring additional experimental data have been addressed as future directions, such as protein validation, RNA expression validation in human samples, and GWAS-identified IOP genes.

Comments on the latest version:

The authors have addressed previous comments responsively. The authors have suggested several experiments to be completed in the future since these could be time-consuming with human samples. The revised article is with better clarity and clearer significance. No additional comments.

Author response:

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

Reviewer #1 (Public Review): 

Summary: 

Balasubramanian et al. characterized the cell types comprising mouse Schlemm's canal (SC) using bulk and single-cell RNA sequencing (scRNA-seq). The results identify expression patterns that delineate the SC inner and outer wall cells and two inner wall 'states'. Further analysis demonstrates expression patterns of glaucoma-associated genes and receptor-ligand pairs between SEC's and neighboring trabecular meshwork. 

Strengths: 

While mouse SC has been profiled in previous scRNA-seq studies (van Zyl et al 2020, Thomson et al 2021), these data provide higher resolution of SC cell types, particularly endothelial cell (SEC) populations. SC is an important regulator of anterior chamber outflow and has important consequences for glaucoma. 

We thank the reviewers for their thorough reading of our manuscript and their insightful comments.

Weaknesses: 

(1) Since SC has previously been characterized in mouse, human, and other species by scRNA-seq in other studies, this study would benefit from more direct comparisons to published datasets. For example, Table 4 could be expanded to list the SC cell numbers profiled in each study. Expression patterns highlighted in this study could be independently verified by plotting in publicly available mouse SC datasets. Further, a comparison to human expression patterns would assess whether type-specific expression patterns are conserved. Alternatively, an integrated analysis could be performed. Indeed, the authors mention that an integrated analysis was attempted but the data is not shown. It is unclear if this was because of a lack of agreement between datasets or other reasons.

Table 4 now includes an expanded list of SC cell numbers in each study. We profiled the expression of Npnt, Selp, and Ccl21a in the Thomson et al., 2021 dataset and have included the concurring results in Figure S5. We were unable to do a similar profile using the Van Zyl., 2020 dataset due to small SC numbers. As previously mentioned, differences such as read depth, strain of animals used (including pigmented vs albino), method of cell isolation (including drug exposure), and number of cells profiled raise a significant impediment to integration with previously published datasets. A comparison to human atlas is a focus of future work.

(2) Figure 1 presents bulk RNA seq results comparing SEC, BEC, and LEC expression patterns. These populations were isolated using cell surface markers and enrichment by FACS. Since each EC population is derived from the same sample, the accuracy of this data hinges on the purity of enrichment. However, a reference is not given for this method and it is not clear how purity was validated. The authors later note that marker Emcn, which was used to identify BECs, is also expressed in SECs and LECs at lower levels. It should be demonstrated that these populations are clearly separated by flow cytometry. 

We have added the following clarifying text to the methods section: Forward and side scatter gates were first used to eliminate events with low scatter which include debris, cell fragments and pyknotic cells. Then propidium iodide positive dead cells were gated out. Further gating on the viable cells was applied such that distinct population of cells were isolated a) SECs: GFP+Lvye1-, b) LECs: GFP+ Lyve1+, c) GFP- BECs: Endomucin+.

We show here a representative of the flow sort showing the clear distinction in SEC and LEC cell isolation.

Author response image 1.

Flow sorted SEC and LEC. We obtained two distinct populations; 1. SEC cells (GPF+LYVE1--blue) 2. LEC (GPF+LYVE1+- red). Note eFluor 660 emission was collected using the Alexa647 (A647) setting of the flow cytometer. Additionally, SEC marker expression from bulk RNA-seq aligns with signature gene expression from SECs in single cell RNA-seq (Figure S3).

(3) Bulk RNA-seq analysis infers similarity from the number of DEGs between samples, however, this is not a robust indicator. A correlation analysis should be run to verify conclusions. 

We have provided a heatmap with hierarchical clustering based on Euclidean distance of the EC subtypes (Figure 1B) analyzed by bulk RNA seq in addition to number of DE genes between subtypes.

(4) Figures 2-4 present three different datasets targeting the same tissue: 1) C57bl/6j scRNA-seq, 2) C57bl/6j snRNA-seq, 3) 129/sj scRNA-seq. Integrated analysis comparing datasets #1 to #2 and #3 is also presented. Integration methods are not described beyond 'normalization for cell numbers'. It is unclear if additional alignment methods were used. Integration across each of these datasets needs careful consideration, especially since different filtering methods were used (e.g. <20% mito in scRNA-seq and <5% in snRNA-seq). Improper integration could affect the ability to cluster or exaggerate differences between cell/types and states. It would be useful to demonstrate the contribution of different samples and datasets to each cell type/state to verify that these are not driven by batch effects, mouse strain, or collection platform. 

We agree that integration should be performed with careful consideration to confounding factors. We demonstrate the contribution of different samples and datasets to show how our datasets integrated well (we had added panels to Figure 3C and 4C) and that cell types/states contribution was uniformly distributed across methods (C57BL/6J single cell and single nuc) and backgrounds (C57BL/6J and 129/Sj) were not a result of integration.

(5) IW1 and IW2 are not well separated, and it is unclear if these represent truly different cell states. Figure 5b shows the staining of CCL21A and describes expression in the 'posterior portion' but in the image there are no DAPI+ nuclei in the anterior portion, suggesting the sampling in this section is different from Figure 5a. This would be improved by co-staining NPNT and CCL21A to demonstrate specificity. 

Since both our antibodies are derived from the same species (goat), a co-labeling wasn’t possible. To be prudent, we used adjacent sections, flat-mounts, and RNAscope and provided further evidence of the anterior/posterior “bias” in supplemental figures.

(6) The substructures observed within clusters in sc/snRNA-seq data suggest that overall profiling may still not be comprehensive. This should be noted in the discussion. 

We agree and have added this note in the discussion: “With greater sampling and deeper transcriptomic depth, it is likely that additional SEC cell states/types will be identified.”

Reviewer #2 (Public Review):

Summary: 

This article has characterized the mouse Schlemm's canal expression profile using a comprehensive approach based on sorted SEC, LEC, and BEC total RNA-Seq, scRNA-Seq, and snRNA-Seq to enrich the selection of SECs. The study has successfully profiled genome-wide gene expression using sorted SECs, demonstrating that SECs have a closer similarity to LECs than BECs. The combined scRNA- and snRNA-Seq data with deep coverage of gene expression led to the successful identification of many novel biomarkers for inner wall SECs, outer wall SECs, collector channel ECs, and pericytes. In addition, the study also identified two novel states of inner wall SECs separated by new markers. The study provides significant novel information about the biology and expression profile of SECs in the inner and outer walls. It is of great significance to have this novel, convincing, and comprehensive study led by leading researchers published in this journal. 

Strengths: 

This is a comprehensive study using various data to support the expression characterization of mouse SECs. First, the study profiled genome-wide expression using sorted SECs, LECs, and BECs from the same tissue/organ to identify the similarities and differences among the three types of cells. Second, snRNA-Seq was applied to enrich the number of SECs from mouse ocular tissues significantly. Increased sampling of SECs and other cells led to more comprehensive coverage and characterization of cells, including pericytes. Third, the combined scRNA- and snRNA-Seq data analyses increase the power to further characterize the subtle differences within SECs, leading to identifying the expression markers of Inner and Outer wall SECs, collector channel ECs, and distal region cells. Fourth, the identified unique markers were validated for RNA and protein expression in mouse ocular tissues. Fifth, the study explored how the IOP- and glaucoma-associated genes are expressed in the ScRNA- and snRNA-Seq data, providing potential connections of these GWAS genes with IOP and glaucoma. Sixth, the initial pathway and network analyses generated exciting hypotheses that could be tested in other independent studies. 

We thank the reviewer for their comments on the strengths of this study.

Weaknesses: 

A few minor weaknesses have been noted. First, since snRNA-Seq and scRNA-Seq generated different coverage of expressed genes in the cells, how did the combined analyses balance the un-equal sequencing coverage and missing data points in the snRNA-Seq data? Second, the RNA/protein validation of selected SEC molecular markers was done using mouse anterior segment tissues. It would be more helpful to examine whether these molecular markers for SECs could work well in human SECs. Third, the effort to characterize the GWAS-identified IOP- and glaucoma-associated genes is exciting but with limited new information. Additional work could be performed to prioritize these genes.

Integration of sc-Seq and sn-Seq data: We have addressed a similar integration question from reviewer 1 and have now included a plot showing the distribution of cells upon integration. Integration methods are not perfect and generally result in some loss of data especially when datasets of un-equal sequencing coverage are integrated. However, we did not observe any obvious differences between the original (un-integrated) and integrated datasets. We also noted that cell types/states contribution was similarly distributed across methods (C57BL/6J single cell and single nuc) and backgrounds (C57BL/6J and 129/Sj) and clustering were not a result of batch-effects.

We agree about the human relevance of SEC markers, and this will be a focus of future work.

Another focus of our future work is to understand how GWAS identified IOP and glaucoma genes change in disease states.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Minor: 

(1) Figure 5- DAPI should be listed in the legend. 

(2) Figure 5- It would be helpful to label IW1 and IW2 regions in the UMAPs. 

We have incorporated the suggestions in Figure 5 and legend.

Reviewer #2 (Recommendations For The Authors): 

(1) The study has validated RNA/protein expression of the selected biomarkers for IW/OW SECs in mouse eyes. It would be more helpful to confirm that these newly identified molecular biomarkers for SECs could apply to human eyes. This could be examined through available human scRNA-/snRNA-Seq data or targeted RNA and protein staining experiments. The additional validation in human SECs would make the current discovery more convincing. 

We agree with the importance of validation in human samples, and is the scope of future work.

(2) The combination of scRNA-Seq and snRNA-Seq from three batches of experiments increased the statistical power to identify subtypes of SECs. It would be helpful to include more details on how the qc, missing data, and normalization across different batches were dealt with. 

We have incorporated more details in the methods section of the paper.

(3) The authors explored the underlying molecular connection between the newly identified IOP/glaucoma-associated genes using the newly generated SEC-targeted scRNA/snRNA-Seq data. Many of these associated genes were present in the same SEC cells. It would be interesting to see how many of these genes' expression levels are correlated with each other via a network. These potential correlation networks across SECs could lead to identifying novel upstream regulators or network hubs, which could target many IOP-associated genes for future studies. 

We agree with the importance of a correlation network analysis, but this is a focus of future work, especially in normal and disease states.

eLife assessment

This important study introduces and evaluates the efficacy of a novel form of non-invasive brain stimulation in humans: kilohertz transcranial magnetic perturbation (kTMP). The evidence provided for the ability of kTMP to increase cortical excitability with minimal sensation is compelling, with two separate replication experiments. Although exploratory in nature, this work represents new avenues for non-invasive brain stimulation research that has potential long-term appeal for both clinical and research applications. This paper will be of significant interest to neuroscientists interested in brain stimulation.

Reviewer #1 (Public review):

Summary:

This paper reports the first results on the effects of a novel waveform for weak transcranial magnetic stimulation, which is refered to as "perturbation" (kTMP). The waveform is sinusoidal at kHz frequency with subthreshold intensities of 2V/m, instead of the suprathreshold pulses used in conventional TMS (~100V/m). The effect reported here concerns motor-evoked potentials (MEPs) elicited on the hand with single-pulse TMS. These MEPs are considered a marker of "corotico-spinal excitability". The manuscripts report that kTMP at 3.5kHz enhances MEPs with a medium effect size, with independent replication of this finding on 3 separate cohorts of subjects (N=16, 15, 16). This result is important for the field of non-invasive brain stimulation. The evidence in support of this claim is compelling. Despite the replications, this remains an exploratory study that will require replication with adequately powered planned comparisons.

Strengths:

• This is a novel modality for non-invasive brain stimulation.<br /> • Knowing the history in this field, this is likely to lead to a large number of follow-up studies in basic and clinical research.<br /> • The modality causes practically no sensation, which makes it perfectly suitable for control conditions. Indeed, the study itself used a persuasive double-blinding procedure.<br /> • The replication of the main result in two subsequent experiments is very compelling.<br /> • The effect size of Cohen's d=0.5 is very promising.<br /> • It is nice the E-fields were measured on a phantom, in addition to modeling.

Weakness:

• Statistical analysis combining Experiments 1, 2, 3 after inspecting the data is inappropriate.<br /> • Post-hoc definition of outliers that were removed is unfortunate.<br /> • While sensation has been documented, blinding was not directly assessed.<br /> • Despite the replications, this remains an exploratory study as it lacks power analysis and planned comparisons.

Other comments from an earlier review were adequately addressed.

Reviewer #2 (Public review):

Summary:

kTMP is a novel method of stimulating the brain using electromagnetic fields. It has potential benefits over existing technology because it is a safe and easy technology. It explores a range of brain frequencies that has not been explored in depth before (2-5kHz) and thus offers new opportunities.

Strengths:

This work relied on standard methods and was carefully and conservatively performed.

Weaknesses:

There were few weaknesses. The sham condition was prepared as well as could be done, but sham is always challenging in a treatment with sound and sensation, and with knowledgeable operators. New technology, also, is very exciting to subjects and it is difficult to achieve a natural experiment. These difficulties are related to the technology, however, and not to the execution of these experiments..

Author response:

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

Response to Public Comments

(1) BioRxiv version history.

Reviewer 1 correctly noted that we have posted different versions of the paper on bioRxiv and that there were significant changes between the initial version and the one posted as part of the eLife preprint process. Here we provide a summary of that history.

We initially posted a bioRxiv preprint in November, 2021 (Version I) that included the results of two experiments. In Experiment 1, we compared conditions in which the stimulation frequency was at 2 kHz, 3.5 kHz, or 5.0 kHz. In Experiment 2, we replicated the 3.5 kHz condition of Experiment 1 and included two amplitude-modulated (AM) conditions, with a 3.5 kHz carrier signal modulated at 20 Hz or 140 Hz. Relative to the sham stimulation, non-modulated kTMP at 2 kHz and 3.5 kHz resulted in an increase in cortical excitability in Experiment 1. This effect was replicated in Experiment 2.

In the original posting, we reported that there was an additional boost in excitability in the 20 Hz AM condition above that of the non-modulated condition. However, in re-examining the results, we recognized that the 20 Hz AM condition included an outlier that was pulling the group mean higher. We should have caught this outlier in the initial submission given that the resultant percent change for this individual is 3 standard deviations above the mean. Given the skew in the distribution, we also performed a log transform on the MEPs (which improves the normality and homoscedasticity of MEP distributions) and repeated the analysis. However, even here the participant’s results remained well outside the distribution. As such, we removed this participant and repeated all analyses. In this new analysis, there was no longer a significant difference between the 20 Hz AM and non-modulated conditions in Experiment 2. Indeed, all three true stimulation conditions (non-modulated, AM 20 Hz, AM 140 Hz) produced a similar boost in cortical excitability compared to sham. Thus, the results of Experiment 2 are consistent with those of Experiment 1, showing, in three new conditions, the efficacy of kHz stimulation on cortical excitability. But the results fail to provide evidence of an additional boost from amplitude modulation. 

We posted a second bioRxiv preprint in May, 2023 (Version 2) with the corrected results for Experiment 2, along with changes throughout the manuscript given the new analyses.

Given the null results for the AM conditions, we decided to run a third experiment prior to submitting the work for publication. Here we used an alternative form of amplitude modulation (see Kasten et. al., NeuroImage 2018). In brief, we again observed a boost in cortical excitability in from non-modulated kTMP at 3.5 kHz, but no additional effect of amplitude modulation.  This work is included in the third bioRrxiv preprint (Version 3), the paper that was submitted and reviewed at eLife.

(2) Statistical analysis.

Reviewer 1 raised a concern with the statistical analyses performed on aggregate data across experiments.  We recognize that this is atypical and was certainly not part of an a priori plan. Here we describe our goal with the analyses and the thought process that led us to combine the data across the experiments.

Our overarching aim is to examine the effect of corticospinal excitability of different kTMP waveforms (carrier frequency and amplitude modulated frequency) matched at the same estimated cortical E-field (2 V/m). Our core comparison was of the active conditions relative to a sham condition (E-field = 0.01 V/m). We included the non-modulated 3.5 kHz condition in Experiments 2 and 3 to provide a baseline from which we could assess whether amplitude modulation produced a measurable difference from that observed with non-modulated stimulation. Thus, this non-modulated condition as well as the sham condition was repeated in all three experiments. This provided an opportunity to examine the effect of kTMP with a relatively large sample, as well as assess how well the effects replicate, and resulted in the strategy we have taken in reporting the results. 

As a first step, we present the data from the 3.5 kHz non-modulated and sham conditions (including the individual participant data) for all three experiments in   4. We used a linear mixed effect model to examine if there was an effect of Experiment (Exps 1, 2, 3) and observed no significant difference within each condition. Given this, we opted to pool the data for the sham and 3.5 kHz non-modulated conditions across the three experiments. Once data were pooled, we examined the effect of the carrier frequency and amplitude modulated frequency of the kTMP waveform. 

(3) Carry-over effects

As suggested by Reviewer 1, we will examine in the revision if there is a carry-over effect across sessions (for the most part, 2-day intervals between sessions). For this, we will compare MEP amplitude in baseline blocks (pre-kTMP) across the four experimental sessions.

Reviewer 1 also commented that mixing the single- and paired-pulse protocols might have impacted the results. While our a priori focus was on the single-pulse results, we wanted to include multiple probes given the novelty of our stimulation method. Mixing single- and different paired-pulse protocols has been relatively common in the non-invasive brain stimulation literature (e.g., Nitsche 2005, Huang et al, 2005, López-Alonso 2014, Batsikadze et al 2013) and we are unaware of any reports suggested that mixed designs (single and paired) distort the picture compared to pure designs (single only).

(4) Sensation and Blinding

Reviewer 2 bought up concerns about the sham condition and blinding of kTMP stimulation. We do think that kTMP is nearly ideal for blinding. The amplifier does emit an audible tone (at least for individuals with normal hearing) when set to an intensity to produce a 2 V/m E-field. For this reason, the participants and the experimenter wore ear plugs. Moreover, we played a 3.5 kHz tone in all conditions, including the sham condition, which effectively masked the amplifier sound. We measured the participant’s subjective rating of annoyance, pain, and muscle twitches after each kTMP session (active and sham). Using a linear mixed effect model, we found no difference between active and sham for each of these ratings suggesting that sensation was similar for active and sham (Fig 8). This matches our experience that kHz stimulation in the range used here has no perceptible sensation induced by the coil. To blind the experimenters (and participants) we used a coding system in which the experimenter typed in a number that had been randomly paired to a stimulation condition that varied across participants in a manner unknown to the experimenter.

Reviewer 1 asked why we did not explicitly ask participants if they thought they were in an active or sham condition. This would certainly be a useful question. However, we did not want to alert them of the presence of a sham condition, preferring to simply describe the study as one testing a new method of non-invasive brain stimulation. Thus, we opted to focus on their subjective ratings of annoyance, pain, and finger twitches after kTMP stimulation for each experimental session.

Response to Recommendations for the Authors

Reviewer #1: 

Reviewer # 1 in the public review noted the possibility of carry-over effects and suggested that we compare the amplitude of the MEPS in the pre blocks across the four sessions.

Although we did not anticipate carry-over effects lasting 2 or more days, we have now conducted an analysis in which we use a linear mixed effect model with a fixed factor of Session and a random factor of Participant. The results show that there is not an effect of session [χ2(3) = 4.51, p \= 0.211].

Author response table 1.

Detailed comments and some suggestions to maybe improve the writing and figures: 

Abstract: 

BioRxiv Version 1: "We replicated this effect in Experiment 2 and found that amplitude-modulation at 20 Hz produced an additional boost in cortical excitability. " 

BioRxiv Version 2, 3 and current manuscript: "Although amplitude-modulated kTMP increased MEP amplitude compared to sham, no enhancement was found compared to non-modulated kTMP." 

I am a little concerned about this history because the conclusions seem to have changed. It looks like the new data has a larger number of subjects, which could explain the divergence. Although it is generally not good practice to analyze the data at interim time points, without accounting for alpha spending. It appears that data analysis methods may have also changed, as some of the extreme points in version 1 seem to be no longer in the new manuscript (Figure 4 Sham Experiment 1). 

In the public review above we explain in detail the different versions of the bioRxiv preprint and how the results changed from the first version to the current manuscript.

Introduction: <br /> "Second, the E-fields for the two methods exist in orthogonal subspaces" Can you explain what this means? 

Thank you for this suggestion, we have updated the paper (pg. 4, line 78-81) by adding two sentences to explain what we mean by orthogonal subspaces and describe the consequences of this with respect to the E-fields resulting from tES and TMS. Specifically, we now comment that even if the E-fields of tES and TMS are similar in focality, they may target different populations of neurons.  

"In addition, the kTMP waveform can be amplitude modulated to potentially mimic E-fields at frequencies matching endogenous neural rhythms [15]." That may be so, but reference [15] makes the exact opposite point, namely, that kHz stimulation has little effect on neuronal firing until you get to very strong fields. The paper that makes that claim is by Nir Grossman, but in my view, it is flawed as responses are most likely due to peripheral nerve (axon) stimulation there given the excessive currents used in that study. The reference to Wang and Peterchev [17] is in agreement with that by showing that you need 2 orders of magnitude stronger fields to activate neurons. 

The reviewers are correct that that Ref 15 (Esmaeilpour et al, 2021), as well as Wang et al, 2023 use much higher E-fields than we target in our present study. However, our point here is that, while we cannot use our approach to apply E-fields at endogenous frequencies, we can do amplitude modulation of the kHz carrier frequency at these lower frequencies. We cited Esmaeilpour et al., (2021) because they show that high frequency stimulation with amplitude-modulated waveforms resulted in dynamic modulation at the “beating” frequency. Given we are well in subthreshold space in this paper, and well below the E-field levels in Esmaeilpour et al (2021), the open question is whether amplitude modulation at this level will be able to perturb neural activity (e.g., increase power of endogenous oscillations at the targeted frequency). 

To address this concern, we modified the sentence (pg.6, lines 120-121) to now read "In addition, the kTMP waveform can be amplitude modulated at frequencies matching endogenous neural rhythms." In this way, we are describing a general property of kTMP (as well as other methods that can use high frequency signals).

I am not aware of any in-vitro study showing the effects of kHz stimulation at 2V/m. The review paper by Neudorfer et al is very good. But if I got it correctly in a quick read it is not clear that there is experimental evidence for subthreshold effects. They do talk about facilitation, but the two experimental papers cited there on the auditory nerve don't quantify field magnitudes. I would really love it if you could point me to a relevant empirical study showing the effects of kHz stimulation at 2 V/m. 

Perhaps all this is a moot point as you are interested in lasting (plastic) effects on MEP. For this, you cite one study with 11 subjects showing the effects of kHz tACS on MEPs [20]. I guess that is a start. The reference [21] is only a safety study, so it is probably not a good reference for that. Reference [22] also seems out of place as it is a modeling study. The effects on depression of low-intensity magnetic stimulation in references [23-26] are intriguing. 

We agree with the reviewer that Ref 20 (now Ref 18: Chaieb, Antal & Paulus; 2011) is the most relevant one to cite here since it provides empirical evidence for changes in neural excitability from kHz stimulation, and in fact, serves as the model for the current study. We have retained Refs 23-26 (now Ref 19-22: Rohan et al., 2014; Carlezon et al., 2005; Rohan et al., 2004 & Dublin et al., 2019) since they also do show kHz effects on mood and removed Refs 21 (Chaieb et al., 2014) and 22 (Wang et al., 2018) for the reasons cited by the Reviewer.

Figure 1: "The gray dashed function depicts the dependence of scalp stimulation threshold upon frequency [14]." It's hard to tell from that reference what the exact shape is, but the frequency dependence is likely steeper than what is shown here, i.e. 2 mA at 10 Hz can be really quite unpleasant. 

We have removed the gray dashed line given that this might be taken to suggest a discrete transition. We now just have a graded transition to reflect that the tolerance of tES is subjective. We start the shading at 2 mA for the lowest frequencies given that there is general agreement that 2 mA is well-tolerated and decrease the shading intensity as frequency increases. The general aim of the figure is not to make strong claims about the threshold of scalp discomfort for tES, but to show that kTMP can target much higher cortical E-fields within the tolerable range.

Methods: <br /> Procedures: <br /> It does not seem like double-blinding has been directly assessed. 

We did not assess double blinding by directly assessing whether the participant was in a sham or active condition. We did not want to alert the participants of the presence of a sham condition after the first session of the 4-session study, preferring to simply describe the study as a test of a new method of non-invasive brain stimulation. For this reason, we opted to focus on their subjective ratings of annoyance, pain, and finger twitches after kTMP stimulation for each experimental session. These ratings did not differ between active and sham kTMP, which suggests kTMP has good potential for double blinding.

MEP data analysis: Taking the mean of log power is unusual, but I suppose the reference provided gives a good justification. Does this explain the deviation from the biorxiv v1 results? 

We opted to perform a logarithmic transformation of MEP amplitudes to improve the normality and homoscedasticity of the MEP distribution. We cite three papers (Refs 50-52: Peterchev et al., 2013, Nielsen 1996a, & Nielsen 1996b) that have applied a similar approach in handling MEP data. We had not done the transformation in the first bioRxiv but opted to do so in the eLife submission based on further review of the literature. We note that the two analyses produce similar statistical outcomes once we removed the outlier discussed in the Public Review.

"Interactions were tested by comparing a model in which the fixed effects were restricted to be additive against a second model that could have multiplicative and additive effects." Not sure what this means. Why not run a full model with interactions included and read off the stats from that single model for the various factors? Should one not avoid running multiple models as one would have to correct p-values for multiple comparisons for every new test? 

We used the lme4 package in R to fit our linear mixed effect models (Ref 54: Bates, Mächler, Bolker & Walker, 2015). In this package they intentionally leave out p-values for individual models or factors because they note there is a lack of convergence in the field about how to calculate parameter estimates in complex situations for linear mixed effect models (e.g., unbalanced designs). They suggest model comparison using the likelihood-ratio test to obtain and report p-values, which is what we report in the current manuscript.

We revised the text in the section Linear Mixed Effects Models to state that likelihood ratio tests were used to obtain p-values to remove any confusion.

Procedures: <br /> kTPM: Nice that fields were measured. Would be nice to see the data that established the empirical constant k. 

We have expanded our discussion of how we established k in the Methods section. We first derived k using the equation E0 \= kfcI based on previously published reports of the current (I) and frequency (fc) of the MagVenture Cool-B65 coil (now Refs 29-30: Deng, Lisanby & Peterchev, 2013; Drakaki, Mathiesen, Siebner, Madsen & Thielscher, 2022). We then verified this value using the triangular E-field probe to within 5% error.

Figure 3, spectrum. The placement of the fm label on the left panel is confusing. It suggests that fm was at the edge of the spectrum shown, which would not be the best way to show that there is nothing there - obviously, there isn't, but the figure could be more didactic. 

Thanks for pointing this out. We modified the figure, moving the ‘fm’ label to the center of the first panel. This change makes it clear that there is no peak at the amplitude modulated frequency.

"a trio of TMS assays of cortical excitability" Can you clarify what this means? 

Sorry for the confusion. The trio of TMS assays refers to the single pulse and two paired-pulse protocols (SICI - ICF). We edited the Procedure section to clarify this (pg 9, line 195-197).

Figure 2A: it would be nice to indicate which TMS blocks were single pulse and which were the two paired-pulse protocols. It is hard to keep track of it all for the three different experiments. 

We have now clarified in the text (see above) that all three probes were used in each block for Experiments 1 and 2, and only the single-pulse probe in Experiment 3. We have modified the legend for Figure 2 to also provide this information.

Results: <br /> "Based on these results, we combined the data across the three experiments for these two conditions in subsequent analyses." This strikes me as inappropriate. Should not a single model have been used with a fixed effect of experiment and fixed effect of stimulation condition? 

We recognize that pooling data across experiments may be atypical. Indeed, our initial plan was to simply analyze each experiment on its own (completely within-subject analysis). However, after completing the three experiments, we realized that since the sham and non-modulated 3.5 kHz conditions were included in each experiment, we had an opportunity to examine the effect of kTMP in a relatively large N study (for NIBS research). Before pooling the data, we wanted to make sure that the factor of experiment did not impact the results and our analysis showed there was no effect of experiment. Note that we did not include the factor of stimulation condition in this model because we did not want to do multiple comparisons of the same contrast (3.5 kHz compared to sham). By pooling the data before analysis of the stimulation conditions we could then focus on our two key independent variables: 1) kTMP carrier frequency and 2) kTMP amplitude modulated frequency, doing fewer significance tests to minimize multiple comparisons. The linear mixed effect (LME) model allows us to include a random effect of participant. In this way, we account for the fact that some comparisons are within subjects and some comparisons are between subjects.

The reviewer is correct that after pooling the data, we could have continued to include the factor of experiment in the LME models. This factor could still account for variance even though it was not significant in the initial test. Given this, we have now reanalyzed the data including the fixed factor of experiment in all the comparisons that contain data from multiple experiments. This has led us to modify the text in the Methods section under Linear Mixed Effects Models and in the Results section under Repeated kTMP Conditions (3.5 kHz and Sham) across Experiments. In addition, the results of the LME models have been updated throughout the Results section. We note that the pattern of results was unchanged with this modification of our analyses.

"Pairwise comparisons of each active condition to sham showed that an increase was observed following both 2 kHz ..." I suppose this is all for Experiment 1? It is a little confusing to go back and forth between combining experiments and then separate analyses per experiment without some guiding text, aside from being a bit messy from the statistical point of view. 

We did not go back to performing separate analyses of the experiments after pooling the data. Once we ran the test to justify pooling the data, subsequent tests were done with the pooled data to evaluate the effects of carrier frequency and amplitude modulation.

Figure 5 is confusing because the horizontal lines with ** on top seem to refer to the same set of sham subjects, but the subjects of Experiments 2 and 3 are different from Experiment 1, so in these pairwise comparisons there is a mix of between-subject and within subject-comparison going on here. Did I get that right? 

Yes – that is correct. As noted above we pooled the data after showing that there was no effect of experiment. Thus, the data for the sham and 3.5 kHz non-modulated conditions are from three different experiments. There was some overlap of subjects in Experiments 1 and Experiment 2 (Experiment 3 was all new participants).  We used a linear mixed effect model so that we could account for this mixed design. Participant was always included as a random factor, which allows us to account for the fact that some comparisons are within, and some are between. Based on a previous comment, we now include Experiment as a fixed factor (see above) which provides a way to evaluate variance across the different experiments.

"We next compared sham vs. active non-modulated kTMP and found that active kTMP produced a significant increase in corticospinal excitability [χ2(1) = 23.46 p < 0.001" Is this for the 3.5Hz condition? 

No, that is for an omnibus comparison of non-modulated kTMP (including 2 kHz, 3.5 kHz and 5 kHz conditions) vs. sham. We have edited the paper to include the three conditions that are included as the active non-modulated kTMP conditions for clarity (pg. 22, line 463). Having observed a significant omnibus result, we continued with paired comparisons: “Pairwise comparisons of each active condition to sham showed that an increase was observed following both 2 kHz [χ2(1) = 6.90, p = 0.009; d = 0.49] and 3.5 kHz kTMP [χ2(1) = 37.75, p < 0.001; d = 0.70; Fig 5: Non-Modulated conditions]. The 5 kHz condition failed to reach significance [χ2(1) = 1.43, p = 0.232; d = 0.21].”

Paired-Pulse Assays: There are a number of results here without pointing to a figure, and at one point there is a reference to Figure 6, which may be in error. It would help to point the reader to some visual corresponding the the stats. 

Thank you. This was an error on line 542. It should have read Figure 7. We have added two other pointers to Figure 7 where we discuss the absence of an effect of kTMP on SICI.

Reviewer #2 (Recommendations For The Authors):

I would recommend a couple of changes to the background.

"Orthogonal subspaces" line 78. This is a fairly formal term that has little relevance here, although the difference between scalar and vector potential-based fields is interesting to think about. If it stays, it should be mathematically supported, but it's easily rewritten to deliver the gist of it. 

We have updated the paper by adding text that we hope will clarify what we mean by orthogonal subspaces (pg. 4, line 78-81). We note that we developed the math behind this statement in a previous paper (Ref # 10: Sheltraw et al., 2021). We have changed the location of the citation so that it directly follows these sentences and will provide a pointer to readers interested in the physics and math concerning orthogonal subspaces. 

The statement that the scalp e-field for TES is greater than the e-field for TMS for similar cortical fields needs a little more clarification, since historically they have operated orders of magnitude apart, and it is easy to misread and trip over this statement (although it is factually true). Presenting a couple of numbers at cortical and scalp positions would help illustrate the point. That you are not considering applying TES at traditional TMS levels but rather TMS at TES values is what is initially easy to miss. 

We appreciate the feedback and have updated this section to provide the reader with a better intuition of this point. We now specify that the scalp to cortical E-field ratio is approximately 18 times larger for tES compared to TMS and cite our previous paper which has much more detail about how this was calculated.

A note that the figures show scalp sensation around 1.0 V/m while the text states 0.5; cortical depths are an important thing for the reader to keep in mind. 

This comment, when considered in tandem with one of the comments of Reviewer 1 led us to revise Figure 1. We removed the dashed gray line which might be taken to suggest a strict cutoff in terms of tolerability (which we did not intend). We now use shading that fades away to make the point of continuity. We have extended this down to a cortical E-field of 0.5 V/m to correspond with the text.  

This is a nicely done and carefully reported experiment and I look forward to seeing more. 

Thank you for your kind note!

Author response:

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

Public reviews:

Reviewer #1:

This work by Leclercq and colleagues performed metabolomics on biospecimens collected from 96 patients diagnosed with several types of alcohol use disorders (AUD). The authors discovered strong alterations in circulating glycerophospholipids, bile acids, and some gut microbe-derived metabolites in AUD patients compared to controls. An exciting part of this work is that metabolomics was also performed in frontal cortex of post-mortem brains and cerebrospinal fluid of heavy alcohol users, and some of the same metabolites were seen to be altered in the central nervous system. This is an important study that will form the basis for hypothesis generation around diet-microbe-host interactions in alcohol use disorder. The work is done in a highly rigorous manner, and the rigorously collected human samples are a clear strength of this work. Overall, many new insights may be gained by this work, and it is poised to have a high impact on the field.

Strengths:

(1) The rigorously collected patient-derived samples.

(2) There is high rigor in the metabolomics investigation.

(3) Statistical analyses are well-described and strong.

(4) An evident strength is the careful control of taking blood samples at the same time of the day to avoid alterations in meal- and circadian-related fluctuations in metabolites.

Weaknesses:

(1) Some validation in animal models of ethanol exposure compared to pair-fed controls would help strengthen causal relationships between metabolites and alterations in the CNS.

(2) The classification of "heavy alcohol users" based on autopsy reports may not be that accurate.

(3) The fact that most people with alcohol use disorder choose to drink over eating food, there needs to be some more discussion around how dietary intake (secondary to heavy drinking) most likely has a significant impact on the metabolome.<br />

We thank this reviewer for his/her encouraging comments and for highlighting the fact that this study is important in the field to generate hypotheses around diet-microbe-host interactions in alcohol use disorder.

Concerning weakness #1: Regarding the validation in animal models of ethanol exposure, we were very careful in our discussion to avoid pretending that the study allowed to test causality of the factors. This was certainly not the objective of the present study. The testing of causality would indeed probably necessitate animal models but these models could only test the effects of one single metabolite at a time and could not at the same time capture the complexity of the changes occurring in AUD patients. The testing of metabolites would be a totally different topic. Hence, we do not feel comfortable in conducting rodent experiments for several reasons. First, AUD is a very complex pathology with physiological and psychological/psychiatric alterations that are obviously difficult to reproduce in animal models. Secondly, as mentioned by the reviewer, AUD pathology spontaneously leads to nutritional deficits, including significant reductions in carbohydrates, lipids, proteins and fiber intakes. We have recently published a paper in which we carefully conducted detailed dietary anamneses and described the changes in food habits in AUD patients (Amadieu et al., 2021). As explained below, some blood metabolites that are significantly correlated with depression, anxiety and craving belong to the xanthine family and are namely theobromine, theophylline, and paraxanthine, which derived from metabolism of coffee, tea or chocolate (which are not part of the normal diet of mice or rats).Therefore, conducting an experiment in animal model of ethanol exposure compared to pair-fed controls will omit the important impact of nutrition in blood metabolomics and consequently won’t mimic the human AUD pathology. In addition, if we take into consideration the European Directive 2010/63/EU (on the protection of animals used for scientific purposes) which aims at Reducing (Refining, Replacing) the number of animals used in experiment, it is extremely difficult to justify, at the ethical point of view, the need to reproduce human results in an animal model that won’t be able to mimic the nutritional, physiological and psychological alterations of alcohol use disorder.

Concerning weakness #2: The classification of subjects to the group who have a history of heavy alcohol use was not solely on autopsy record, but was also based on medical history i.e. diagnosis of alcohol-related diseases: ICD-10 codes F10.X, G31.2, G62.1, G72.1, I42.6, K70.0-K70.4, K70.9, and K86.0, or signs of heavy alcohol use in the clinical or laboratory findings, e.g., increased levels of gamma-glutamyl transferase, mean corpuscular volume, carbohydrate-deficient transferrin, as stated in the methods section of the manuscript. In Finland, the medical records from the whole life of the subjects are available. We consider that getting diagnosis of alcohol-related disease is clear sign of history of heavy alcohol use.

Concerning weakness#3:  As explained above, we do agree with the reviewer that AUD is not only “drinking alcohol” but is also associated with reduction in food intake that obviously influenced the metabolomics data presented in this current study.  We have therefore added some data, which have not been published before, in the results section that refer to key nutrients modified by alcohol intake and we refer to those data and their link with metabolomics in the discussion section:

Results section page 8, Line 153-155. This sentence has been added:

“The changes in metabolites belonging to the xanthine family during alcohol withdrawal could be explained by the changes in dietary intake of coffee, tea and chocolate (see Fig S5).”

Discussion section: Page 11, Line 235-240.

“Interestingly, the caffeine metabolites belonging to the xanthine family such as paraxanthine, theophylline and theobromine that were decreased at baseline in AUD patients compared to controls, increased significantly during alcohol withdrawal to reach the levels of healthy controls. Changes in dietary intake of coffee, tea and chocolate during alcohol withdrawal could explain these results”.

In the conclusion, Page 16, Line 354-356, we clearly stated that: “LC-MS metabolomics plasma analysis allowed for the identification of metabolites that were clearly linked to alcohol consumption, and reflected changes in metabolism, alterations of nutritional status, and gut microbial dysbiosis associated with alcohol intake”

Reference:

Amadieu C, Leclercq S, Coste V, Thijssen V, Neyrinck AM, Bindels LB, Cani PD, Piessevaux H, Stärkel P, Timary P de, Delzenne NM. 2021. Dietary fiber deficiency as a component of malnutrition associated with psychological alterations in alcohol use disorder. Clinical Nutrition 40:2673–2682. doi:10.1016/j.clnu.2021.03.029

Leclercq S, Cani PD, Neyrinck AM, Stärkel P, Jamar F, Mikolajczak M, Delzenne NM, de Timary P. 2012. Role of intestinal permeability and inflammation in the biological and behavioral control of alcohol-dependent subjects. Brain Behav Immun 26:911–918. doi:10.1016/j.bbi.2012.04.001

Leclercq S, De Saeger C, Delzenne N, de Timary P, Stärkel P. 2014a. Role of inflammatory pathways, blood mononuclear cells, and gut-derived bacterial products in alcohol dependence. Biol Psychiatry 76:725–733. doi:10.1016/j.biopsych.2014.02.003

Leclercq S, Matamoros S, Cani PD, Neyrinck AM, Jamar F, Stärkel P, Windey K, Tremaroli V, Bäckhed F, Verbeke K, de Timary P, Delzenne NM. 2014b. Intestinal permeability, gut-bacterial dysbiosis, and behavioral markers of alcohol-dependence severity. Proc Natl Acad Sci U S A 111:E4485–E4493. doi:10.1073/pnas.1415174111

Voutilainen T, Kärkkäinen O. 2019. Changes in the Human Metabolome Associated With Alcohol Use: A Review. Alcohol and Alcoholism 54:225–234. doi:10.1093/alcalc/agz030

Public Reviewer #2:

The authors carried out the current studies with the justification that the biochemical mechanisms that lead to alcohol addiction are incompletely understood. The topic and question addressed here are impactful and indeed deserve further research. To this end, a metabolomics approach toward investigating the metabolic effects of alcohol use disorder and the effect of alcohol withdrawal in AUD subjects is valuable. However, it is primarily descriptive in nature, and these data alone do not meet the stated goal of investigating biochemical mechanisms of alcohol addiction. The current work's most significant limitation is the cross-sectional study design, though inadequate description and citation of the underlying methodological approaches also hampers interest. Most of the data are cross-sectional in the study design, i.e., alcohol use disorder vs controls. However, it is well established that there is a high degree of interpersonal variation with metabolism, and further, there is somewhat high intra-personal variation in metabolism over time. This means that the relatively small cohort of subjects is unlikely to reflect the broader condition of interest (AUD/withdrawal). The authors report a comparison of a later time-point after alcohol withdrawal (T2) vs. the AUD condition. However, without replicative time points from the control subjects it is difficult to assess how much of these changes are due to withdrawal vs the intra-personal variation described above.

We agree with the reviewer. Our goal was not to investigate the biochemical mechanisms of AUD but rather to investigate how metabolomics could contribute to the psychological alterations of AUD. The goals of the study are defined at the end of the introduction (Page 4 – Lines 80-91), as follows:

“The aims of this study are multiple. First, we investigated the impact of severe AUD on the blood metabolome by non-targeted LC-MS metabolomics analysis. Second, we investigated the impact of a short-term alcohol abstinence on the blood metabolome followed by assessing the correlations between the blood metabolome and psychological symptoms developed in AUD patients. Last, we hypothesized that metabolites significantly correlated with depression, anxiety or alcohol craving could potentially have neuroactive properties, and therefore the presence of those neuroactive metabolites was confirmed in the central nervous system using post-mortem analysis of frontal cortex and cerebrospinal fluid of persons with a history of heavy alcohol use. Our data bring new insights on xenobiotics- or microbial-derived neuroactive metabolites, which can represent an interesting strategy to prevent or treat psychiatric disorders such as AUD”.

Due to the fact that the method section describing the study design is located at the end of the manuscript, we have decided to clarify the methodological approach in the first paragraph of the result section in order to show that in fact, we have performed a longitudinal study (which includes the same group of AUD, tested at two time points – at the beginning and at the end of alcohol withdrawal). This is stated as follows:

Results section, Page 6, Line 97-99: “All patients were hospitalized for a 3-week detoxification program, and tested at two timepoints: T1 which represents the first day of alcohol withdrawal, and T2 which represents the last day of the detoxification program”.

We propose to add a figure with a schematic representation of the protocol. We let the editor deciding whether this figure can be added (as supplemental material).

Author response image 1.

Schematic representation of the protocol

We agree with the reviewer that the correlational analysis (between blood metabolites and psychological symptoms) is conducted at one time point (T1) only, which has probably led to the confusion between cross-sectional and longitudinal study. In fact we had a strong motivation to provide correlations at T1, instead of T2. T1, which is at the admission time, is really the moment where we can take into account variability of the psychological scores. Indeed, after 3 weeks of abstinence (T2), the levels of depression, anxiety and alcohol craving decreased significantly ( as shown in other studies from our group (Leclercq et al., 2014b, 2014a, 2012)) and remained pretty low in AUD patients, with a much lower inter-individual variability which makes the correlations less consistent.

We agree with the reviewer that there is a high intra and inter-personal variability in the metabolomics data, that could be due to the differences in previous meals intakes within and between subjects. While AUD subjects have been tested twice (at the beginning and at the end of a 3-week detoxification program), the control subjects have only been tested once. Consequently, we did not take into account the intra-personal variability in the control group. The metabolomics changes observed in AUD patients between T1 and T2 are therefore due to alcohol withdrawal but also to intra-personal variability. This is a limitation of the study that we have now added in the discussion section, Page 16, Lines 354-357  as follows:

“The selection of the control group is always challenging in alcohol research. Here, the healthy subjects were matched for sex, age and BMI but not for smoking status or nutritional intake. Alcohol addiction is a major cause of malnutrition in developed countries and tobacco smoking is more prevalent in alcohol users compared to healthy subjects. These two main confounding factors, although being an integral part of the alcoholic pathology, are known to influence the blood metabolome. Furthermore, another limitation is that the control group was tested only once, while the AUD patients were tested twice (T1 and T2). This means that we do not take into consideration the intra-personal variability of the metabolomics data when interpreting the results of alcohol withdrawal effects”.

The limitation concerning the small sample size is already mentioned in the discussion section, as follows:

“Large studies are usually required in metabolomics to observe small and medium size changes. Here, we included only 96 AUD patients, but they were all well characterized and received standardized therapies (for instance, vitB supplementation) during alcohol withdrawal”.

Overall, there is not enough experimental context to interpret these findings into a biological understanding. For example, while several metabolites are linked with AUD and associated with microbiome or host metabolism based on existing literature, it's unclear from the current study what function these changes have concerning AUD, if any. The authors also argue that alcohol withdrawal shifts the AUD plasma metabolic fingerprint towards healthy controls (line 153). However, this is hard to assess based on the plots provided since the change in the direction of the orange data subset is considers AUD T2 vs T1. In contrast, AUD T2 vs Control would represent the claimed shift. To support these claims, the authors would better support their argument by showing this comparison as well as showing all experimental groups (including control subjects) in their multi-dimensional model (e.g., PCA).

We thank the reviewer for these comments. It is true in this type of discovery-based approach the causality cannot be interpreted nor do we claim so. The aim was to characterize the metabolic alterations in this population, response to withdrawal period and suggest potential candidate metabolites linked to psychological symptoms. Rigorous pre-clinical assays and validation trials in humans are required to prove the causality, if any, of the discussed metabolites.

The original claim on line 153 was poorly constructed and the Figure 2c is meant to visualize the influence of withdrawal on selected metabolites and also show the effect of chronic alcohol intake on the selected metabolites at baseline. The description of the Figure 2c has been modified in result section from line 156 onwards: “Overall, Fig. 2c demonstrates that a number of identified metabolites altered in sAUD patients relative to control are affected by alcohol withdrawal. Apart from 4-pyridoxic acid, cotinine, and heme metabolites bilirubin and biliverdin, the shifts observed in the selected metabolites are generally in the opposite direction as compared to the baseline.”

The authors attempt to extend the significance of their findings by assessing post-mortem brain tissues from AUD subjects; however, the finding that many of the metabolites changed in T2/T1 are also present in AUD brain tissues is interesting; however, not strongly supporting of the authors' claims that these metabolites are markers of AUD (line 173). Concerning the plasma cohort itself, it is unclear how the authors assessed for compliance with alcohol withdrawal or whether the subjects' blood-alcohol levels were independently verified.

We did not claim that the metabolites significantly correlated with the psychological symptoms - and present in central nervous system (frontal cortex or CSF) -  are “markers of AUD”. Line 173 did not refer to this idea, and the terms “markers of AUD” do not appear in the whole manuscript.

Regarding the compliance with alcohol cessation, we did not assess the ethanol blood level. The patients are hospitalized for a 3-week detoxification program, they are not allowed to drink alcohol and are under strict control of the nurses and medical staff of the unit. Consuming alcoholic beverage within the hospitalization unit is a reason for exclusion. However, we carefully monitored the liver function during alcohol withdrawal. For the reviewers’ information, we have added here below, the evolution of liver enzymes (ALT, AST, gGT) during the 3-week detoxification program as indirect markers of alcohol abstinence.

Author response image 2.

Data are described as median ± SEM. AST, Aspartate transaminase; ALT, Alanine transaminase; gGT: gamma glutamyltranspeptidase. ** p<0.01 vs T1, *** p<0.001 vs T1

 

The second area of concern is the need for more description of the analytical methodology, the lack of metabolite identification validation evidence, and related statistical questions. The authors cite reference #59 regarding the general methodology. However, this reference from their group is a tutorial/review/protocol-focused resource paper, and it is needs to be clarified how specific critical steps were actually applied to the current plasma study samples given the range of descriptions provided in the citations. The authors report a variety of interesting metabolites, including their primary fragment intensities, which are appreciated (Supplementary Table 3), but no MS2 matching scores are provided for level 2 or 3 hits. Further, level 1 hits under their definition are validated by an in-house standard, but no supporting data are provided besides this categorization. Finally, a common risk in such descriptive studies is finding spurious associations, especially considering many factors described in the current work. These include AUD, depression, anxiety, craving, withdrawal, etc. The authors describe the use of BH correction for multiple-hypothesis testing. However, this approach only accounts for the many possible metabolite association tests within each comparison (such as metabolites vs depression). It does not account for the multi-variate comparisons to the many behavior/clinical factors described above. The authors should employ one of several common strategies, such as linear mixed effects models, for these types of multi-variate assessments.

The methodological details related to the sample processing, data acquisition, data pre-processing and metabolite identification have been provided in the supplementary materials and described below. Supplementary table 3 has been amended with characteristic MS2 fragments for both positive and negative ionization modes if data was available. Additionally, all annotations against the in-house library additions have been rechecked, identification levels corrected and EICs for all level 1 identifications are provided in the supplementary material.

As described in the statistical analysis methods, BH correction was employed in the group-wise comparisons to shortlist the altered features for identification. Manual curating was then applied for the significant features and annotated metabolites subjected to correlation analysis. In this discovery-based approach the aim was to discover potential candidates linked with psychological symptoms for subsequent work to evaluate causality. Hence, the application of multi-variate analysis assessing biomarker candidates is not in the scope of this study.

“LC-MS analysis. Plasma sample preparation and LC-MS measurement followed the parameters previously detailed in Klåvus et al (57).  Samples were randomized and thawed on ice before processing. 100 µl of plasma was added to 400 µl of LC-MS grade acetonitrile, mixed by pipetting four time, followed by centrifugation in 700 g for 5 minutes at 4 °C. A quality control sample was prepared by pooling 10 µl of each sample together. Extraction blanks having only cold acetonitrile and devoid of sample were prepared following the same procedure as sample extracts. LC-MS grade acetonitrile, methanol, water, formic acid and ammonium formate (Riedel-de Haën™, Honeywell, Seelze, Germany) were used to prepare mobile phase eluents in reverse phase (Zorbax Eclipse XDBC18, 2.1 × 100 mm, 1.8 μm, Agilent Technologies, Palo Alto, CA, USA) and hydrophilic interaction (Acquity UPLC® BEH Amide 1.7 μm, 2.1 × 100 mm, Waters Corporation, Milford, MA, USA) liquid chromatography separation. In reverse phase separation, the samples were analyzed by Vanquish Flex UHPLC system (Thermo Scientific, Bremen, Germany) coupled to high-resolution mass spectrometry (Q Exactive Focus, Thermo Scientific, Bremen, Germany) in both positive and negative polarity mass range from 120 to 1200, target AGC 1e6 and resolution 70,000 in full scan mode. Data dependent MS/MS data was acquired for both modes with target AGC 8e3 and resolution 17,500, precursor isolation window was 1.5 amu, normalized collision energies were set at 20, 30 and 40 eV and dynamic exclusion at 10.0 seconds. In hydrophobic interaction separation, the samples were analyzed by a 1290 LC system coupled to a 6540 UHD accurate mass Q-ToF spectrometer (Agilent Technologies, Waldbronn, Karlsruhe, Germany) using electrospray ionization (ESI, Jet Stream) in both positive and negative polarity with mass range from 50 to 1600 and scan rate of 1.67 Hz in full scan mode. Source settings were as in the protocol. Data dependent MS/MS data was acquired separately using 10, 20 and 40 eV collision energy in subsequent runs. Scan rate was set at 3.31 Hz, precursor isolation width of 1.3 amu and target counts/spectrum of 20,000, maximum of 4 precursor pre-cycle, precursor exclusion after 2 spectra and release after 15.0 seconds. Detectors were calibrated prior sequence and continuous mass axis calibration was performed throughout runs by monitoring reference ions from infusion solution for operating at high accuracy of < 2 ppm. Quality control samples were injected in the beginning of the analysis to equilibrate the system and after every 12 samples for quality assurance and drift correction in all modes. All data were acquired in centroid mode by either MassHunter Acquisition B.05.01 (Agilent Technologies) or in profile mode by Xcalibur 4.1 (Thermo Fisher Scientific) softwares.

Metabolomics analysis of TSDS frontal cortex and CSF samples using the same 1290 LC system coupled with a 6540 UHD accurate mass Q-ToF spectrometer has been previously accomplished by Karkkainen et al (10).

Peak picking and data processing. Raw instrumental data (*raw and *.d files) were converted to ABF format using Reifycs Abf Converter (https://www.reifycs.com/AbfConverter). MS-DIAL (Version 4.70) was employed for automated peak picking and alignment with the parameters according to Klåvus et al., 2020 (57) separately for each analytical mode. For the 6540 Q-ToF mass data minimum peak height was set at 8,000 and for the Q Exactive Focus mass data minimum peak height was set at 850,000. Commonly, m/z values up to 1600 and all retention times were considered, for aligning the peaks across samples retention time tolerance was 0.2 min and MS1 tolerance 0.015 Da and the “gap filling by compulsion” was selected. Alignment results across all modes and sample types as peak areas were exported into Microsoft Excel sheets to be used for further data pre-processing.

Pre-processing including drift correction and quality assessment was done using the notame package v.0.2.1 R software version 4.0.3 separately for each mode. Features present in less than 80% of the samples within all groups and with detection rate in less than 70% of the QC samples were flagged. All features were subjected to drift correction where the features were log-transformed and a regularized cubic spline regression line was fitted for each feature against the quality control samples. After drift correction, QC samples were removed and missing values in the non-flagged features were imputed using random forest imputation. Finally, the preprocessed data from each analytical mode was merged into a single data matrix.

Molecular feature characteristics (exact mass, retention time and MS/MS spectra) were compared against in-house standard library, publicly available databases such as METLIN, HMDB and LIPIDMAPS and published literature. Annotation of metabolites and the level of identification was based on the recommendations given by the Chemical Analysis Working Group (CAWG) Metabolomics Standards Initiative (MSI) (59): 1 = identified based on a reference standard, 2 = putatively annotated based on physicochemical properties or similarity with public spectral libraries, 3 = putatively annotated to a chemical class and 4 = unknown.”

Reference 59: Sumner LW, Amberg A, Barrett D, Beale MH, Beger R, Daykin CA, et al. Proposed minimum reporting standards for chemical analysis. Metabolomics. 2007;3:211–221.

Recommendations for the authors:

Reviewer #1:

(1) There should be more discussion comparing and contrasting the differences between the 2 cohorts (ALCOHOLBIS versus GUT2BRAIN), instead of stressing the similarities.

As indicated in the results section, we have verified that the ALCOHOLBIS cohort and GUT2BRAIN cohort are similar in term of age, gender, smoking habits, drinking habits and severity of psychological symptoms. Those similar features are important to allow the combination of the metabolomics data from the two cohorts, which subsequently allows to have a bigger sample size (n = 96) and more statistical power.

(2) The identification of 97 heavy alcohol users based on hospital codes at autopsy may not be the most rigorous way to define those with AUD. More information is needed on how these 97 were classified as heavy alcohol users.

The classification of subjects to the group who have a history of heavy alcohol use was not based solely on the autopsy records. The classification was also based on medical history, which in Finland is available from the whole life of the subjects, and including diagnoses and laboratory finding. The subjects needed to have a diagnosis of alcohol-related disease, as stated in the methods section of the manuscript. However, since some of the used diagnoses are related to organ damage related to heavy alcohol use, we do not claim that these subjects would all have alcohol dependence. But history of heavy use of alcohol is needed to get organ damage associated with alcohol use. Therefore, we consider that diagnosis of alcohol-related disease is a clear sign of a history of heavy alcohol use.

(3) The fact that the control group mainly died of cardiovascular disease confounds the interpretations around alcohol impact metabolite levels. How much of the metabolomics differences are related to hyperlipidemia or other CVD risk factors in the controls?

There are no healthy controls in post-mortem studies, since all subjects need to die from something to be included to the cohort. The challenge in studying AUD is that they die relatively young. The only other group of individuals who die outside of hospital at the relatively same age as subjects with AUD are those with CVD. Post-mortem autopsies are done in Finland to all who die outside of hospital, and these are the main source of samples for post-mortem sample cohorts. Therefore, there is no other control group to compare AUD subject to in these types of studies.

As for the altered metabolites in the post-mortem sample, the phospholipids observed could be associated with CVD. However, alterations in phospholipids are also commonly associated with alcohol use and AUD (for a review see (Voutilainen and Kärkkäinen, 2019)) and this effect is also seen in the results from the clinical cohorts in this study (Figure 1). Therefore, it cannot be said that these phospholipids finding would be due to selection of the control group.

(4) When examining metabolomics alterations, it is extremely important to understand what people are eating (i.e., providing a substrate). A major confounding issue here is that heavy alcohol users typically choose drinking over eating food. How much of the observed alterations in the plasma metabolome is due to the decreased food intake? Some validation in animal models of ethanol exposure compared to pair-fed controls would help strengthen causal relationships between metabolites and alterations in the circulation and CNS.

Regarding the validation in animal models of ethanol exposure, we were very careful in our discussion to avoid pretending that the study allowed to test causality of the factors. This was certainly not the objective of the present study. The testing of causality would indeed probably necessitate animal models but these models could only test the effects of one single metabolite at a time and could not at the same time capture the complexity of the changes occurring in AUD patients. The testing of metabolites would be a totally different topic. Hence, we do not feel comfortable in conducting rodent experiments for several reasons. First, AUD is a very complex pathology with physiological and psychological/psychiatric alterations that are obviously difficult to reproduce in animal models. Secondly, as mentioned by the reviewer, AUD pathology spontaneously leads to nutritional deficits, including significant reductions in carbohydrates, lipids, proteins and fiber intakes. We have recently published a paper in which we carefully conducted detailed dietary anamneses and described the changes in food habits in AUD patients (Amadieu et al., 2021). As explained below, some blood metabolites that are significantly correlated with depression, anxiety and craving belong to the xanthine family and are namely theobromine, theophylline, and paraxanthine, which derived from metabolism of coffee, tea or chocolate (which are not part of the normal diet of mice or rats).Therefore, conducting an experiment in animal model of ethanol exposure compared to pair-fed controls will omit the important impact of nutrition in blood metabolomics and consequently won’t mimic the human AUD pathology. In addition, if we take into consideration the European Directive 2010/63/EU (on the protection of animals used for scientific purposes) which aims at Reducing (Refining, Replacing) the number of animals used in experiment, it is extremely difficult to justify, at the ethical point of view, the need to reproduce human results in an animal model that won’t be able to mimic the nutritional, physiological and psychological alterations of alcohol use disorder.

As explained above, we do agree with the reviewer that AUD is not only “drinking alcohol” but is also associated with reduction in food intake that obviously influenced the metabolomics data presented in this current study.  We have therefore added some data, which have not been published in the previous version of the manuscript, in the results section that refer to key nutrients modified by alcohol intake and we refer to those data and their link with metabolomics in the discussion section:

Results section page 8, Line 153-155. This sentence has been added:

“The changes in metabolites belonging to the xanthine family during alcohol withdrawal could be explained by the changes in dietary intake of coffee, tea and chocolate (see Fig S5).”

Discussion section: Page 11, Line 234-238.

“Interestingly, the caffeine metabolites belonging to the xanthine family such as paraxanthine, theophylline and theobromine that were decreased at baseline in AUD patients compared to controls, increased significantly during alcohol withdrawal to reach the levels of healthy controls. Changes in dietary intake of coffee, tea and chocolate during alcohol withdrawal could explain these results”.

In the conclusion, Page 16, Line 360-32, we clearly stated that: “LC-MS metabolomics plasma analysis allowed for the identification of metabolites that were clearly linked to alcohol consumption, and reflected changes in metabolism, alterations of nutritional status, and gut microbial dysbiosis associated with alcohol intake”

Reference:

Amadieu C, Leclercq S, Coste V, Thijssen V, Neyrinck AM, Bindels LB, Cani PD, Piessevaux H, Stärkel P, Timary P de, Delzenne NM. 2021. Dietary fiber deficiency as a component of malnutrition associated with psychological alterations in alcohol use disorder. Clinical Nutrition 40:2673–2682. doi:10.1016/j.clnu.2021.03.029

Leclercq S, Cani PD, Neyrinck AM, Stärkel P, Jamar F, Mikolajczak M, Delzenne NM, de Timary P. 2012. Role of intestinal permeability and inflammation in the biological and behavioral control of alcohol-dependent subjects. Brain Behav Immun 26:911–918. doi:10.1016/j.bbi.2012.04.001

Leclercq S, De Saeger C, Delzenne N, de Timary P, Stärkel P. 2014a. Role of inflammatory pathways, blood mononuclear cells, and gut-derived bacterial products in alcohol dependence. Biol Psychiatry 76:725–733. doi:10.1016/j.biopsych.2014.02.003

Leclercq S, Matamoros S, Cani PD, Neyrinck AM, Jamar F, Stärkel P, Windey K, Tremaroli V, Bäckhed F, Verbeke K, de Timary P, Delzenne NM. 2014b. Intestinal permeability, gut-bacterial dysbiosis, and behavioral markers of alcohol-dependence severity. Proc Natl Acad Sci U S A 111:E4485–E4493. doi:10.1073/pnas.1415174111

Voutilainen T, Kärkkäinen O. 2019. Changes in the Human Metabolome Associated With Alcohol Use: A Review. Alcohol and Alcoholism 54:225–234. doi:10.1093/alcalc/agz030

Reviewer #2:

(1) More methodological information about the laboratory processing of samples, instrumentation, and data analysis needs to be provided. Reference 59 needs to be more specific and include important methodological details for this project. Please provide an actual methods section for the mass-spectrometry-based metabolomics.

The reviewer is correct that the methods should be described in detail but due to word limits, the description was moved to a supplementary file. Methodological details are provided in the answer to the final comment in the public reviews section and we kindly refer to that for the methodological details. Reference 57 (Klåvus et al) is a method paper and covers the whole untargeted metabolomics pipeline that is used in our work.

(2) The VIP figures, e.g., Figure 1b and Figure 2b are not very informative and would be better represented in a supplementary table

VIP scores for all annotated metabolites are provided in the supplementary table 3 along with peak data and other values derived from statistical tests. Furthermore, we have removed the VIP value in figures 1 and 2 and we have replaced them by an updated Volcano plot to represent also the VIP values in addition to the q and Cohen’s d values.

(3) The findings on odd-chain lyso-lipids are interesting, and while these have been reported biologically, odd-chain lipids are uncommon and should be validated with authentic standards as available (please provide an XIC of the level 1 peak and standard if possible, e.g., LPC 17:0) or at least a supplementary figure on manual inspection of the negative mode MS2 spectrum showing the putative fatty acid chain fragment. The current assignments are based on positive mode lipid class fragments and accurate mass.

We thank the reviewer for pointing this out and it is correct that the negative MS2 spectrum is essential for lipid identification. Although the current assignments show only positive fragments for many lipids, the fatty acid chain, if reported, has been confirmed from negative mode MS2 spectrum. The supplementary table 3 with peak information has been augmented with fragment information from both negative and positive ionizations if available. Also, reference and experimental MS2 spectra have been provided as separate supplemental file for level 1 identifications, including the odd-chain lyso-lipids LPC 15:0 and 17:0.

(4) Please provide some supplementary information (MS1/MS2 if available) on the untargeted features of interest (up and down-regulated) from Figure 1C, especially the 5 encircled features. If any manual annotation of these features was attempted, please include a brief description in the results/discussion.

All statistically significant features with MS2 data have been subjected to manual annotation and database searches using at least METLIN, HMDB and LipidMaps. Additionally, if the manual inspection failed to provide any identification, in silico fragmentation software MS-FINDER was used to calculate candidate molecular formula. The features were labeled as unknown if all efforts were unsuccessful. The peak characteristics of the key unknowns in Figure 1b have also been included in the supplemental table.

A note of the manual inspection has been included in the result section line 129: “The top-ranked metabolites in Fig. 1b remained unknown regardless of manual curation.”

Reviewer #3:

I think this is an interesting paper with a very solid methodology and an abundance of results. I am not an expert on metabolomics, and I have some very interesting hours here, trying (but sometimes failing) to grasp this paper's content. This paper also needs to be closely read by a reviewer who knows the metabolomics field and can give feedback on the meaning of the results. I have focused purely on the AUD clinical side as this is where I may contribute. My main concern is conceptualizing the aims and what authors want to investigate. As far as I understand, this is a study of the relationship between alcohol use and the metabolome, and in this respect, I think there are some issues.

Just take the abstract that talks about (in the first sentence) alcohol use disorder ("AUD") - a term that generally sometimes refers to harmful use of alcohol and alcohol addiction and sometimes to all F10-diagnosis (and thus an inaccurate term), then the following sentence talks about what leads to alcohol addiction (not dependence) - and this in a mechanistic direction and in the last part of the second sentence talks about metabolomics being able to decipher metabolic events related to AUD. So, even in the first two sentences, it is confusing - is this about correlates, mechanisms, prevention, or treatment? The inaccuracy of terms continues in sentence 4. We have "chronic alcohol abuse" (?) and "severe alcohol use disorder (AUD)" (abbreviated for the second time). Later, only "alcohol abuse" is used and the abstract ends with something about these findings being interesting in "the management of [...] AUD". All this illustrates that there is a large mixture of concepts - what aspect of alcohol use or abuse are you looking at? Moreover, of intention: is it to find correlates, explanations, or targets for interventions? Without clarity in this respect, one can get lost in what all these interesting measures mean - how we should interpret them. This comment is made only for the abstract. However, but it is equally valid and important for the introduction and discussion parts of the ms, where additional terms and formulations are introduced: "heavy alcohol use" (lines 86-7) and "prevent or treat psychiatric disorders such as AUD" (lines 90-1). This is then reflected in the discussion where the authors claim that what they have found is related to "chronic alcohol abuse" (line 188), "heavy alcohol drinkers" (line 191), and "AUD patients" (lines 199 and 202 and further on).  

We thank the reviewer for this useful comment and we apologize for the confusion. We agree that it is important to use the correct terms and definitions. All patients included in this study were diagnosed as severe AUD (for more information on the diagnosis, see answer to the comments related to DSM-IV and DSM5). This manuscript is consequently related to severe AUD and other terms like “alcohol abuse, “alcohol addiction” are therefore not appropriate. In the revised version of the manuscript, we have used severe AUD or the abbreviation sAUD. The figure and legends have been changed accordingly.

In the first paragraph of the results section, ALCOHOLBIS and GUT2BRAIN are compared. It says they are similar on many measures, including craving, but different on some measures, again including craving. It is difficult to grasp this even if the authors try to explain (lines 101-2). This sentence also introduces some discussion in the results section by saying something normative about their finding and relating this to other research (references 12, 13, and 14).

We would like to apologize for the confusion related to first paragraph of the results section. We have indeed indicated that, while the ALCOHOLBIS cohort and the GUT2BRAIN cohort are highly similar in term of biological and psychological features, a significant difference does exist in the compulsive component of the craving score. Indeed, the mean score of compulsion is 11 ± 3 in the ALCOHOLBIS cohort and 14  ± 3 in the GUT2BRAIN cohort. In healthy controls, the mean score of compulsion is 1.5 ± 1.5. Despite the statistically significant difference in craving between both cohorts, we do not think that this difference is relevant in our context since both scores (11 and 14) are considered high compared to the control group. In order to simplify the message, we have revised the first paragraph as follows:

“Both groups of patients were similar in terms of age, gender, smoking and drinking habits and presented with high scores of depression, anxiety and alcohol craving at T1 (Table 1). These biological and psychological similarities allow us to combine both cohorts (and consequently increase sample size) and compare them to a group of heathy controls for metabolomics analysis”.

In line 104 the abbreviation PCA is introduced but needs to be explained. Such objections could be made for many of the abbreviations used (sPLS-DA VIP, LPC, CSF, CNS, LPE, etc.), but of course, they may be made more difficult by the unusual way of stacking the different sections.

We thank the reviewer for pointing these out. Most abbreviations are written out in the figure legends or method section but indeed the organization of the different sections makes it less evident. The abbreviations pointed out have been opened in the results section when they are first used.

Furthermore, they say that the severity of AUD was "evaluated by a psychiatrist using the Diagnostic and Statistical Manual of Mental Disorders (DSM) criteria, fourth edition (DSM-IV) (ALCOHOLBIS cohort) or fifth edition (DSM-5)" (GUT2BRAIN cohort): This makes sense for DSM-5 but needs to be explained more for DSM-IV. They also need to say what levels were included.

We thank the reviewer for this very appropriate remark that deserves some explanations.

While the patients of the GUT2BRAIN cohort were enrolled in 2018-2019 where the DSM5 was applicable, the patients from the ALCOHOLBIS cohort were recruited many years before. The protocol related to the ALCOHOLBIS cohort was written before 2013, and approved by ethical committee, where the DSM-IV was the last version of the DSM used at that moment. 

We therefore totally agree with the reviewer that our sentence “the severity of AUD was "evaluated by a psychiatrist using the Diagnostic and Statistical Manual of Mental Disorders (DSM) criteria, fourth edition (DSM-IV) (ALCOHOLBIS cohort) or fifth edition (DSM-5)" (GUT2BRAIN cohort)” is not correct. Indeed, DSM-IV (before 2013) described two distinct disorders, alcohol abuse and alcohol dependence, while the DSM-5 integrates the two DSM-IV disorders into a single disorder called alcohol use disorder with mild (2 or 3 symptoms), moderate (4 or 5 symptoms) and severe (6 or more symptoms) sub-classifications.

In this present study, we have enrolled patients that received the diagnosis of alcohol dependence (DSM-IV criteria) or severe alcohol use disorder (DSM5 criteria).

We have changed the paragraph related to this issue into this new one:

“The severity of AUD was evaluated by a psychiatrist using the Diagnostic and Statistical Manual of Mental Disorders (DSM) criteria, fourth edition (DSM-IV) (Alcoholbis cohort) or fifth edition (DSM-5) (GUT2BRAIN cohort). Patients evaluated with the DSM-IV received the diagnosis of “alcohol dependence”, while the patients evaluated with the DSM-5 received the diagnosis of “severe alcohol use disorder” (6 or more criteria). To simplify, we used the term “sAUD” (for severe alcohol use disorder) that includes both diagnosis (sAUD and alcohol dependence)”.

I am unsure about the shared first co-authorship and the shared last co-authorship request, but I leave this up to the editors and the journal policies. Also, the order of the different parts may be correct (the M+M placed last) but is unusual for many journals. This is also up to the journal to decide.

As mentioned in the guidelines to authors, the method section should be included at the end of the manuscript.

eLife assessment

This study provides valuable insights and allows for hypothesis generation around diet-microbe-host interactions in alcohol use disorder. The strength of the evidence is convincing: the work is done in a rigorous manner in a well-described cohort of patients with AUD before and after withdrawal. There are several weaknesses, including validating the metabolites identified by metabolomics, the cross-sectional study design, the lack of a healthy control group, and the descriptive nature of such clinical cohort studies. Nevertheless, the study provides a wealth of new data that may be the basis for future studies that test causality and elucidate the role of single metabolites in the psychiatric sequela of AUD.

Reviewer #1 (Public review):

Summary:

This work by Leclercq and colleagues performed metabolomics on biospecimens collected from 96 patients diagnosed with severe alcohol use disorder (AUD). The authors discovery strong alterations in circulating glycerophospholipids, bile acids, and some gut microbe-derived metabolites in AUD patients compared to controls. An exciting part of this work is that metabolomics was also done in post-mortem samples of the frontal cortex and cerebrospinal fluid of heavy alcohol users, and some of the same metabolites were seen to be altered in the central nervous system. This important study will form the basis for hypothesis generation around diet-microbe-host interactions in alcohol use disorder. The work is done in a highly rigorous manner, and the rigorously collected human samples is an evident strength of this work. Overall, this work will provide many new insights, and it is poised to have a high impact on the field.

Strengths:

(1) The rigorously collected patient-derived samples<br /> (2) There is high rigorous in the metabolomics investigation<br /> (3) Statistical analyses are well-described and strong.<br /> (4) The careful control of taking blood samples at the same time to avoid alterations in meal- and circadian-related fluctuations in metabolites is a clear strength.

Weaknesses:

None remaining

Reviewer #2 (Public review):

The authors carried out the current studies with the justification that the biochemical mechanisms that lead to alcohol addiction are incompletely understood. The topic and question addressed here are impactful and indeed deserve further research. To this end, a metabolomics approach toward investigating the metabolic effects of alcohol use disorder and the effect of alcohol withdrawal in AUD subjects is valuable. However, this work is primarily descriptive in nature, and these data alone do not meet the stated goal of investigating biochemical mechanisms of alcohol addiction. The current work's most significant limitation is the cross-sectional study design, though inadequate description and citation of the underlying methodological approaches also hampers interest.

Most of the data are cross-sectional in study design, i.e., alcohol use disorder vs controls. However, it is well established that there is a high degree of interpersonal variation with metabolism, and further, there is somewhat high intra-personal variation in metabolism over time. This means that the relatively small cohort of subjects is unlikely to just reflect the broader condition of interest (AUD/withdrawal). The authors report a comparison of a later time-point after alcohol withdrawal (T2) vs the AUD condition. Nonetheless, without replicate time points from the control subjects it is difficult to assess how much of these changes are due to withdrawal vs the intra-personal variation described above. Overall, insufficient experimental context exists to interpret these findings into a biological understanding. For example, while several metabolites are linked with AUD and associated with microbiome or host metabolism based on existing literature, it is unclear from the current study what function these changes have concerning AUD, if any. The authors also argue that alcohol withdrawal shifts the AUD plasma metabolic fingerprint towards healthy controls (line 153). However, this is hard to assess based on the provided plots since the direction of change of the orange data subset considers AUD T2 vs. T1. In contrast, AUD T2 vs. Control would represent the claimed shift. To substantiate these claims, the authors would better support their argument by showing this comparison in all experimental groups (including control subjects) in their multi-dimensional model (e.g., PCA). The authors attempt to extend the significance of their findings by assessing post-mortem brain tissues from AUD subjects; however, the finding that many of the metabolites changed in T2/T1 are also found in AUD brain tissues is interesting but does not strongly support the authors' claims that these metabolites are markers of AUD (line 173). Concerning the plasma cohort itself, it is unclear how the authors assessed for compliance with alcohol withdrawal or whether the subjects' blood-alcohol levels were independently verified.

The second area of concern is the lack of description of the analytical methodology, the lack of metabolite identification validation evidence, and related statistical questions. The authors cite reference #59 regarding the general methodology. However, this reference from their group is a tutorial/review/protocol focused resource paper and it needs to be clarified how specific critical steps were actually applied to the current plasma study samples, given the range of descriptions provided in the citations. The authors report a variety of interesting metabolites, including their primary fragment intensities, which is appreciated (Supp Table 3), but no MS2 matching scores are provided for level 2 or 3 hits. Further, level 1 hits under their definition are validated by an in-house standard, but not supporting data are provided other than this categorization. Finally, a common risk in such descriptive studies is finding spurious associations, especially considering the many factors as described in the current work. These include AUD, depression, anxiety, craving, withdrawal, etc. The authors describe the use of BH correction for multiple-hypothesis testing. Still, this approach only accounts for the many possible metabolite association tests within each comparison (such as metabolites vs. depression) and does not account for the multi-variate comparisons to the many behavior/clinical factors described above. The authors should employ one of several common strategies, such as linear mixed effects models for these types of multi-variate assessments.

Revised Review after Resubmission:

I thank the authors for their responses and revisions to the figures and data and their clarifications of their results and study goals. However, based on this updated information, it is now more apparent that the paper falls into the common trap of descriptive studies where insufficient experimental design was considered to test the association in question robustly. Further, follow-up initiatives are lacking to test the findings by other experimental means. Despite the authors' responses, the paper still fails to convert or interpret the metabolomics findings into any new biological understanding or meaningfully testable hypotheses, and the results remain descriptive in nature with significant caveats.

The authors clarify that their study's "goal was not to investigate the biochemical mechanisms of AUD but how metabolomics could contribute to the psychological alterations of AUD." However, the 2nd sentence of the abstract remains as follows: "The biochemical mechanisms that lead to this disorder are not yet fully understood, and in this respect, metabolomics represents a promising approach to decipher metabolic events related to AUD."This leads the reader to conclude that the purpose of the current study is to use metabolomics to address this gap, despite their later clarification. In the revised response, the authors walk back their claims of these goals, yet the manuscript text and data is largely unchanged in the revision. The serious caveats pointed out by several reviewers concerning the study as reported significantly reduces the utility of the described findings for the broader scientific community, and the authors largely downplay these limitations without addressing the underlying issues.

The authors also clarified in their response that the study's key purpose of the study is to assess "correlations between the blood metabolome and psychological symptoms developed in AUD patients." This goal is dubious as the vast majority of metabolites are not psychoactive, and it is implausible that the metabolome would affect mental state or vice versa. More biological frameworks and citations are needed for this paradigm. The soundness of the goal is further questioned by the study's simplistic design and the authors' admission that "In this discovery-based approach, the aim was to discover potential candidates linked with psychological symptoms for subsequent work to evaluate causality." Yet, the authors side-step the point about the risk of finding spurious associations and decline to control this risk using widely-accepted approaches such as multi-variate correction, instead continuing to use only BH correction for multiple hypothesis testing. The reviewers previously pointed out that BH correction only accounts for the many possible metabolite association tests within each comparison (such as metabolites vs depression). However, it does not account for the multi-variate comparisons to the many behavior/clinical factors. This issue is ignored in the response because the study's goal is hypothesis generating. Instead, the authors focused their responses on the issue of causality which was not the central point of the criticism.

Further, the authors employ mainly systemic plasma analyses unlikely to reflect brain biochemistry. The authors deny that the purpose of including the post-mortem brain tissue data was to demonstrate that "metabolites significantly correlated with the psychological symptoms - and present in the central nervous system (frontal cortex or CSF) - are "markers of AUD," yet if this is not the goal, the structure of the experiment, and the value of these data, is unclear. Another reviewer pointed out that it is difficult to control cross-sectional post-mortem tissue due to a lack of suitable controls, and the authors again side-step the question by citing the lack of suitable controls and the impossibility of "healthy controls" in post-mortem samples. This is true, but this lack of technical feasibility and the confounding factor of CVD/lipid metabolism does not justify the weak experimental design in this respect. Therefore, it remains unclear what can be understood from these data, given the limitations.

Finally, the authors acknowledge the limitation in their revision that they did not assess a second-time point in the control cohort of samples which could have been used to tease apart intra-personal variation from AUD-associated changes during alcohol-abstinence. Unfortunately, this is not a small caveat to simply acknowledge in the discussion section; it severely limits the interpretation and utility of the reported data more broadly, and the authors do not address this underlying problem.

Reviewer #3 (Public review):

Summary:

The authors have compared different groups of AUD patients at different levels and have examined metabolomics.

Strengths:

A well-written and comprehensive study.

eLife assessment

This important study describes changes in excitability in motor neurons of the peripheral autonomous nervous system during aging. The manuscript provides convincing evidence indicating that sympathetic neurons from aged mice show higher excitability compared to neurons from young mice which was linked to decreased activity of KCNQ2/3 potassium channels. This research has implications for understanding the age-related changes that occur in the peripheral nervous system.

Reviewer #1 (Public review):

Summary:

The authors study age-related changes in the excitability and firing properties of sympathetic neurons, which they ascribe to age-related changes in the expression of KCNQ (Kv7, "M-type") K+ currents in rodent sympathetic neurons, whose regulation by GPCRs has been most thoroughly studied for over 40 years.

Strengths:

The strengths include the rigor of the current-clamp and voltage-clamp experiments and the lovely, crisp presentation of the data, The separation of neurons into tonic, phasic and adapting classes is also interesting, and informative. The ability to successfully isolate and dissociate peripheral ganglia from such older animals is also quite rare and commendable! There is much useful detail here.

Weaknesses:

Whereas the description of the data are very nice, and useful, the manuscript does not provide much in the way of mechanistic insights. As such, the effect is more of an epi-phenomenon of unclear insight, and the authors cannot ascribe changes in signaling mechanisms, such as that of M1 mAChRs to the phenomena that is supported by data.

Comments on latest version:

I do not have any additional issues to be addressed by the authors.

Reviewer #2 (Public review):

Summary:

This research provides compelling and detailed evidence showing that aging influences intrinsic membrane properties of peripheral sympathetic motor neurons, which become hyperexcitable. The authors found that sympathetic motor neurons from old mice exhibit increased firing rates (spontaneous and evoked), more depolarized membrane resting potential, and increased rheobase. Furthermore, the study investigates cellular mechanisms underlying age-associated hyperexcitability and shows solid evidence supporting that a decreased activity of KCNQ2/3 channels during aging is a major contributor to the increased excitability of sympathetic old neurons. The conclusions of this paper are supported by the data.

Strengths:

Detailed and rigorous analysis of electrical responses of peripheral sympathetic motor neurons using electrophysiology (perforated patch and whole-cell recordings). The study identifies a decreased KCNQ2/3 current as a cellular mechanism behind age-induced hyperexcitability in sympathetic motor neurons.

Weaknesses:

The revised version of the manuscript has addressed all my concerns.

Reviewer #3 (Public review):

This revised study described changes in membrane excitability and Na+ and K+ current amplitudes of sympathetic motor neurons in culture. The findings indicate that neurons isolated from aged animals show increased membrane excitability manifested as increased firing rates in response to electrical stimulation and changes in related membrane properties including depolarized resting membrane potential, increased rheobase, and spontaneous firing. By contrast, neuron cultures from young mice show little to no spontaneous firing and relatively low firing rates in response to current injection. These changes in excitability correlate with reductions in the magnitude of KCNQ currents in neurons cultured from aged mice compared to neurons from cultured from young mice. The authors conclude that aging promotes hyperexcitability of sympathetic motor neurons through changes in KCNQ channels.

Author response:

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

Recommendations for the authors:

Please make corrections as suggested by reviewer 1 to improve the manuscript. Specifically, reviewer 1 suggests making changes to p values in Figure 5, and the importance of citing original scholarly works related to effects of increase in excitability of sympathetic neurons by M1 receptors, and the terminology for M currents and KCNQ currents. These changes will improve the manuscript and are strongly recommended.

The section dealing with Aging Reduces KCNQ currents seems to contain a lot of extraneous information especially in the last part of the long paragraph and this section should be rewritten for improved clarity and - the implications or lack thereof - of the correlation of KCNQ with AP firing rates. The apparent lack of correlation between KCNQ current and KCNQ2 protein needs to be better explained. This is a central part of the study and this result undercuts the premise of the paper. Additionally, the poor specificity of Linordipine for KCNQ should be pointed out in the limitations.

Finally, the editor notes that the author response should not contain ambiguities in what was addressed in the revision. In the original summary of consolidated revisions that were requested, one clearly and separately stated point (point 4) was that experiments in slice cultures should be strongly considered to extend the significance of the work to an intact brain preparation. The author response letter seems to imply that this was done, but this is not the case. The author response seems to have combined this point with another separate point (point 3) about using KCNQ drugs, and imply that all concerns were addressed. Authors should be clear about what revisions were in fact addressed.

Summary of recommendations from the three reviewers:

Please make corrections as suggested by reviewer 1 to improve the manuscript.

Specifically, reviewer 1 suggests making changes to p values in Figure 5,

As a team, we have decided to keep p values. Here is our rationale:

Our lab favors reporting p-values for all statistical comparisons to help readers identify what we consider statistically significant. We color-coded the p-values, with red for p-value < 0.05 and black for p-value > 0.05. As a reader, seeing a p-value=0.7 allows me to know that the authors performed an analysis comparing these conditions and found the mean not to be different. Not presenting the p-value makes me wonder whether the authors even analyzed those groups. We value the ability to analyze the data by seeing all p-values than not being distracted by non-significant p-values.

and the importance of citing original scholarly works related to effects of increase in excitability of sympathetic neurons by M1 receptors, and the terminology for M currents and KCNQ currents. These changes will improve the manuscript and are strongly recommended.

We cited original papers on that area and changed the terminology for M current. I kept KCNQ when referring to the channel protein or abundance.

The section dealing with Aging Reduces KCNQ currents seems to contain a lot of extraneous information especially in the last part of the long paragraph and this section should be rewritten for improved clarity… and - the implications or lack thereof - of the correlation of KCNQ with AP firing rates.

I separated the long paragraph in two. I also removed extraneous information in that section. It now reads:

Previous work by our group and others demonstrated that cholinergic stimulation leads to a decrease in M current and increases the excitability of sympathetic motor neurons at young ages.67-71 The molecular determinants of the M current are channels formed by KCNQ2 and KCNQ3 in these neurons.70, 76, 77 Thus, Figure 6A shows a voltage response (measured in current-clamp mode) and a consecutive M current recording (measured in voltage-clamp mode) in the same neuron upon stimulation of cholinergic type 1 muscarinic receptors. It illustrates the temporal correlation between the decrease of M current with the increase in excitability and firing of APs. This strong dependence led us to hypothesize that aging decreases M current, leading to a depolarized RMP and hyperexcitability (Figure 6B). For these experiments, we measured the RMP and evoked activity using perforated patch, followed by the amplitude of M current using a whole-cell voltage clamp in the same cell. We also measured the membrane capacitance as a proxy for cell size. Interestingly, M current density was smaller by 29% in middle age (7.5 ± 0.7 pA/pF) and by 55% in old (4.8 ± 0.7 pA/pF) compared to young (10.6 ± 1.5 pA/pF) neurons (Figure 6C-D). The average capacitance was similar in young (30.8 ± 2.2 pF), middle-aged (27.4 ± 1.2 pF), and old (28.8 ± 2.3 pF) neurons (Figure 6E), suggesting that aging is not associated with changes in cell size of sympathetic motor neurons, and supporting the hypothesis that aging alters the levels of M current. Next, we tested the effect on the abundance of the channels mediating M current. Contrary to our expectation, we observed that KCNQ2 protein levels were 1.5 ± 0.1 -fold higher in old compared to young neurons (Figure 6F-G). Unfortunately, we did not find an antibody to detect consistently KCNQ3 channels. We concluded that the decrease in M current is not caused by a decrease in the abundance of KCNQ2 protein.

B. and - the implications or lack thereof - of the correlation of KCNQ with AP firing rates.

I am not sure to understand the request in the section on the correlation of KCNQ with AP firing rate. I divided the long paragraph.

The apparent lack of correlation between KCNQ current and KCNQ2 protein needs to be better explained. This is a central part of the study and this result undercuts the premise of the paper.

Indeed, total KCNQ2 protein abundance increases while M current decreases. We do not claim in our work that changes in excitability are caused by a reduction in the expression or density of KCNQ2 channels. On the contrary, our current working hypothesis is that the reduction in M current is caused by changes in traffic, degradation, posttranslational modifications, or cofactors for KCNQ2 or KCNQ3 channels. I have modified the description in the results section and discussion to clarify this concept. We also note that the discussion section contains a paragraph discussing this discrepancy.

Additionally, the poor specificity of Linordipine for KCNQ should be pointed out in the limitations.

Thank you for the suggestion. I have added the following sentences to the Limitations section. It reads: “We want to point out that linopirdine has been reported to affect other ionic currents besides M current (Neacsu and Babes, 2010; Lamas et al., 1997). Despite this limitation, the application of linopirdine to young sympathetic motor neurons led to depolarization and firing of action potentials.”

Finally, the editor notes that the author response should not contain ambiguities in what was addressed in the revision. In the original summary of consolidated revisions that were requested, one clearly and separately stated point (point 4) was that experiments in slice cultures should be strongly considered to extend the significance of the work to an intact brain preparation. The author response letter seems to imply that this was done, but this is not the case. The author response seems to have combined this point with another separate point (point 3) about using KCNQ drugs, and imply that all concerns were addressed. Authors should be clear about what revisions were in fact addressed.

We apologize for this omission. After reviewing this comment, I realized I did not respond to the Major points in the section of the Recommendations for the authors from Reviewer 3. We missed that entire section. Our previous responses addressed the Public review of Reviewer 3. When doing so, we did not separate the sentences, omitting the request to perform the experiment in slices.

The proposed experiments will require an upward microscope coupled to an electrophysiology rig; unfortunately, we do not have the equipment to do these experiments. We agree that our findings need to be tested in intact preparations to understand how the hyperactivity of sympathetic motor neurons affects systemic responses and the function of controlling organ function. This is a crucial step to move the field forward. Our laboratory is trying to find the appropriate experimental design to address this problem. We believe we must go beyond redoing these experiments in slices.

Reviewer #1 (Recommendations For The Authors):

(1) The significance values greater than p < 0.05 do not add anything and distract focus from the results that are meaningful. Fig. 5 is a good example. What does p = 0.7 mean? Or p = 0.6? Does this help the reader with useful information?

We thank Reviewer 1 for raising this question. We have attempted different versions of how we report p values, as we want to make sure to address rigor and transparency in reporting data.

Our lab favors reporting p-values for all statistical comparisons to help readers identify what we consider statistically significant. We color-coded the p-values, with red for p-value < 0.05 and black for p-value > 0.05. As a reader, seeing a p-value=0.7 allows me to know that the authors performed an analysis comparing these conditions and found the mean not to be different. Not presenting the p-value makes me wonder whether the authors even analyzed those groups. We value the ability to analyze the data by seeing all p-values than not being distracted by non-significant p-values.

(2) Fig. 1 is not informative and should be removed.

Although we agree with the reviewer that this figure is not informative, it was created to guide the reader in identifying the problem addressed in our manuscript in the physiological context. Our colleagues who read the first drafts of the manuscript recommended this, so we prefer to keep the figure.

(3) The emphasis on a particular muscarinic agonist favored by many ion channel physiologists, oxotremorine, is not meaningful (lines 192, 198). The important point is stimulation of muscarinic AChRs, which physiologically are stimulated by acetylcholine. The particular muscarinic agonist used is unimportant. Unless mandated by eLife, "cholinergic type 1 muscarinic receptors" are usually referred to as M1 mAChRs, or even better is "Gq-coupled M1 mAChRs." I don't think that Kruse and Whitten, 2021 were the first to demonstrate the increase in excitability of sympathetic neurons from stimulation of M1 mAChRs. Please try and cite in a more scholarly fashion.

A) We have modified lines 192 and 198, removing the mention of oxotremorine.

B) We have modified the nomenclature used to refer to cholinergic type 1 muscarinic receptors.

C) We cited references on the role of M current on sympathetic motor neuron excitability.

(4) The authors may want to use the term "M current" (after defining it) as the current produced by KCNQ2&3-containing channels in sympathetic neurons, and reserve "KCNQ" or "Kv7" currents as those made by cloned KCNQ/Kv7 channels in heterologous systems. A reason for this is to exclude currents KCNQ1-containing channels, which most definitely do not contribute to the "KCNQ" current in these cells. I am not mandating this, but rather suggesting it to conform with the literature.

Thank you for the suggestion. I have modified the text to use the term M current. I maintained the use of KCNQ only when referring to KCNQ channel, such as in the section describing the abundance of KCNQ2.

(5) The section in the text on "Aging reduces KCNQ current" is confusing. Can the authors describe their results and their interpretation more directly?

(6) Please explain the meaning of the increase in KCNQ2 abundance with age in Fig. 6G. How is this increase in KCNQ2 expression consistent with an increase in excitability? The explanation of "The decrease in KCNQ current and the increase in the abundance of KCNQ2 protein suggest a potential compensatory mechanism that occurs during aging, which we are actively investigating in an independent study." is rather odd, considering that the entire thesis of this paper is that changes in excitability and firing properties are underlied by changes in KCNQ2/3 channel expression/density. Suddenly, is this not the case?? What about KCNQ3? It would be very enlightening if the authors would just quantify the ratio of KCNQ2:KCNQ3 subunits in M-type channels in young and old mice using simple TEA dose/response curves (see Shapiro et al., JNS, 2000; Selyanko et al., J. Physiol., Hadley et al., Br. J. Pharm., 2001 and a great many more). It is also surprising that the authors did not assess or probe for differences in mAChR-induced suppression of M current between SCG neurons of young and old mice. This would seem to be a fundamental experiment in this line of inquiry.

We have divided this paragraph in sections.

A. Please explain the meaning of the increase in KCNQ2 abundance with age in Fig. 6G. How is this increase in KCNQ2 expression consistent with an increase in excitability? The explanation of "The decrease in KCNQ current and the increase in the abundance of KCNQ2 protein suggest a potential compensatory mechanism that occurs during aging, which we are actively investigating in an independent study." is rather odd, considering that the entire thesis of this paper is that changes in excitability and firing properties are underlied by changes in KCNQ2/3 channel expression/density. Suddenly, is this not the case??

Our interpretation is that the decrease in M current is not caused by a decrease in the abundance of KCNQ (2) channels. We do not claim that changes in excitability are caused by a reduction in the expression or density of KCNQ2 channels. On the contrary, our working hypothesis is that the reduction in M current is caused by changes in traffic, degradation, posttranslational modifications, or cofactors for KCNQ2 or KCNQ3 channels. We have modified the description in the results section to clarify this concept. “We concluded that the decrease in M current is not caused by a decrease in the abundance of KCNQ2 protein.”

B. What about KCNQ3?

Unfortunately, we did not find an antibody to detect KCNQ3 channels. I have added a sentence to state this.

C. KCNQ2: KCNQ3 subunits in M-type channels in young and old mice using simple TEA dose/response curves.

Our laboratory is working to deeply understand the mechanism behind the changes in M current and its regulation by mAChRs in young and old ages. However, it is part of different research to attend to the complexity of the question. We think pharmacology experiments are insufficient to understand the question's complexity as we described in the next answer.

D. It is also surprising that the authors did not assess or probe for differences in mAChR-induced suppression of M current between SCG neurons of young and old mice. This would seem to be a fundamental experiment in this line of inquiry.

As mentioned, our laboratory is working to understand the mechanism behind M current and its regulation in young and old ages deeply. Our preliminary data show that M currents recorded in old neurons show two behaviors with the activation of mAChR: 1) they do not respond (blue line), or 2) they show a smaller and slower current inhibition than young neurons (red line). This data shows the complexity of the mechanism behind the M current in old neurons where changes in basal levels of PIP2, phospholipids metabolism, KCNQ2/3 changes in traffic/degradation, and M current pharmacology need to be addressed together for a proper interpretation. Showing only one part of this set of experiments in this article may lead to misinterpretation of results.

Author response image 1.

(7) Why do the authors use linopirdine instead of XE-991? Both are dirty drugs hardly specific to KCNQ channels at 25 uM concentrations, but linopirdine less so. The Methods section lists the source of XE991 used in the study, not linopirdine. Is there an error?

A. Why do the authors use linopirdine instead of XE-991?

We use linopiridine with the experimental goal of observing the recovery phase during the washout. The main difference between the effects of XE991 and linopiridine on Kv7.2/3 is associated with the recovery phase. Currents under XE991 treatment recover 30% after 10 min compared to 93.4% with linopiridine in expression systems at -30 mV (Greene DL et al., 2017, J Pharmacol Exp Ther). After validation of KCNQ2/3 inhibition by linopirdine (IC50 value of 2.4 µM), we found linopirdine the most appropriate drug for our experiments.

Unfortunately, we were not able to observe a recovery in our experiments. The limited recovery after washout may be associated with the membrane potential of our conditions (-60 to -50 mV).

B. Both are dirty drugs hardly specific to KCNQ channels at 25 uM concentrations, but linopirdine less so.

We understand the concern of the reviewer. The specificity of XE-991 and linopiridine is not absolute. Linopiridine has been reported to activate TRPV1 channels (EC50 =115 µM, Neacsu and Babes, 2010, J Pharmacol Sci) or nicotinic acetylcholine receptors and GABA-induced Cl- currents (EC50 =7.6 µM and 8.1 µM respectively; Lamas et al, 1997, Eur J Neurosci).

To clarify this limitation in the article, we have added the following sentence in the section Limitations and Conclusions. “We want to point out that linopirdine has been reported to affect other ionic currents besides M current (Neacsu and Babes, 2010; Lamas et al., 1997). Despite this limitation, the application of linopirdine to young sympathetic motor neurons led to depolarization and firing of action potentials.”

C. The Methods section lists the source of XE991 used in the study, not linopirdine. Is there an error?

Thank you for pointing out this. We have added information for both retigabine and linopirdine in the Methods section; both were missing.

(8) Can the authors use a more scientific explanation of RTG action than "activating KCNQ channels?" For instance, RTG induces both a negative-shift in the voltage-dependance of activation and a voltage-independent increase in the open probability, both of which differing in detail between KCNQ2 and KCNQ3 subunits. The authors are free to use these exact words. Thus, the degree of "activation" is very dependent upon voltage at any voltages negative to the saturating voltages for channel activation.

We have modified the text to reflect your suggestion. Thank you.

(9) Methods: did the authors really use "poly-l-lysine-coated coverslips?" Almost all investigators use poly-D-lysine as a coating for mammalian tissue-culture cells and more substantial coatings such as poly-D-lysine + laminin or rat-tail collagen for peripheral neurons, to allow firm attachment to the coverslip.

That is correct. We used poly-L-lysine-coated coverslips. Sympathetic motor neurons do not adhere to poly-D-Lysine.

(10) As a suggestion, sampling M-type/KCNQ/Kv7 current at 2 kHz is not advised, as this is far faster than the gating kinetics of the channels. Were the signals filtered?

Signals were not filtered. Currents were sampled at 2KHz. Our conditions are not far from what is reported by others. Some sample at 10KHz and even 50 KHz. Others do not report the sample frequency.

Reviewer #2:

Weaknesses:

None, the revised version of the manuscript has addressed all my concerns.

We are very appreciative and glad that our responses satisfied your previous concerns.

Reviewer #3:

The main weakness is that this study is a descriptive tabulation of changes in the electrophysiology of neurons in culture, and the effects shown are correlative rather than establishing causality.

In the previous revision, Reviewer 3 wrote: “It is difficult to know from the data presented whether the changes in KCNQ channels are in fact directly responsible for the observed changes in membrane excitability.” And suggested the “use of blockers and activators to provide greater relevance.”

Attending this recommendation, we performed experiments in Fig. 8. Young neurons exposed to linopirdine depolarize membrane potential and promote action potential firing. In contrast, the old neurons treated with retigabine repolarize membrane potential and stop firing action potentials. This new set of experiments suggests age-related electrophysiological changes in old neurons are associated with changes in M current. The main finding of our article.

If Reviewer 3 refers to establishing causality between aging and a reduction in M current, I would like to emphasize that our laboratory is working toward a better understanding of the molecular mechanism of how M current is affected by aging; however, it will be part of a different article.  One of our attempts was to reverse aging with rapamycin, but the previous recommendation was to remove those experiments.

… but the specifics of the effects and relevance to intact preparations are unclear.

Additional experiments in slice cultures would provide greater significance on the potential relevance of the findings for intact preparations.

I apologize for missing this point in the previous revision. The proposed experiments will require an upward microscope coupled to an electrophysiology rig. Unfortunately, I do not

have the equipment to do these experiments.

eLife assessment

This study presents useful findings for how sevoflurane anesthesia modulates the activity of corticotropin-releasing hormone neurons in the paraventricular nucleus of the hypothalamus and how manipulation of such PVHCRH neurons influences anesthesia and post-anesthesia responses. The technical approaches are solid and the data presented is largely clear. Whether PVHCRH neurons are critical for the mechanisms of sevoflurane anesthesia is a direction for the future.

Joint Public Review:

This study describes a group of CRH-releasing neurons, located in the paraventricular nucleus of the hypothalamus, which, in mice, affects both the state of sevoflurane anesthesia and a grooming behavior observed after it. PVHCRH neurons showed elevated calcium activity during the post-anesthesia period. Optogenetic activation of these PVHCRH neurons during sevoflurane anesthesia shifts the EEG from burst-suppression to a seemingly activated state (an apparent arousal effect), although without a behavioral correlate. Chemogenetic activation of the PVHCRH neurons delays sevoflurane-induced loss of righting reflex (another apparent arousal effect). On the other hand, chemogenetic inhibition of PVHCRH neurons delays recovery of righting reflex and decreases sevoflurane-induced stress (an apparent decrease in the arousal effect). The authors conclude that PVHCRH neurons "integrate" sevoflurane-induced anesthesia and stress. The authors also claim that their findings show that sevoflurane itself produces a post-anesthesia stress response that is independent of any surgical trauma, such as an incision. In its revised form, the article does not achieve its intended goal and will not have impact on the clinical practice of anesthesiology nor on anesthesiology research.

Strengths:

The manuscript uses targeted manipulation of the PVHCRH neurons with state-of-the-art methods and is technically sound. Also, the number of experiments is substantial.

Weaknesses:

The most significant weaknesses remain: a) overinterpretation of the significance of their findings b) the failure to use another anesthetic as a control, c) a failure to compellingly link their post-sevoflurane measures in mice to anything measured in humans, and d) limitations in the novelty of the findings. These weaknesses are related to the primary concerns described below:

Concerns about the primary conclusion that PVHCRH neurons integrate the anesthetic effects and post-anesthesia stress response of sevoflurane GA:

It is important to compare the effects of sevoflurane with at least one other inhaled ether anesthetic as one step towards elevating the impact of this paper to the level required for a journal such as eLife. Isoflurane, desflurane, and enflurane are ether anesthetics that are very similar to each other, as well as being similar to sevoflurane. For example, one study cited by the authors (Marana et al. 2013) concludes that there is weak evidence for differences in stress-related hormones between sevoflurane and desflurane, with lower levels of cortisol and ACTH observed during the desflurane intraoperative period. It is important to determine whether desflurane activates PVHCRH neurons in the post-anesthesia period, and whether this is accompanied by excess grooming in the mice because this will distinguish whether the effects of sevoflurane generalize to other inhaled anesthestics, or, alternatively, relate to unique idiosyncratic properties of this gas that may not be a part of its anesthetic properties.

Concerns about the clinical relevance of the experiments:

In anesthesiology practice, perioperative stress observed in patients is more commonly related to the trauma of the surgical intervention, with inadequate levels of antinociception or unconsciousness intraoperatively and/or poor post-operative pain control. The authors seem to be suggesting that the sevoflurane itself is causing stress because their mice receive sevoflurane but no invasive procedures, but there is no evidence of sevoflurane inducing stress in human patients. It is important to know whether sevoflurane effectively produces behavioral stress in the recovery room in patients that could be related to the putative stress response (excess grooming) observed in mice. For example, in surgeries or procedures which required only a brief period of unconsciousness that could be achieved by administering sevoflurane alone (comparable to the 30 min administered to the mice), is there clinical evidence of post-operative stress? It is also important to describe a rationale for using a 30 min sevoflurane exposure. What proportion of human surgeries using sevoflurane use exposure times that are comparable to this?

It is the experience of one of the reviewers that human patients who receive sevoflurane as the primary anesthetic do not wake up more stressed than if they had had one of the other GABAergic anesthetics. If there were signs of stress upon emergence (increased heart rate, blood pressure, thrashing movements) from general anesthesia, this would be treated immediately. The most likely cause of post-operative stress behaviors in humans is probably inadequate anti-nociception during the procedure, which translates into inadequate post-op analgesia and likely delirium. It is the case that children receiving sevoflurane do have a higher likelihood of post-operative delirium. Perhaps the authors' studies address a mechanism for delirium associated with sevoflurane, but this is barely mentioned. Delirium seems likely to be the closest clinical phenomenon to what was studied. As noted by the Besnier et al (2017) article cited by the authors, surgery can elevate postoperative glucocorticoid stress hormones, but it generally correlates with the intensity of the surgical procedure. Besnier et al also note the elevation of glucocorticoids is generally considered to be adaptive. Thus, reducing glucocorticoids during surgery with sevoflurane may hamper recovery, especially as it relates to tissue damage, which was not measured or considered here. This paper only considers glucocorticoid release as a negative factor, which causes "immunosuppression", "proteolysis", and "delays postoperative recovery and...leads to increased morbidity".

It is also the case that there are explicit published findings showing that mild and moderate surgical procedures in children receiving sevoflurane (which might be the closest human proxy to the brief 30 minute sevoflurane exposure used here) do not have elevated cortisol (Taylor et al, J Clin Endocrinol Metab, 2013). This again raises the question of whether the enhanced grooming or elevated corticosterone observed in the mice here has any relevance to humans.

Concerns about the novelty of the findings:

The key finding here is that CRH neurons mediate measures of arousal, and arousal modulates sevoflurane anesthesia induction and recovery. However, CRH is associated with arousal in numerous studies. In fact, the authors' own work, published in eLife in 2021, showed that stimulating the hypothalamic CRH cells lead to arousal and their inhibition promoted hypersomnia. In both papers the authors use fos expression in CRH cells during a specific event to implicate the cells, then manipulate them and measure EEG responses. In the previous work, the cells were active during wakefulness; here- they were active in the awake state the follows anesthesia (Figure 1). Thus, the findings in the current work are incremental and not particularly impactful. Claims like "Here, a core hypothalamic ensemble, corticotropin-releasing hormone neurons in the paraventricular nucleus of the hypothalamus, is discovered" are overstated. PVHCRH cell populations were discovered in the 1980s. Suggesting that it is novel to identify that hypothalamic CRH cells regulate post-anesthesia stress is unfounded as well: this PVH population has been shown over four decades to regulate a plethora of different responses to stress. Anesthesia stress is no different. Their role in arousal is not being discovered in this paper. Even their role in grooming is not discovered in this paper.

The activation of CRH cells in PVH has already been shown to result in grooming by Jaideep Bains (a paper cited by the authors). Thus, the involvement of these cells in this behavior is not surprising. The authors perform elaborate manipulations of CRH cells and numerous analyses of grooming and related behaviors. For example, they compare grooming and paw licking after anesthesia with those after other stressors such as forced swim, spraying mice with water, physical attack and restraint. The authors have identified a behavioral phenomenon in a rodent model that does not have a clear correlation with a behavior state observed in humans during the use of sevoflurane as part of an anesthetic regimen. The grooming behaviors are not a model of the emergence delirium or the cognitive dysfunction observed commonly in patients receiving sevoflurane for general anesthesia. Emergence delirium is commonly seen in children after sevoflurane is used as part of general anesthesia and cognitive dysfunction is commonly observed in adults-particularly the elderly -- following general anesthesia.

Author response:

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

Public reviews

This study describes a group of CRH-releasing neurons, located in the paraventricular nucleus of the hypothalamus, which, in mice, affects both the state of sevoflurane anesthesia and a grooming behavior observed after it. PVHCRH neurons showed elevated calcium activity during the post-anesthesia period. Optogenetic activation of these PVHCRH neurons during sevoflurane anesthesia shifts the EEG from burst-suppression to a seemingly activated state (an apparent arousal effect), although without a behavioral correlate. Chemogenetic activation of the PVHCRH neurons delays sevoflurane-induced loss of righting reflex (another apparent arousal effect). On the other hand, chemogenetic inhibition of PVHCRH neurons delays recovery of righting reflex and decreases sevoflurane-induced stress (an apparent decrease in the arousal effect). The authors conclude that PVHCRH neurons "integrate" sevoflurane-induced anesthesia and stress. The authors also claim that their findings show that sevoflurane itself produces a post-anesthesia stress response that is independent of any surgical trauma, such as an incision. In its revised form, the article does not achieve its intended goal and will not have impact on the clinical practice of anesthesiology nor on anesthesiology research.

Thanks for the reviews. Please see our responses to the following comments.

Weaknesses:

The most significant weaknesses remain:

a) overinterpretation of the significance of their findings

b) the failure to use another anesthetic as a control,

c) a failure to compellingly link their post-sevoflurane measures in mice to anything measured in humans, and

d) limitations in the novelty of the findings. These weaknesses are related to the primary concerns described below:

Concerns about the primary conclusion that PVHCRH neurons integrate the anesthetic effects and post-anesthesia stress response of sevoflurane GA

(1) After revision, their remain multiple places where it is claimed that PVHCRH neurons mediate the anesthetic effects of sevoflurane (impact statement: we explain "how sevoflurane-induced general anesthesia works..."; introduction: "the neuronal mechanisms that mediate the anesthetic effects...of sevoflurane GA remain poorly understood" and "PVHCRH neurons may act as a crucial node integrating the anesthetic effect and stress response of sevoflurane").The manuscript simply does not support these statements. The authors show that a short duration exposure to sevoflurane inhibits PVHCRH neurons, but this is followed by hyperexcitability of these neurons for a short period after anesthesia is terminated. They show that the induction and recovery from sevoflurane anesthesia can be modulated by PVHCRH neuronal activity, most likely through changes in brain state (measured by EEG). They also show that PVHCRH neuronal activity modulates corticosterone levels and grooming behavior observed post-anesthesia (which the authors argue are two stress responses).These two things (effects during anesthesia and effects post-anesthesia)may be mechanistically unrelated to each other. None of these observations relate to the primary mechanism of action for sevoflurane. All claims relating to "anesthetic effects" should be removed. Even the term "integration" seems wrong-it implies the PVH is combining information about the anesthetic effect and post-anesthesia stress responses.

As requested, we have removed all claims related to ‘anesthetic effects’ or ‘integration’. Please see the revised manuscript.

(2) lt is important to compare the effects of sevoflurane with at least one other inhaled ether anesthetic as one step towards elevating the impact of this paper to the level required for a journal such as eLife. Isoflurane, desflurane, and enflurane are ether anesthetics that are very similar to each other, as well as being similar to sevoflurane. For example, one study cited by the authors (Marana et al.2013) concludes that there is weak evidence for differences in stress-related hormones between sevoflurane and desflurane, with lower levels of cortisol and ACTH observed during the desflurane intraoperative period. It is important to determine whether desflurane activates PVHCRH neurons in the post-anesthesia period, and whether this is accompanied by excess grooming in the mice, because this will distinguish whether the effects of sevoflurane generalize to other inhaled anesthestics, or, alternatively, relate to unique idiosyncratic properties of this gas that may not be a part of its anesthetic properties.

Thanks for your insightful comments and suggestions. Regarding your request for additional experiments, we acknowledge the value they could add to our study. However, investigating whether the effects of sevoflurane generalize to other inhaled anesthetics is beyond the scope of our current study. There is evidence indicating the prevalence of anesthetic stress caused by inhaled ether anesthetics1,2. The post-anesthesia stress-related behaviors caused by sevoflurane administration are reminiscent of delirium observed clinically. Notably, studies have shown that the use of desflurane for maintenance of anesthesia did not significantly affect the incidence or duration of delirium compared to sevoflurane administration3. This suggests that our observations likely represent a generalized response to inhaled ether anesthetic rather than being specific to sevoflurane.

Concerns about the clinical relevance of the experiments

In anesthesiology practice, perioperative stress observed in patients is more commonly related to the trauma of the surgical intervention, with inadequate levels of antinociception or unconsciousness intraoperatively and/or poor post-operative pain control. The authors seem to be suggesting that the sevoflurane itself is causing stress because their mice receive sevoflurane but no invasive procedures, but there is no evidence of sevoflurane inducing stress in human patients. It is important to know whether sevoflurane effectively produces behavioral stress in the recovery room in patients that could be related to the putative stress response (excess grooming) observed in mice. For example, in surgeries or procedures which required only a brief period of unconsciousness that could be achieved by administering sevoflurane alone (comparable to the 30 min administered to the mice), is there clinical evidence of post-operative stress? It is also important to describe a rationale for using a 30 min sevoflurane exposure. What proportion of human surgeries using sevoflurane use exposure times that are comparable to this?

It is also the case that there are explicit published findings showing that mild and moderate surgical procedures in children receiving sevoflurane (which might be the closest human proxy to the brief 30 minutes sevoflurane exposure used here) do not have elevated cortisol (Taylor et al, J Clin Endocrinol Metab, 2013). This again raises the question of whether the enhanced grooming or elevated corticosterone observed in the mice here has any relevance to humans.

Thanks for the comments. Most ear, nose, and throat surgeries in children involve a short period of anesthesia with sevoflurane alone4-6, which is similar to the 30-minute exposure in our mouse study. In clinical settings, emergence delirium and agitation are common in young children undergoing sevoflurane anesthesia7, often accompanied by troublesome excitation phenomena during induction and awakening8. These clinical observations align with the post-operative stress response (e.g., excessive grooming) we identified in our study.

It is the experience of one of the reviewers that human patients who receive sevoflurane as the primary anesthetic do not wake up more stressed than if they had had one of the other GABAergic anesthetics. If there were signs of stress upon emergence (increased heart rate, blood pressure, thrashing movements) from general anesthesia, this would be treated immediately. The most likely cause of post-operative stress behaviors in humans is probably inadequate anti-nociception during the procedure, which translates into inadequate post-op analgesia and likely delirium. It is the case that children receiving sevoflurane do have a higher likelihood of post-operative delirium. Perhaps the authors' studies address a mechanism for delirium associated with sevoflurane, but this is barely mentioned. Delirium seems likely to be the closest clinical phenomenon to what was studied. As noted by the Besnier et al (2017) article cited by the authors, surgery can elevate postoperative glucocorticoidstress hormones, but it generally correlates with the intensity of the surgical procedure. Besnier et al also note the elevation of glucocorticoids is generally considered to be adaptive. Thus, reducing glucocorticoids during surgery with sevoflurane may hamper recovery, especially as it relates to tissue damage, which was not measured or considered here. This paper only considers glucocorticoid release as a negative factor, which causes "immunosuppression", "proteolysis", and "delays postoperative recovery and leads to increased morbidity".

Thanks for the comments. We agree that the post-anesthetic stress behaviors mentioned in our manuscript are similar to the clinical phenomenon of delirium, which were defined in Cheng Li’s study as ‘sevoflurane-induced post-operative delirium’9. Therefore, we conducted additional behavioral tests for cognitive function, including the Y-maze and novel object recognition test, in mice administrated 30-minute sevoflurane anesthesia. The results demonstrate that chemogenetic inhibition of PVHCRH neurons ameliorated the short-term memory impairment in mice exposed to 30-minute sevoflurane GA (Figure 7-figure supplement 9), suggesting PVHCRH neurons may involve in modulating sevoflurane-induced postoperative delirium.

Concerns about the novelty of the findings:

The key finding here is that CRH neurons mediate measures of arousal, and arousal modulates sevoflurane anesthesia induction and recovery. However, CRH is associated with arousal in numerous studies. In fact, the authors' own work, published in eLife in 2021, showed that stimulating the hypothalamic CRH cells lead to arousal and their inhibition promoted hypersomnia. In both papers the authors use fos expression in CRH cells during a specific event to implicate the cells, then manipulate them and measure EEG responses. In the previous work, the cells were active during wakefulness; here- they were active in the awake state the follows anesthesia (Figure1). Thus, the findings in the current work are incremental and not particularly impactful. Claims like "Here, a core hypothalamic ensemble, corticotropin-releasing hormone neurons in the paraventricular nucleus of the hypothalamus, is discovered" are overstated. PVHCRH cell populations were discovered in the 1980s. Suggesting that it is novel to identify that hypothalamic CRH cells regulate post-anesthesia stress is unfounded as well: this PVH population has been shown over four decades to regulate a plethora of different responses to stress. Anesthesia stress is no different. Their role in arousal is not being discovered in this paper. Even their role in grooming is not discovered in this paper.

Thanks for the comments. As requested, we have revised our manuscript by removing overstated sentences. Please see the revised manuscript. In terms of novelty, our study reveals that PVHCRH neurons are implicated not only in the induction and emergence of sevoflurane general anesthesia but also in sevoflurane-induced post-operative delirium. This finding represents a novel contribution to the field, as it has not been previously reported by other studies.

The activation of CRH cells in PVH has already been shown to result in grooming by Jaideep Bains (a paper cited by the authors). Thus, the involvement of these cells in this behavior is not surprising. The authors perform elaborate manipulations of CRH cells and numerous analyses of grooming and related behaviors. For example, they compare grooming and paw licking after anesthesia with those after other stressors such as forced swim, spraying mice with water, physical attack and restraint. The authors have identified a behavioral phenomenon in a rodent model that does not have a clear correlation with a behavior state observed in humans during the use of sevoflurane as part of an anesthetic regimen. The grooming behaviors are not a model of the emergence delirium or the cognitive dysfunction observed commonly in patients receiving sevoflurane for general anesthesia. Emergence delirium is commonly seen in children after sevoflurane is used as part of general anesthesia and cognitive dysfunction is commonly observed in adults-particularly the elderly-- following general anesthesia. No features of delirium or cognitive dysfunction are measured here.

As requested, behavioral tests for cognitive function have been conducted and displayed in Figure 7-figure supplement 9.

Other concerns:

In Figure 2, cFos was measured in the PVH at different points before, during and after sevoflurane. The greatest cFos expression was seen in Post 2, the latest time point after anesthesia. However, this may simply reflect the fact that there is a delay between activity levels and expression of cFos (as noted by the authors, 2-3 hours). Thus, sacrificing mice 30 minutes after the onset of sevoflurane application would be expected to drive minimal cFos expression, and the cFos observed at 30 minutes would not accurately reflect the activity levels during the sevoflurane. Also, the authors state that the hyperactivity, as measured by cFos, lasted "approximately 1 hours before returning to baseline", but there is no data to support this return to baseline.

Thanks for the comments. We apologize that the protocol we used for c-fos staining may not accurately reflect the activity levels, so we have removed Figure 2F. The sentence ‘lasted approximately 1 hours before returning to baseline’ refers to the calcium signal but not c-fos level.

In Figure 7, the number of animals appears to change from panel to panel even though they are supposed to show animals from the same groups. For example, cort was measured in only 3 saline-treated O2 animals (Fig 7E), but cFos and CRH were assessed in 4 (Fig C,D). Similarly, grooming time and time spent in open arms was measured in 6 saline-treated O2 controls (Fig 7F, H) but central distance was measured in 8(Fig 7G). There are other group number discrepancies in this figure--the number of data points in the plots do not match what is reported in the legend for numerous groups. Similarly, Figure 4 has a mismatch between the Ns reported in the legend and the number of points plotted per bar. For example, there were 10 animals in the hM3Di group; all are shown for the LORR and time to emergence plots, but only8 were used for time to induction. The legends reported N=7 for the mCherry group, yet 9 are shown for the time to emergence panel. No reason for exclusions is cited. These figures (and their statistics) should be corrected.

Thanks for the comments. We have rechecked and corrected our figures and illustrations in the revised manuscript.

Recommendations for the authors:

In Figure 6, the BSR pre-stim data points for panels F and H look exactly identical, even though these data are from two different sets of mice. It seems likely that one of these panels is not depicting the correct pre-stim data points. Please check this.

Thanks for the comments. We have corrected this mistake.

General anesthesia is a combination of behavioral and physiological states induced and maintained primarily by pharmacologic agents. The authors do not provide a definition of general anesthesia.

Thanks for the advice. We have added the definition of general anesthesia in the introduction part.

The first sentence of the abstract closely resembles the first sentence of the abstract of Brown，Purdon and Van Dort,Annu. Rev. Neurosci. 2011,34:601-28 yet, there is no citation.

Thanks for the comments. We have revised the first sentence.

ln the Discussion, the authors cite the research on circuitry that is relevant for emergence from general anesthesia. Conspicuously missing from this section of the paper is the large body of work by Solt and colleagues which has demonstrated that dopamine agonists (such as methylphenidate), electrical stimulation of the ventral tegmental area and optogenetic stimulation of the D1 neurons in the ventral tegmental area can hasten emergence from general anesthesia. Also omitted is the work of Kelzand colleagues and a discussion of neural inertia.

Thanks for the suggestions. We have added these citations as requested.

As regards the weaknesses of p-values for reporting the results of scientific studies, l offer the following reference to the authors. Ronald L. Wasserstein & Nicole A.Lazar (2016)The ASA Statement on p-Values: Context, Process, and Purpose, The American Statistician,70:2,129- 133, DOl:10.1080/00031305.2016.1154108

Thanks for the suggestions. We have revised the manuscript as requested.

The methods for the CRF antibody are unclear. It was previously suggested that the antibody be validated (for example, show an absence of immunostaining with CRF knockdown) because the concentration of antiserum (1:800) is quite high, suggesting either the antibody is not potent or (more concerning) not specific. The methods also indicated that colchicine was infused ICV prior to perfusion for staining of cFos and CRF, but no surgical methods are described that would enable ICV infusion, and it is not clear why colchicine was used. Please clarify.

The anti-CRF antibody is validated by other studies11,12. F For CRF immunostaining, animals' brains were pre-treated with intraventricular injections of colchicine (20 μg in 500 nL saline) 24 hours before perfusion to inhibit fast axonal transport13,14. Additional details regarding these methods have been included in the Method section of the revised manuscript.

Editor's note:

Full statistical reporting including exact p-values alongside summary statistics (test statistic and df) and 95% confidence intervals is lacking.

Thanks for the suggestions. We have added full statistical reporting in the revised manuscript as requested.

Reference

(1) Marana, E. et al. Desflurane versus sevoflurane: a comparison on stress response. Minerva Anestesiol 79, 7-14 (2013).

(2) Yang, L., Chen, Z. & Xiang, D. Effects of intravenous anesthesia with sevoflurane combined with propofol on intraoperative hemodynamics, postoperative stress disorder and cognitive function in elderly patients undergoing laparoscopic surgery. Pak J Med Sci 38, 1938-1944, doi:10.12669/pjms.38.7.5763 (2022).

(3) Driscoll, J. N. et al. Comparing incidence of emergence delirium between sevoflurane and desflurane in children following routine otolaryngology procedures. Minerva Anestesiol 83, 383-391, doi:10.23736/s0375-9393.16.11362-8 (2017).

(4) Galinkin, J. L. et al. Use of intranasal fentanyl in children undergoing myringotomy and tube placement during halothane and sevoflurane anesthesia. Anesthesiology 93, 1378-1383, doi:10.1097/00000542-200012000-00006 (2000).

(5) Greenspun, J. C., Hannallah, R. S., Welborn, L. G. & Norden, J. M. Comparison of sevoflurane and halothane anesthesia in children undergoing outpatient ear, nose, and throat surgery. J Clin Anesth 7, 398-402, doi:10.1016/0952-8180(95)00071-o (1995).

(6) Messieha, Z. Prevention of sevoflurane delirium and agitation with propofol. Anesth Prog 60, 67-71, doi:10.2344/0003-3006-60.3.67 (2013).

(7) Shi, M. et al. Dexmedetomidine for the prevention of emergence delirium and postoperative behavioral changes in pediatric patients with sevoflurane anesthesia: a double-blind, randomized trial. Drug Des Devel Ther 13, 897-905, doi:10.2147/dddt.S196075 (2019).

(8) Veyckemans, F. Excitation and delirium during sevoflurane anesthesia in pediatric patients. Minerva Anestesiol 68, 402-405 (2002).

(9) Xu, Y., Gao, G., Sun, X., Liu, Q. & Li, C. ATPase Inhibitory Factor 1 Is Critical for Regulating Sevoflurane-Induced Microglial Inflammatory Responses and Caspase-3 Activation. Front Cell Neurosci 15, 770666, doi:10.3389/fncel.2021.770666 (2021).

(10) Friedman, E. B. et al. A conserved behavioral state barrier impedes transitions between anesthetic-induced unconsciousness and wakefulness: evidence for neural inertia. PLoS One 5, e11903, doi:10.1371/journal.pone.0011903 (2010).

(11) Giardino, W. J. et al. Parallel circuits from the bed nuclei of stria terminalis to the lateral hypothalamus drive opposing emotional states. Nat Neurosci 21, 1084-1095, doi:10.1038/s41593-018-0198-x (2018).

(12) Yeo, S. H., Kyle, V., Blouet, C., Jones, S. & Colledge, W. H. Mapping neuronal inputs to Kiss1 neurons in the arcuate nucleus of the mouse. PLoS One 14, e0213927, doi:10.1371/journal.pone.0213927 (2019).

(13) de Goeij, D. C. et al. Repeated stress-induced activation of corticotropin-releasing factor neurons enhances vasopressin stores and colocalization with corticotropin-releasing factor in the median eminence of rats. Neuroendocrinology 53, 150-159, doi:10.1159/000125712 (1991).

(14) Yuan, Y. et al. Reward Inhibits Paraventricular CRH Neurons to Relieve Stress. Curr Biol 29, 1243-1251.e1244, doi:10.1016/j.cub.2019.02.048 (2019).

eLife assessment

This valuable study explores a new strategy of lysin-derived antimicrobial peptide-primed screening to find peptidoglycan hydrolases from bacterial proteomes. Using this strategy, the authors identified five peptidoglycan hydrolases from Acinetobacter baumannii, which they tested on various Gram-positive and Gram-negative pathogens for antimicrobial activity. The revised manuscript addressed most of the prior concerns, and the data presented are solid and will be of interest to microbiologists.

Reviewer #1 (Public review):

Summary:

Li Zhang et al. characterized two new Gram-negative endolysins identified through an AMP-targeted search in bacterial proteomes. These endolysins exhibit broad lytic activity against both Gram-negative and Gram-positive bacteria and retain significant antimicrobial activity even after prolonged exposure to high temperatures (100{degree sign}C for 1 hour). This stability is attributed to a temperature-reversible transition from a dimer to a monomer. The authors suggest several potential applications, such as complementing heat sterilization processes or being used in animal feed premixes that undergo high-temperature pelleting, which I agree with.

Strengths:

The claims are well-supported by relevant and complementary assays, as well as extensive bioinformatic analyses.

Weaknesses:

My last comments are minor and nearly all aim to improve the use of English language in the manuscript. However, a section describing the statistical analysis is still lacking. I believe that the presented manuscript can benefit from language editing, but I leave this decision with the editor.

Reviewer #2 (Public review):

Summary:

The study explores a new strategy of lysin-derived antimicrobial peptide-primed screening to find peptidoglycan hydrolases from bacterial proteomes. Using this strategy authors identified five peptidoglycan hydrolases from A. baumannii. They further tested their antimicrobial activities on various Gram positive and Gram-negative pathogens.

Strengths:

Overall, the study is good and adds new members to the peptidoglycan hydrolases family. The authors also show that these lysins have bactericidal activities against both Gram-positive and Gram-negative bacteria. The crystal structure data is good, reveals different thermostablility to the peptidoglycan hydrolases. Structural data also reveals that PhAb10 and PHAb11 form thermostable dimer and data is corroborated by generating variant protein defective in supporting intermolecular bond pairs. The mice bacterial infection shows promise for the use of these hydrolases as antimicrobial agents.

Weaknesses:

While the authors have employed various mechanisms to justify their findings, some aspects are still unclear. Only CFU has been used to test bactericidal activity. This should also be corroborated by live/dead assay. Moreover, SEM or TEM analysis would reveal the effect of these peptidoglycan hydrolases on Gram-negative /Gram-positive cell envelopes. The authors claim that these hydrolases are similar to T4 lysozyme, but they have not correlated their findings with already published findings on T4 lysozyme. T4 lysozyme has C-terminal amphipathic helix with antimicrobial properties. Moreover, heat, denatured lysozyme also shows enhanced bactericidal activity due to the formation of hydrophobic dimeric forms, which are inserted in the membrane. Authors also observe that heat denatured PHAb10 and PHAb11 have bactericidal activity but no enzymatic activity. These findings should be corroborated by studying the effect of these holoenzymes/ truncated peptides on bacterial cell membranes. Also, a quantitative peptidoglycan cleavage assay should be performed in addition to halo assay. Including these details would make the work more comprehensive.

Revised version: The authors have addressed most of the questions in the revised version of the paper.

Author response:

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

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

Li Zhang et al. characterized two new Gram-negative endolysins identified through an AMPtargeted search in bacterial proteomes. These endolysins exhibit broad lytic activity against both Gram-negative and Gram-positive bacteria and retain significant antimicrobial activity even after prolonged exposure to high temperatures (100{degree sign}C for 1 hour). This stability is attributed to a temperature-reversible transition from a dimer to a monomer. The authors suggest several potential applications, such as complementing heat sterilization processes or being used in animal feed premixes that undergo high-temperature pelleting, which I agree with. 

We appreciate the reviewer’s valuable comments and suggestions.

Strengths: 

The claims are well-supported by relevant and complementary assays, as well as extensive bioinformatic analyses. 

We appreciate the reviewer’s valuable comments and suggestions.

Weaknesses: 

There are numerous statements in the introduction and discussion sections that I currently do not agree with and consider need to be addressed. Therefore, I recommend major revisions. 

Based on your valuable comments and suggestions, we have revised relevant introduction and discussion sections (pages 3-4, lines 82-101; page 21, lines 480-483).

Major comments: 

Introduction and Discussion: 

The introduction and the discussion are currently too general and not focused. Furthermore, there are some key concepts that are missing and are important for the reader to have an overview of the current state-of-the-art regarding endolysins that target gram-negatives. Specifically, the concepts of 'Artilysins', 'Innolysins', and 'Lysocins' are not introduced. Besides this, the authors do not mention other high-throughput mining or engineering strategies for endolysins, such as e.g. the VersaTile platform, which was initially developed by Hans Gerstmans et al. for one of the targeted pathogens in this manuscript (i.e., Acinetobacter baumannii). Recent works by Niels Vander Elst et al. have demonstrated that this VersaTile platform can be used to high-throughput screen and hit-to-lead select endolysins in the magnitude tens of thousands. Lastly, Roberto Vázquez et al. have recently demonstrated with bio-informatic analyses that approximately 30% of Gram-negative endolysin entries have AMP-like regions (hydrophobic short sequences), and that these entries are interesting candidates for further wet lab testing due to their outer membrane penetrating capacities. Therefore, I fully disagree with the statement being made in the introduction that endolysin strategies to target Gram-negatives are 'in its infancy' and I urge the authors to provide a new introduction that properly gives an overview of the Gram-negative endolysin field.   

We thank the reviewer for the valuable suggestions. A new paragraph has been added to the revised manuscript to reflect the concepts and strategies for lysin engineering and discovery against Gram-negative bacteria (pages 3-4, lines 82-101). 

Results: 

It should be mentioned that the halo assay is a qualitative assay for activity testing. I personally do not like that the size of the halos is used to discriminate in endolysin activity. In this reviewer's opinion, the size of the halo is highly dependent on (i) the molecular size of the endolysin as smaller proteins can diffuse further in the agar, and (ii) the affinity of the CBD subdomain of the endolysin for the bacterial peptidoglycan. It should also be said that in the halo assay, there is a long contact time between the endolysin and the bacteria that are statically embedded in the agar, which can result in false positive results. How did the authors mitigate this? 

We quite agree with the reviewer that the halo assay is only a qualitative method for activity testing and may be perturbed by multiple parameters (DOI:

10.3390/antibiotics9090621). In our study, the halo assay was used only as a preliminary method to rapidly distinguish the activities of multiple candidates, and then the candidates with high antibacterial activities were further characterized through a series of in vitro and in vivo assays in this work.

Testing should have been done at equimolar concentrations. If the authors decided to e.g. test 50 µg/mL for each protein, how was this then compensated for differences in molecular weight? For example, if PHAb10 and PHAb11 have smaller molecular sizes than PHAb7, 8, and 9, there is more protein present in 50 µg/mL for the first two compared to the others, and this would explain the higher decrease in bacterial killing (and possibly the larger halos). 

We thank the reviewer for his valuable suggestions and concerns. We agree with the reviewer that when we need to know exactly how much times more active an enzyme is than the another, we should directly compare the performance of the two enzymes at equimolar concentrations. In our previous work, we followed this rule to distinguish novel chimeric lysins from their parental lysins or their variants (DOI: 10.1128/AAC.00311-20; DOI: 10.1128/AAC.01610-19; DOI: 10.1128/AAC.02043-18). In the present work, our initial goal of testing was to reflect the robustness and efficiency of screening strategy initiated by lysinderived antimicrobial peptides. With this in mind, we therefore did not spend more effort to compare the activities of these candidates in detail but continued to clarify their host range and thermo-tolerance mechanisms, and then continued to examine their performance in infection models. Nonetheless, in future work, we will definitely follow your suggestions when it is necessary to quantify the differences between these candidates.  

Reviewer #2 (Public Review): 

Summary: 

The study explores a new strategy of lysin-derived antimicrobial peptide-primed screening to find peptidoglycan hydrolases from bacterial proteomes. Using this strategy authors identified five peptidoglycan hydrolases from A. baumannii. They further tested their antimicrobial activities on various Gram-positive and Gram-negative pathogens.

We appreciate the reviewer’s valuable comments.

Strengths: 

Overall, the study is good and adds new members to the peptidoglycan hydrolases family. The authors also show that these lysins have bactericidal activities against both Gram-positive and Gram-negative bacteria. The crystal structure data is good, and reveals different thermostablility to the peptidoglycan hydrolases. Structural data also reveals that PhAb10 and PHAb11 form thermostable dimers and data is corroborated by generating variant protein defective in supporting intermolecular bond pairs. The mice bacterial infection shows promise for the use of these hydrolases as antimicrobial agents. 

We appreciate the reviewer’s valuable comments and suggestions.

Weaknesses: 

While the authors have employed various mechanisms to justify their findings, some aspects are still unclear. Only CFU has been used to test bactericidal activity. This should also be corroborated by live/dead assay. Moreover, SEM or TEM analysis would reveal the effect of these peptidoglycan hydrolases on Gram-negative /Gram-positive cell envelopes. The authors claim that these hydrolases are similar to T4 lysozyme, but they have not correlated their findings with already published findings on T4 lysozyme. T4 lysozyme has a C-terminal amphipathic helix with antimicrobial properties. Moreover, heat, denatured lysozyme also shows enhanced bactericidal activity due to the formation of hydrophobic dimeric forms, which are inserted in the membrane. Authors also observe that heat-denatured PHAb10 and PHAb11 have bactericidal activity but no enzymatic activity. These findings should be corroborated by studying the effect of these holoenzymes/ truncated peptides on bacterial cell membranes. Also, a quantitative peptidoglycan cleavage assay should be performed in addition to the halo assay. Including these details would make the work more comprehensive. 

We thank the reviewer for his valuable suggestions and concerns. We agree with the reviewer that employing more methods and techniques such as SEM, TEM, live/dead imaging, and GC-MS will provide a deeper understanding of how these peptidoglycan hydrolases interact with the bacterial envelopes and peptidoglycan bones, which will definitely make our study more comprehensive. The principal idea of this study is, however, to test the robustness and effectiveness of the screening strategy triggered by lysin-derived antimicrobial peptide in discovering new peptidoglycan hydrolases. Therefore, we did not put more efforts in charactering the interactions of these peptidoglycan hydrolases with the bacterial envelopes/membranes in multiple assays; instead, we continued to elucidate their host range and thermo-tolerance mechanisms and then continued to examine their performance in infection models. 

We are also very grateful to the reviewers for their suggestions to correlate our results to published findings on lysozymes. Based on these suggestions, we have included an extensive discussion in the Discussion section of the revised manuscript (page 22, lines 502-514).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Abstract and title. 

In my opinion, the current title does not fully cover the work that is presented in the manuscript. 

According to your valuable comment, we have revised the title to “Dimer-monomer transition defines a hyper-thermostable peptidoglycan hydrolase mined from bacterial proteome by lysin-derived antimicrobial peptide-primed screening”.

Please remove the word 'novel' from the title, as well as elsewhere in the manuscript. As it is true that PHAb10 and PHAb11 are new, they are not novel. There are many reports that have been published on endolysins with activity against Gram-negatives, and sometimes even also Gram-positives. 

We have changed the description of PHAb10 and PHAb11 to avoid using the word “novel”, but alternatively, using “new” or “active” in the title and throughout the text in the revised manuscript.

Additional information for the Introduction section in the Public Review: 

DOI: 10.1128/AAC.00285-16  

DOI: 10.1038/s41598-020-68983-3 

DOI: 10.1128/AAC.00342-19  

DOI: 10.1126/sciadv.aaz1136   

DOI: 10.1111/1751-7915.14339 

DOI: 10.1128/JVI.00321-21  G-

We appreciate the reviewer for these selected references and have cited almost all of them in a new paragraph in the Introduction section of the revised manuscript (pages 3-4, lines 82-101).

Minor Comments: 

Line 30. For a lay person it is not clear what is meant by 'unique mechanism of action.' 

These has been replaced by “direct peptidoglycan degradation activity” in the revised manuscript (page 2, lines 30-31).

Line 60 & 62. Please merge these sentences into one as they have the same meaning.

We have deleted one of the sentences based on your suggestion.

Line 67. Replace 'also' with 'simultaneously'. 

Revised as suggested (page 3, line 66).

Line 74. 'Modern clinical practice' should specifically refer to infectious diseases in humans. 

Revised as suggested (page 3, line 73).

Line 76 to 105. There is too much information that is not focused. This section should be rewritten so that it is in line with the focus of the presented work. I would remove this section and replace it with a new section as proposed in my major comments. 

Based on your suggestion, we deleted this section and prepared a new paragraph in the revised manuscript (pages 3-4, lines 82-101).

Line 113. I strongly disagree with the wording 'in its infancy'. Please see my major comment. 

We have rewritten the paragraph as “However, compared with the current progress in the clinical translation of lysins against Gram-positive bacteria, the discovery of lysins against Gram-negative bacteria that meet the needs described in the WHO priority pathogen list is still urgently needed.” according to your valuable comments in the revised manuscript (page 4, lines 98-101).

Line 116. Remove 'on'. 

Revised as suggested (page 4, line 104).

Results. 

Additional information for the Results section in the Public Review: 

DOI: 10.3390/antibiotics9090621

We thank the reviewer for this valuable reference, which has been cited in the Results section and Methods sections of the revised manuscript (page 7, line 159; page 25, line 605).

Minor comments: 

Line 135. Replace 'would' with 'could'.

Revised as suggested (page 5, line 124).

Line 150. Why was this naming decided to go from 11 -> 7, whereas in Figure 1a the clades go from I to V? This way of naming is not clear to me. 

Thank you for the reviewer's question. There are two numbering systems here: 1-11 is the numbering of peptidoglycan hydrolases mined from different bacterial proteomes by lysin-derived peptide primer screening strategy, and the characterization of candidates mined from the proteome of A. baumannii are 7 to 11 (characterization candidates numbered 1 to 6 are from other bacterial proteomes). Whereas the cladistic analysis of all potential candidates in the A. baumannii proteome is regularly labelled by clade I to V. 

Line 250. Replace 'casts doubt' with 'questions'. 

Revised as suggested (page 10, line 244).

Line 252 to 257. I would encourage the authors to mention if there is any homology in between the peptides on the one hand, and in between the lysozyme catalytic domains on the other hand.

This information has been added to the revised manuscript (page 10, lines 249-251).

Line 266. The following sentence should be reworded: 'However, rare lytic activity was observed in P11-NP, suggesting that a potential role for it in functions other than bactericidal

activity.' 

In the revised manuscript (page 11, lines 261-262), the sentence has been revised as “However, rare lytic activity was observed in P11-NP, suggesting that its function remains to be established”.

Line 276. Replace 'asked' with 'questioned'.

Revised as suggested (page 11, line 270).

From 302 onwards. Why was it chosen to solve the crystal structure of PHAb8, and not PHAb7 and 9? This should be briefly mentioned. 

Initially we tried to decipher the structures of all five enzymes, but we finally obtained the crystal structures of only three enzymes, PHAb8, PHAb10, and PHAb11 by Xray crystallography. This reason has been added in the revised manuscript (page 13, lines 300301).

Line 437. Replace 'the burn wound model' with 'a burn wound model'. 

Revised as suggested (page 19, line 433).

Line 445. Replace 'the mouse abscess model' with 'a mouse abscess model'. 

Revised as suggested (page 19, line 441).

Line 449 to 451. Given that the mice received 5 doses of minocycline and no difference was observed with the group that received tris buffer, was it tested if the Acinetobacter baumannii 3437 isolates became resistant against minocycline during the experiment? 

We appreciate the Reviewer for his valuable concern. In our study, we did not explore in detail the reasons why minocycline was ineffective. But we strongly agree with the reviewer that drug resistance may be one of the reasons.

Discussion. 

Minor comments. 

Line 479. Delete this sentence: 'Policy makers, scientists, enterprisers, and investigators have worked together for decades to exploit the 'trojan horse' globally, but new options for treating antimicrobial resistance in the clinic remain to be seen'. 

Revised as suggested.

Line 483. Reformulate as follows: 'unique mechanism of action, potent bactericidal activity, low risks of drug resistance, and ongoing clinical trials targeting Gram-positive bacteria.' To my knowledge, all these clinical trials target S. aureus, but I might be wrong. 

Revised as suggested (page 21, lines 476-478).

Line 486. 'However, for Gram-negative bacteria, the effects of phage-derived lysins were often hampered by their outer membranes, which requires more strategies to overcome this barrier.' After this sentence, the concepts of Artilysins, Innolysins, and Lysocins should be mentioned, in addition to the introduction. These are important engineering strategies and the reader should be informed that your strategy is thus not the only existent one. 

Revised as suggested (page 21, lines 480-482).

Line 491. Please, again refer to the work of Roberto Vázquez et al., who has done very similar work to your work presented. DOI: 10.1128/JVI.00321-21 

We have cited this interesting work in the Introduction section and Discussion section of the revised manuscript (page 4, line 106; page 21, lines 482-483).

Line 499. Reformulate: 'Gram-positive bacteria are primarily killed through the action of the antimicrobial peptides only'. 

According to your suggestion, it was changed to “while Gram-positive bacteria are killed mainly through the action of the intrinsic antimicrobial peptides” in the revised manuscript (pages 21-22, lines 497-498).

Line 500. Delete this sentence, as this is already mentioned in the results and too detailed:

'Interestingly, we noted a difference in the killing of Gram-positive bacteria by PHAb10 and PHAb11, which may be due to the fact that P11-CP had one more basic amino acid than P10CP, so it had stronger bactericidal activity.' 

Revised as suggested.

Line 503. This statement doesn't make sense because you cannot directly compare ug/mL between endolysins, you must compare equimolar concentrations. Furthermore, testing conditions between studies were different, thus making this claim unjustified. 

These statements have been deleted in the revised manuscript.

Line 524. Please delete:' To our knowledge, this is the first time that an enzyme had been found to adapt to ambient temperature by altering its dimerization state.' 

Revised as suggested.

Figures. 

Figure 1a. Please choose a different name for 'dry job' and 'wet job'. 

Following your suggestion, they have been specified as “In silico analysis” and “Experimental verification” in the revised Figure 1a. 

Figure 6. I suggest moving Figure 6e to the supplementary materials and reorganizing Figure 6 with only panels a to d. 

Revised as suggested.

Materials and Methods, References, and Supplementary Materials.  No comments. 

Reviewer #2 (Recommendations For The Authors): 

Most figure labelings are very small and difficult to read. 

All figures in the revised manuscript have been replaced with high-resolution figures, which hopefully will make these labels easier to follow.

The authors should include a data availability statement in the manuscript.

Revised as suggested (page 28, lines 704-706).

eLife assessment

This study presents useful findings on the efficacy and mechanism of linalool protection against Saprolegnia parasitica oomycetes in the grass carp model. The evidence is incomplete since the claims are partially justified, thus there is a need for more experimental data and more rigorous statistical data analysis . Revisions according to the recommendations will improve the work, making it of interest to scientists within the fields of aquaculture, ichthyology, microbiology, and drug discovery.

Reviewer #1 (Public review):

Summary:

The work seeks to investigate the efficacy of linalool as a natural alternative for combating Saprolegnia parasitica infections, which would provide great benefit to aquaculture. This paper shows the effect of linalool in vitro using a variety of techniques including changes in S. parasitica membrane integrity following linalool exposure and alterations in cell metabolism and ribosome function. Additionally, this work goes on to show that prophylactic and concurrent treatment of linalool at the time of S. parasitica infection can improve survival and tissue damage in vivo in their grass carp infection model. The conclusions of the paper are partially supported by the data, cleaning up, clarifying, and elaborating on some aspects of this work is necessary.

(1) Adding microscopy of the untreated group to compare Figure 2A with would further strengthen the findings here.

(2) Quantification of immune infiltration and histological scoring of kidney, liver, and spleen in the various treatment groups would increase the impact of Figure 4.

(3) The data in Figure 6 I is not sufficiently convincing as being significant.

(4) Comparisons of the global transcriptomic analysis of the untreated group to the PC, LP, and LT groups would strengthen the author's claims about the immunological and transcriptomic changes caused by linalool and provide a true baseline.

Reviewer #2 (Public review):

Summary:

In this study, the authors aimed to delineate the antimicrobial activity of linalool and tried to investigate the mode of action of linalool against S. parasitica infection. One of the main focuses of this work was to identify the in vitro and in vivo mechanisms associated with the protective role of linalool against S. parasitica infection.

Strengths:

(1) The authors have used a variety of techniques to prove their hypothesis.

(2) An adequate number of replicates were used in their studies.

(3) Their findings showed a protective role of linalool against oomycetes and makes it an attractive future antibiotic in the aquaculture industry.

Weaknesses:

There are several weaknesses in this manuscript.

(1) The authors have taken for granted that the readers already know the experiments/assays used in the manuscript. There was not enough explanation for the figures as well as figure legends.

(2) The authors missed adding the serial numbers to the references.

(3) The introduction section does not provide adequate rationale for their work, rather it is focused more on the assays done.

(4) Full forms are missing in many places (both in the text and figure legends), also the resolution of the figures is not good. In some figures, the font size is too small.

(5) There is much mislabeling of the figure panels in the main text. A detailed explanation of why and how they did the experiments and how the results were interpreted is missing.

(6) There is not enough experimental data to support their hypothesis on the mechanism of action of linalool. Most of the data comes from pathway analysis, and experimental validation is missing.

Overall, the conclusions drawn by the authors are partially justified by the data. Importantly, this paper has discovered the novelty of the compound linalool as a potent antimicrobial agent and might open up future possibilities to use this compound in the aquaculture industry.

Author response:

Reviewer #1:

(1) Adding microscopy of the untreated group to compare Figure 2A with would further strengthen the findings here.

Thank you for your comments on our manuscript. We will carefully revise this part. Actually, we used a time-lapse method to capture images at 0 minute before any drugs were added. We will change '0 min' to 'untreated,' which will further strengthen our findings.

(2) Quantification of immune infiltration and histological scoring of kidney, liver, and spleen in the various treatment groups would increase the impact of Figure 4.

Thank you for your comments on our manuscript. To further strengthen Figure 4, we will use quantification of immune infiltration and histological scoring of the kidney, liver, and spleen in different groups. Additionally, we will use ImageJ software for molecular immunohistochemistry and determine the ratio of normal to abnormal cells, providing more comprehensive insights into the effects of the treatments.

(3) The data in Figure 6 I is not sufficiently convincing as being significant.

Thank you for your comments on our manuscript. Previous researches have shown that antibiotics and other drugs can cause alterations in gut microbiota. Therefore, we plan to study the effects of linalool on gut microbiota. The results of this part were mostly built on gut microbiota sequencing and correlation analysis, we have tried several times to isolate vital microbes from the gut, but this is a very challenging work and the results were not good. Thus, in this study, we just predicted the effects of linalool on gut microbiota. In the future, we will continue to delve into interesting aspects of how linalool affects gut microbiota.

(4) Comparisons of the global transcriptomic analysis of the untreated group to the PC, LP, and LT groups would strengthen the author's claims about the immunological and transcriptomic changes caused by linalool and provide a true baseline.

Thank you for your comments on our manuscript. We will compare the global transcriptomic analysis of the untreated group with the PC, LP, and LT groups to strengthen the claims about the immunological and transcriptomic changes induced by linalool, thereby providing a true baseline.

Reviewer #2:

(1) The authors have taken for granted that the readers already know the experiments/assays used in the manuscript. There was not enough explanation for the figures as well as figure legends.

Thank you for your comments on our manuscript. We will provide more detailed explanations of the experiments and assays used in the manuscript, as well as enhance the descriptions in the figure legends, to ensure that readers have a clear understanding of the figures and context.

(2) The authors missed adding the serial numbers to the references.

Thank you for your comments on our manuscript. We will add serial numbers to the references to ensure proper citation and improve the clarity of our manuscript.

(3) The introduction section does not provide adequate rationale for their work, rather it is focused more on the assays done.

Thank you for your comments on our manuscript. We will add a section to the introduction that provides a rationale for our work, specifically focusing on the impact of plant extract on immunoregulation.

(4) Full forms are missing in many places (both in the text and figure legends), also the resolution of the figures is not good. In some figures, the font size is too small.

Thank you for your comments on our manuscript. We will ensure that all abbreviations are expanded where necessary, both in the text and figure legends. Additionally, we will improve the resolution of the figures and increase the font size where needed to enhance clarity.

(5) There is much mislabeling of the figure panels in the main text. A detailed explanation of why and how they did the experiments and how the results were interpreted is missing.

Thank you for your comments on our manuscript. We will improve the labeling of the figure panels, provide detailed explanations of the experimental methods, including their rationale and interpretation, and clarify the connections between the methods.

(6) There is not enough experimental data to support their hypothesis on the mechanism of action of linalool. Most of the data comes from pathway analysis, and experimental validation is missing.

Thank you for your comments on our manuscript. We have tried our best to link transcriptomic data, pathway analysis, experimental validation. We carried out many experiments to substantiate the changes inferred from the transcriptomic data as SEM, TEM, CLSM, molecular docking, RT-qPCR, histopathological examinations. The detailed information is listed as follows. (1) As shown in Figure 2, we combined the transcriptomic data related to membrane and organelle with SEM, TEM, and CLSM images. After deep analysis of these data and observation together, we illustrated that cell membrane may be a potential target for linalool. (2) As shown in Figure 3, we carried out molecular docking to explore the specific binding protein of linalool with ribosome which were screen out as potential target of linalool by transcriptomic data. (3) As shown in Figure 5, transcriptomic data illustrated that linalool enhanced the host complement and coagulation system. To substantiate these changes, we carried out RT-qPCR to detect those important immune-related gene expressions, and found that RT-qPCR analysis results were consistent with the expression trend of transcriptome analysis genes. (4) As shown in Figure 4 and 5, transcriptomics data revealed that linalool promoted wound healing tissue repair, and phagocytosis (Figure. 5E). To ensure these, we carried out histopathological examinations, and found that linalool alleviated tissue damage caused by S. parasitica infection on the dorsal surface of grass carp and enhancing the healing capacity (Figure. 4G). But we know the antimicrobial mechanism of linalool need further investigation, we will conduct more experiments to explore the antimicrobial mechanism of action of linalool in the future.

eLife assessment

This study presents a useful finding on the interplay of CCL5 and miR-324-5p during ischemic stroke injury. Despite its importance, the evidence supporting the claims of the authors is incomplete. In particular, the lack of methodological information, inappropriate statistical testing, a flawed culture system, and the temporal mismatch in the expression of CCL5 and miR-324-5p following stroke have hindered further evaluation of the claims. The work will be of interest to neuroscientists working on brain injury such as stroke.

Reviewer #1 (Public review):

Summary:

Here, the authors attempt to show that CCL5 is increased after stroke, possibly due to decreased miR-324, and that this is a modifiable system to decrease stroke damage. By bidirectionally manipulating CCL5 levels through direct injection of CCL5; a CCL5 blocking antibody; miR324; miR324 antagomir; or CCR5-blocking Maraviroc, they broadly show improvement with lower CCL5 levels. This includes infarct size, behavioral analysis, and immunohistochemical analysis of astrocytes, microglia, and neurons. They further try to mechanistically tie miR324 and CCL5 in astrocytes specifically to stroke-induced changes using a neuronal/astrocytic coculture system. They argue that decreasing CCL5 leads to increased ERK and CREB phosphorylation as a potential neuroprotective mechanism. CCL5 is one potential ligand for CCR5, and recent work identified CCR5 as a targetable mechanism by clinically-approved drug Maraviroc to enhance stroke recovery. Particularly given the high level of interest in CCR5 in stroke recovery, the focus on CCL5 - one of CCR5's potential ligands - and its miR regulation is an exciting expansion of this area of stroke biology.

Strengths:

The authors' findings that decreasing CCL5 acutely after stroke shows behavioral improvement appear robust. This broadly replicates work from other groups, although the finding that miR324 manipulation can phenocopy direct CCL5 manipulation is novel and intriguing. However, many of their other claims are difficult to evaluate based on a combination of missing methodological information, inappropriate statistical testing, and a flawed culture system.

Weaknesses:

Broadly speaking, the manuscript takes a zoomed-out view of what is fundamentally highly localized biology.

(1) miRNA-based regulation, by definition, has to include miR and mRNA in the same cell type; as the authors note, CCL5 is expressed in many cells. It is therefore impossible to propose any interaction on the basis of the tissue-level changes described; any evidence of in vivo cell-type specificity would dramatically improve the claims.

(2) The authors treat an extensive area of ipsilesional cortex uniformly as "IP". Astrocytic and microglial responses to localized injuries such as stroke are highly location-dependent and undoubtedly change dramatically within this area. The presented data cannot be interpreted without confirmation that these were taken at identical distances from the injury, and what that distance was. These do not appear to be adjacent to the injury, where the responses would presumably be the most informative. Similarly, it is difficult to interpret the neuronal Sholl and spine data without more information on where within the large IP region these neurons were found.

The authors attempt to narrow in on cell-type specificity via culture. However, astrocytes are notoriously prone to a dramatic change in culture and require careful methods (immunopanning; see eg doi: 10.1016/j.neuron.2011.07.022) to maintain much resemblance to their in vivo counterpart. It is difficult to conclude much about the role of astrocytes in the CCL5 pathway based on the use of this shaking-based culture system, particularly in the absence of cell-type specific validation in vivo.

There is missing methodological information, including infarct size measurements, TUNEL staining, and statistical testing. The TTC figures look very odd, like a collection of overlapping stars have been placed on the images rather than the natural relatively smooth infarct edges one would expect. It is unclear if the infarct volume measurements accounted for edema, as is standard; there is no description of the protocol used for quantification. It is also unclear if the infarct volume measurement comparisons were also done with t-tests vs ANOVA, as the statistical test used is not listed in the figure legends. In numerous cases where statistical testing is listed, repeated t-tests between subgroups are used vs the more appropriate ANOVA (assuming normality; nonparametric testing as appropriate), making it difficult to have confidence in the results.

Reviewer #2 (Public review):

The authors presented evidence from various in vivo and in vitro experiments demonstrating the mutual interaction between CCL5 and astrocytic miR-342-5p in the ipsilateral core of cerebral ischemia. However, miR-342-5p was downregulated only late after MCAO (D3-7). Additionally, this downregulation was observed not only in the ipsilateral core but also in the ipsilateral penumbra and contralateral sides. Therefore, it is not convincing that the upregulation of CCL5 in the ipsilateral core at later time points (D3 and D7) is attributable to the decreased expression of miR-342-5p. In particular, infarct injury was already evident within a short time period (say 24 h) following MCAO.

(1) The temporal and spatial expression patterns of miR-324-5p do not match those of CCL-5, especially at D1 and D3 (see Figure 1C, 1D). Despite the inverse relationship between miR-324-5p and CCL-5 expression at D7 after MCAO, what was the purpose of administering miR-324-5p agomir (or antagomir) at D1 post-MCAO? If the connection cannot be clearly established, the conclusion reached at the end will be difficult to accept.

(2) Would administering miR-342-5p or anti-CCL5 at later time points (e.g., after D3) reduce infarct size or improve functional recovery? If this is not the case, the effect of CCL5 on neuronal cell damage (infarct size formation) must occur within a very short time after MCAO. Additionally, if the increased CCL5 expression is due to the downregulation of miR-342-5p, its impact would likely be less significant.

(3) While the study offers valuable insights into the roles of CCL5 and its connection with the regulation of miR-342-5p (though this connection is somewhat weak), it is recommended that the authors explore potential translational applications of these findings.

Overall, given the experimental designs and results, it is difficult to support the conclusions drawn in the manuscript.

eLife assessment

This study provides an important insight into the mechanisms of cooperation between Hsp70 and its cochaperones during reactivation of aggregated proteins. Based on convincing evidence, the authors demonstrate that the co-chaperone Hsp110 boosts disaggregation activity by enhancing Hsp70 recruitment to protein aggregates. This work is of broad interest to biochemists and cell biologists working in the protein homeostasis field.

Reviewer #1 (Public review):

Summary:

The manuscript by Sztangierska et al explores how the Hsp70 chaperone together with its JDP-NEF cofactors and Hsp104 disentangle aggregated proteins. Specifically, the study provides mechanistic findings that explain what role the NEF class Hsp110 has in protein disaggregation. The results explain several previous observations related to Hsp110 in protein disaggregation. Importantly, the study provides compelling evidence that Hsp110 acts early in the disaggregation process.

Strengths:

(1) This is a very well performed study with multiple in vitro experiments that provide convincing support for the claims.

(2) An important finding is that the study places Hsp110 function early in the disaggregation process.

(3) The study has an important value in that it picks up on a number of observations in the field that have not been explored or directly tested by experiment. The presented results settle questions and controversy regarding Hsp110 function in disaggregation.

Weaknesses:

(1) While the key finding of this manuscript is that it places Hsp110 early in the disaggregation process, the other findings are advancing the field less.

Reviewer #2 (Public review):

Sztangierska et al. have investigated the impact of the nucleotide exchange (NEF) factor Hsp110 on the Hsp70-dependent dissolution of amorphous aggregates in the presence of representative members of two classes of J-domain protein.<br /> The authors find that the nucleotide exchange factor of the Hsp110 family, sse1, stimulates the disaggregation activity of yeast Hsp70, ssa1, in particular in the presence of the J-domain protein sis1. Linking chaperone-substrate interactions as determined by biolayer interferometry (BLI) to activity assays, they show that sse1 facilitates the loading of more ssa1 onto the aggregate substrate and propose that this is due to active remodelling of the protein aggregate which exposes more chaperone binding sites and thus facilitates reactivation. This study highlights two important facets of Hsp70 biology: different Hsp70 functions rely on the functional cooperation of specific co-chaperone combinations and the stoichiometry of the different players of the Hsp70 system is an important parameter in tuning Hsp70 chaperone activity.

Strengths:

The manuscript presents a systematic analysis of the functional cooperation of sse1 with a class B J-domain protein sis1 in the disaggregation of two different model aggregate substrates, allowing the authors to draw more general conclusions about Hsp70 disaggregation activity.

The authors can pinpoint the role of sse1 to the initial remodeling of aggregates, rather than the later stages of refolding, highlighting the functional specificity of Hsp70 co-chaperones.

They demonstrate the competitive nature of binding to ssa1 between sse1 and sis1 which can explain the poisoning of Hsp70 chaperone activities observed at high NEF concentrations.

Weaknesses:

While structural requirements have been identified that allow sse1, in cooperation with sis1, to facilitates the loading of Hsp70 on the amorphous aggregate substrate, how this is achieved on a mechanistic level remains an open question.

Reviewer #3 (Public review):

Summary:

The authors studied the function of Hsp110 co-chaperones (e.g. yeast Sse1) in Hsp70-dependent protein disaggregation reactions. The study builds on former work by the authors (Wyszkowski et al., 2021, PNAS), analyzing the binding of Hsp70 and J-domain protein (JDP) cochaperones to protein aggregates using bio-layer interferometry (BLI). It was shown before by other groups that Hsp110 enhances Hsp70 disaggregation activity. The mechanism of Hsp110-stimulated disaggregation activity, however, remained poorly defined. Here, the authors show that yeast Hsp110 increases Hsp70 recruitment to the surface of protein aggregates. The effect is largely dependent on J-domain protein (JDP) identity and particularly pronounced for class B JDPs (e.g. yeast Sis1), which are also more effective in disaggregation reactions. The authors also confirm former results, showing inhibition by increased Hsp110 levels and provide novel evidence that the inhibitory effect is caused by competition between Hsp110 and JDPs for Hsp70 binding.

Strengths:

The work represents a very thoroughly executed study, which provides novel insights into the mechanism of Hsp70-mediated protein disaggregation. Key findings established for yeast chaperones are also documented for human counterparts. The observation that Hsp110 might displace JDPs from Hsp70 during the disaggregation reaction is very appealing. It will now become important to validate this initial finding and dissect how it propels the disaggregation reaction.

Weaknesses:

How exactly the interplay between JDPs and Hsp110 orchestrates protein disaggregation remains largely speculative and further analysis is required for a deeper mechanistic understanding.

Author response:

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

Reviewer #1 (Recommendations For The Authors): 

- The title may not reflect the key finding of the paper. It is well established in the field that the disaggregation process is sensitive to perturbations of the levels of the disaggregating factors.

We have changed the title to better reflect the major finding of the work, the importance of the NEF during the initiation of disaggregation. The new title is: Early Steps of Protein Disaggregation by Hsp70 Chaperone and Class B J-Domain Proteins are Shaped by Hsp110.

- Abstract:

Please note that the phrases "stimulation is much limited with class A JDPs", "limited destabilization of the chaperone complex improves disaggregation", and "tuned proportion between the co-chaperones" are hard to understand. Only after having read the manuscript are the meanings of these phrases accessible.

The phrases in the abstract were changed (page 1, lines 10-14).

- The subheading "Sse1 improves aggregate modification by Hsp70" on p. 7 is unclear. What is measured is a decrease in aggregate size dependent on Hsp70-JDP as well as Sse1.

The subheading was changed to include more precise information, into “Sse1 leads to Hsp70-depenent reduction of aggregate size”.

- The subheading "Biphasic effects of Sse1 on the Hsp70 disaggregation activity" does not describe the finding clearly; "Biphasic effects" is a term that is hard to understand.

To avoid phrases that can be understood in many ways, we have changed the subheading into “Hormetic effects of Sse1 in Hsp70 disaggregation activity”

- p.5, last line. Hsp110 typo The typos have been corrected.

Reviewer #2 (Recommendations For The Authors):

(1) The article emphasises multiple times the importance of stoichiometry between the (co-)chaperones. Most figures would benefit from an indication of the used stoichiometry (or all absolute concentrations) to support the points made about the stoichiometry, especially the figures showing titrations of Sse1, Sse1-2, and Sis1 (Fig. 3D, 3E, 4A-C, S2B, S5F, S6A-E).

The information of protein concentrations has been included in all figure captions.

(2) The manuscript includes a summary model. While this model is a plausible hypothesis of the mechanism of disaggregation by Hsp70, in particular when viewed with previous data (Wyszkowski et al., 2021), it focuses rather heavily on the potential remodeling of clients by Hsp70, which is not the primary focus of the data presented in this manuscript. More emphasis could be put on the JDP class/ functional specificity observed.

The model has been changed according to the Reviewer’s comments to better reflect the findings presented in the manuscript (Figure 5).

(3) The methods section is very brief. I recommend including additional details about reaction conditions (temperature, buffer compositions, protein concentrations) even when previously reported elsewhere to improve the readability of the manuscript. Details regarding the DLS experiments performed are missing.

More detailed information on the experimental conditions has been added to the Methods section, as well as to figure legends.

(4) Many experiments incorporate BLI to assess the effect of NEFs on the binding of the Hsp70 and JDP to aggregates. Although appropriate controls are included (no ATP, Hsp70, and JDP only), a control with only Hsp70 and the NEF would be useful to determine to which extent the NEF itself alters the thickness of the (Hsp70-bound) aggregate biolayer.

The suggested controls were added (Figure 1—figure supplement 1 G) and discussed in the manuscript (page 5, lines 23-24).

Reviewer #3 (Recommendations For The Authors):

- The refolding assay makes use of Luciferase denatured in 5 M GdnHCl. These conditions lead to a spontaneous refolding yield of 20% (Figure 3C), which is very high and limits conclusions on the effect of Hsp110 but also JDPs on the refolding process. Typically this assay uses 6 M GdnHCl for Luciferase denaturation and under these conditions, spontaneous refolding of Luciferase is hardly observed (e.g. Laufen et al. PNAS 1999). The authors are therefore asked to repeat key experiments using altered (6M) GdnHCl concentrations.

We based our experiments assessing luciferase refolding on the publication by Imamoglu et al. (2020), in which the authors, using 5 M GdnHCl for luciferase denaturation, demonstrated that spontaneous and chaperone-assisted luciferase refolding strongly depends on luciferase concentration. In this work, a similar degree of luciferase refolding was reported for the same final luciferase concentration (100 nM) as we used in our experiments (Figure 1—figure supplement 1D). As an additional control, we compared the effects of 5 M and 6 M of GdnHCl during denaturation on luciferase refolding under the same conditions (100 nM, 25 °C, 2 h) and we observed no significant differences (Author response image 1).

Author response image 1.

Chaperone-assisted folding of luciferase after denaturation at 5 M or 6 M GdnHCl. Luciferase was denatured in 5 M or 6 M GdnHCl according to the protocol in the Materials and Methods section. Luminescence was monitored alone or after incubation with Luminescence was monitored alone or after incubation with Ssa1-Sis1 or Ssa1-Ydj1. Chaperones were used at 1 µM concentration. Luciferase activity was measured after 2 hours and normalized to the activity of the native protein. Error bars indicate SD from three repeats.

- Figure 1B: The authors are asked to provide binding curves for Ssa1/Sse1 (no Sis1) and Sis1/Sse1 (no Ssa1) as controls. Particularly the latter combination is required as direct cooperation between Hsp110 and JDPs has been suggested in the literature (Mattoo et al., JBC 2013).

We performed the suggested BLI experiment, and the results are presented in the new Figure 1—figure supplement 1 G (page 5, lines 23-24).

- Figure 1B (and other figure parts showing BLI data): it is unclear how often the BLI experiments have been performed. This should be stated in the figure legend. Can the authors add SDs to the respective curves?

We added detailed information about the number of replicates to the figure legends. SD bars were added to the BLI results shown in Figures1-4, apart from the results of titrations, for which, for the sake of clarity, the three replicates are represented in the plots on the right (Figure 3D). In the case of less than 3 repeats of the results presented in the Supplementary Figures, the remaining repeats are added to the provided Source Data file, information about which has been added to the captions of the respective figures. 

- The observation that Hsp110 can interrupt Hsp70 interaction with JDPs is intriguing. Do the authors envision JDP displacement from the aggregate? If so this could be shown in BLI experiments by monitoring the release of fluorescently labeled Sis1 (similar to labeled Ssa1, Fig. S3C). Or will the released JDP immediately rebind to another binding site on the aggregate? The authors should at least discuss the diverse scenarios as they are relevant to the mechanism of protein disaggregation.

The proposed experiment is challenging due to the transient nature of Sis1 binding to aggregate and high background observed with the method using the fluorescently labelled proteins. The aspect of chaperone’s re-binding after their release by Hsp110 proposed by the reviewer has been introduced into the Discussion section (pages 12/13, lines 25-4). We speculate that Hsp110 might release an Hsp70 molecule as well as a JDP molecule that had been bound to the aggregate through Hsp70 (Figure 5).  

- Figure 2B: Ssa1/Sis1/Sse1 strongly decreases the size of Luciferase-GFP aggregates. Yet this activity only allows for limited refolding of aggregated Luciferase and the reaction stays largely dependent on Hsp104. How do the authors envision the role of the hexameric disaggregase in this process? Does it act exclusively on small-sized aggregates after Hsp110-dependent fragmentation?

A question of the Hsp104 activity with the Hsp70-processed aggregates is indeed intriguing and we agree that it should have been discussed more thoroughly. We added to the manuscript the results of the reactivation of luciferase-GFP with and without Hsp104 to emphasize the role of Hsp104 in the active protein recovery (Figure 2—figure supplement 1A) (page 7, lines 24-27). We propose that aggregate fragmentation by Hsp70-JDPB-Hsp110 increases the effective aggregate surface, at which Hsp104 might become engaged. We do not think that Hsp104 acts only on small aggregates, it might be just more effective, when the number of exposed polypeptides is larger. In the cell, where Hsp104 binds to aggregates of various sizes, protein aggregates apparently also need to undergo such Hsp110-boosted pre-processing by Hsp70, based on the finding that Sse1 is not necessary for Hsp104 recruitment to aggregates, but it is required for Hsp104-dependent disaggregation (Kaimal et al., 2017). We have added a comment on this problem to the Discussion section (pages 11/12, lines 33-4) .

- Page 9: The authors state that the Sse1-2 variant is nearly as effective as Sse1 Wt in stimulating substrate dissociation and refer to published work (Polier et al., 2008). It is unclear how the variant should have Wtlike activity in triggering substrate release although its activity in catalyzing nucleotide exchange is reduced to 5% (both activities are coupled). The observation that high Sse1-2 concentrations do not inhibit protein disaggregation does not necessarily exclude the possibility that high Sse1 WT concentration inhibit the reaction by overstimulating substrate release. The latter possibility should be considered by the authors and added to the discussion section.

We agree with the Reviewer that the description of the Sse1-2 variant was misleading, as it was lacking the key information, that according to the published data (Polier et al., 2008), it was 10 times higher the concentration of the Sse1-2 variant than Sse1 WT that had a similar nucleotide-exchange activity to the wild type. We have changed the text (page 9, lines 16-22, page 13, lines 26-28) to avoid confusion as well as the model in the Figure 5, to underline the importance of substrate release as the cause of the Hsp110-dependent inhibition.

- While similar effects are observed for human class A and class B JDP co-chaperones, they are clearly less pronounced. A mechanistic explanation for the difference between yeast and human chaperones is currently missing and the authors are asked to elaborate on this aspect.

There are indeed clear differences between the human and yeasts systems, especially regarding the dependence on the NEF. Hsc70 has been reported to have a lower rate of ADP release (Dragovic et al., 2006) and thus might rely more on Hsp110 than its yeast ortholog. For the same reason, the strong Hsc70 stimulation by Hsp105 is also observed with class A JDP. We have added a comment on these effects in the Discussion section (page 12, lines 17-21).

Minor points

- Figure S1C (right): the disaggregation rate (%GFP/h) is somewhat misleading/confusing as a value of more than 150%/h is determined in the presence of the complete disaggregation system while only approx. 60% GFP is indeed refolded by the system (Figure S1C, left). Showing the rate as %GFP/min seems more rational.

We changed the units according to the Reviewer’s comment (Figure 1—figure supplement 1A, C).

- Figure S5B: Only a single data point is shown for Ssa1/Sis1/Sse1.

We changed the figure to include datapoints from all three repeats (Figure 3—figure supplement 1 B).

- There are several typos throughout the manuscript. A more careful proofreading is recommended

We have corrected the typos.

Reviewer #1 (Public Review):

The experiments differ somewhat in regard to the aggregated protein used. For example, in Figure 1A, FFL is used with only limited reactivation (10% reactivated at the last timepoint and the curve is flattening), while in Figure 2B FFL-EGFP is used to monitor microscopically what appears to be complete disaggregation. Does FFL-EGFP behave the same as FFL in assays such as the one in Figure 1A or are there major differences that may impact how the data should be interpreted?

We added the results of Luc-GFP reactivation (Figure 2—figure supplement 1 B) (discussed on page 7, lines 24-27 of the manuscipt) which agree with the results obtain with Luciferase as a substrate (Figure 1—figure supplement 1 B). They clearly show that the Ssa1-Sis1-Sse1-dependent decrease in aggregate size is not associated with the recovery of active protein.

Reviewer #2 (Public Review):

Experimental data concerning the class A JDPs should be interpreted with caution. These experiments show very small reactivation activities for luciferase in the range of 0-1% without the addition of Hsp104 and 0-15% with the addition of Hsp104. Moreover, since the assay is based on the recovery of luciferase activity, it conflates two chaperone activities, namely disaggregation and refolding. It is possible that the small degree of reactivation observed for the class A JDP reflects a minor subpopulation of the aggregated species that is particularly easy to disaggregate/refold and may thus not be representative of bulk behaviour.

The disaggregation by the Hsp70 system can be enhanced by the addition of small heat shock proteins at the step of substrate aggregation (Rampelt et al., 2012). However, sHsps compete with Hsp70 for binding to the aggregate (Żwirowski et al., 2017) and for that reason we decided not to include sHsps in the experiments presented in the manuscript, as it would introduce another level of complexity. However, as a control, we performed the disaggregation assay with Hsp70 with Ydj1 using luciferase aggregates formed in the presence or absence of sHsp (Author response image 2). In 1 h, the Hsp70 system without Hsp104 yielded 5% of recovered luciferase activity and the system with Hsp104, 23% compared to the native. The impact of Sse1 on Ssa1-Ydj1 and Ssa1-Ydj1-Hsp104 was similar as for luciferase aggregates formed without sHsps (Figure 1A, Figure 1—figure supplement 1 B). Furthermore, according to the Reviewer’s comment, we have changed the Figure 5 to underscore the more prominent role of class A JDPs in the final protein folding than in disaggregation.

Author response image 2.

Disaggregaton of heat-aggregated luciferase – impact of sHsps. Luciferase (2 μM) was denatured with (blue) or without (red) Hsp26 (20 μM) at 45 ̊C for 15 min in the buffer A (Materials and Methods). Upon 100-fold dilution with the buffer A, supplemented wih 5 mM ATP, 2 mM DTT, 1.2 μM creatine kinase, 20 mM creatine phosphate, chaperones indicated in the legend were added to the final concentration of 1 μM, except for Sse1, concentration of which was 0.1 μM. Shown is luciferase activity measured after 1 h of incubation at 25 °C, normalized to the activity of native luciferase.

Reviewer #3 (Public Review):

Enhanced recruitment of Hsp70 in the presence of Hsp110 was shown for amyloid fibrils before (Beton et al., EMBO J 2022) and should be acknowledged. 

We have added the suggested citation with a respective comment (page 11, lines 20-21).

eLife assessment

This fundamental study demonstrates a novel method for imaging glutamate receptors in situ via cryo-ET. The use of cutting-edge methods is well-described and is compelling. This paper is broadly relevant to biophysicists and neuroscientists.

Reviewer #1 (Public review):

Summary:

Matsui et al. present an experimental pipeline for visualizing molecular machinery of synapses in the brain, which includes numerous techniques, starting with generating labeled antibodies and recombinant mice, continuing with HPF and FIB milling and finishing with tilt series collection and 3D image processing. This pipeline represents a breakthrough in preparation of brain tissue for high resolution imaging and can be used in future tomographic research to reconstruct molecular details of synaptic complexes as well as pre- and post-synaptic assemblies. This methodology can also be adapted for a broader range of tissue preparations and signifies the next step towards better structural understanding of how molecular machineries operate in natural conditions.

Strengths:

The manuscript is very well written, contains a detailed description of methodology, provides nice illustrations and will be an outstanding guide for future research.

Weaknesses:

None noted.

Reviewer #2 (Public review):

Summary

The authors present a method that allows for the identification and localization of molecular machinery at chemical synapses in unstained, unfixed native brain tissue slices. They believe that this approach will provide a 3D structural basis for understanding different mechanisms of synaptic transmission, plasticity, and development. To achieve this, the group used genetically engineered mouse lines and generated thin brain slices that underwent high-pressure freezing (HPF) and focused ion beam (FIB) milling. Utilizing cryo-electron tomography (cryo-ET) and integrating it with cryo-fluorescence microscopy, they achieved micrometer resolution in identifying the glutamatergic synapses along with nanometer resolution to locate AMPA receptors GluA2-subunits using Fab-AuNP conjugates. The findings are summarized with detailed examples of successfully prepared substrates for cryo-ET, specific morphological identification and localization, and the detailed structural organization of excitatory synapses, including synaptic vesicle clusters close to the postsynaptic density and in the cleft.

Strengths

The study advances previous work that used cultured neurons or synaptosomes. Combining cryo-electron tomography (cryo-ET) with fluorescence-guided targeting and labeling with Fab-AuNP conjugates enabled the study of synapses and molecular structures in their native environment without chemical fixation or staining. This preserves their near-native state, offering high specificity and resolution. The methods developed are mostly generalizable, allowing adaptation for identifying and localizing other key molecules at glutamatergic synapses and potentially useful for studying a variety of synapses and cellular structures beyond the scope of this research.

Weaknesses

The preparation and imaging techniques are complex and require highly specialized equipment and expertise, potentially limiting their accessibility and widespread adoption.

Additionally, the methods might need further modifications/tweaks to study other types of synapses or molecular structures effectively.

The reliance on genetically engineered mouse lines and monoclonal, high-affinity antibodies/Fab fragments to specifically label receptors/proteins would limit the wider employment of these methods.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Matsui et al. present an experimental pipeline for visualizing the molecular machinery of synapses in the brain, which includes numerous techniques, starting with generating labeled antibodies and recombinant mice, continuing with HPF and FIB milling, and finishing with tilt series collection and 3D image processing. This pipeline represents a breakthrough in the preparation of brain tissue for high-resolution imaging and can be used in future tomographic research to reconstruct molecular details of synaptic complexes as well as pre- and post-synaptic assemblies. This methodology can also be adapted for a broader range of tissue preparations and signifies the next step towards a better structural understanding of how molecular machineries operate in natural conditions.

Strengths:

The manuscript is very well written, contains a detailed description of methodology, provides nice illustrations, and will be an outstanding guide for future research.

Weaknesses:

None noted.

Reviewer #2 (Public Review):

Summary:

The authors present a method that allows for the identification and localization of molecular machinery at chemical synapses in unstained, unfixed native brain tissue slices. They believe that this approach will provide a 3D structural basis for understanding different mechanisms of synaptic transmission, plasticity, and development. To achieve this, the group used genetically engineered mouse lines and generated thin brain slices that underwent high-pressure freezing (HPF) and focused ion beam (FIB) milling. Utilizing cryo-electron tomography (cryo-ET) and integrating it with cryo-fluorescence microscopy, they achieved micrometer resolution in identifying the glutamatergic synapses along with nanometer resolution to locate AMPA receptors GluA2-subunits using Fab-AuNP conjugates. The findings are summarized with detailed examples of successfully prepared substrates for cryo-ET, specific morphological identification and localization, and the detailed structural organization of excitatory synapses, including synaptic vesicle clusters close to the postsynaptic density and in the cleft.

Strengths:

The study advances previous work that used cultured neurons or synaptosomes. Combining cryo-electron tomography (cryo-ET) with fluorescence-guided targeting and labeling with Fab-AuNP conjugates enabled the study of synapses and molecular structures in their native environment without chemical fixation or staining. This preserves their near-native state, offering high specificity and resolution. The methods developed are generalizable, allowing adaptation for identifying and localizing other key molecules at glutamatergic synapses and potentially useful for studying a variety of synapses and cellular structures beyond the scope of this research.

Weaknesses

The preparation and imaging techniques are complex and require highly specialized equipment and expertise, potentially limiting their accessibility and widespread adoption.

Additionally, the methods might need further modifications/tweaks to study other types of synapses or molecular structures effectively.

The reliance on genetically engineered mouse lines may again impact the generalizability of the findings.

Similarly, the requirement of monoclonal, high-affinity antibodies/Fab fragments to specifically label receptors/proteins would limit the wider employment of these methods.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Matsui et al. present an experimental pipeline for visualizing the molecular machinery of synapsis in the brain, which includes numerous techniques, starting with generating labeled antibodies and recombinant mice, continuing with HPF and FIB milling, and finishing with tilt series collection and 3D image processing. This pipeline represents a breakthrough in the preparation of brain tissue for high-resolution imaging and can be used in future tomographic research to reconstruct molecular details of synaptic complexes as well as pre- and post-synaptic assemblies. This methodology can also be adapted for a broader range of tissue preparations and signifies the next step towards a better structural understanding of how molecular machineries operate in natural conditions.

The manuscript is very well written, contains a detailed description of methodology, provides nice illustrations, and will be an outstanding guide for future research. I only have a few suggestions to further improve this excellent manuscript.

The labeling experiment in Supplementary Figure 3 may have a limitation in the accessibility of certain "narrow" regions to 15F1Fabs (both JF646 and AuNP labeled). Would that be more correct to refer to the labeling of accessible GluA2-containing AMPARs rather than the majority of these receptors in the tissue (lines 180-183)?

The text has been modified to reference “accessible GluA2-containing AMPARs”

Minor comments:

(1) Lines 38-39. "natively derived" appears to be unnecessary here and can be deleted.

Done

(2) Line 153. Please specify the 20% dextran cryoprotectant.

Done.

(3) Lines 155-157. Please label the stratum radiatum and stratum lacunosum-moleculare in Figure 3B.

Done

(4) Figures 1C, 2B, 5B, 5D-E. Missing units for Y-axes.

Done

(5) Supplemental Figure 1. Please add band annotation.

Done

(6) Supplemental Figure 3. Scale bars are missing.

Done

(7) Supplemental Video 1 does not play.

The video file has been corrected.

Reviewer #2 (Recommendations For The Authors):

My congratulations to the authors for undertaking this challenging work.

Major concerns that need to be addressed:

It's unclear if the anti-GluA2 15F1 Fab-AuNP conjugate would affect the receptor clustering and localization on the synaptic membranes. It binds at the distal end, which is likely to impact its interactions with other synaptic proteins, which may affect the synaptic organization and function.

Concern addressed in the ‘Discussion’ section.

The hippocampal slices were treated with the anti-GluA2 15F1 Fab-148 AuNP conjugate for 1 hour at room temperature. It might be helpful to discuss the potential affects of Fab-AuNp on synaptic function. It has been demonstrated previously that introducing binders of the receptors ectodomains can affect synaptic function.

Concern also addressed in the ‘Discussion’ section. 

Kunimichi Suzuki et al. Science369,eabb4853(2020).DOI:10.1126/science.abb4853 https://patents.google.com/patent/US20230192810A1/en

eLife assessment

This revised study presents valuable evidence that a combination of endothelial cells, astrocytes, and neuroblastoma cells of human origin can integrate to form an in vitro brain blood barrier, that recapitulates key aspects of its natural counterpart, especially at short times. Convincingly, the mechanism by which neuroblastoma-secreted GDNF increases Claudin-5 and VE-cadherin is described. To substantiate the role of GDNF in vivo, authors demonstrated that knock-down of this neurotrophic factor, increased the permeability of the brain blood barrier in mice. This in vitro system can be used to study the permeability of the human brain blood barrier to different drugs.

Reviewer #1 (Public review):

Summary:

This paper by Yang et al. established an in vitro triple co-culture BBB model and demonstrated its advantages compared with the mono or double co-culture BBB model. Further, the authors used their established in vitro BBB model and combined it with other methodologies to investigate the specific signaling mechanisms that co-culture with astrocytes but also neurons enhancing the integrity of endothelial cells.

Strengths:

The results persuasively demonstrated that the established triple co-culture BBB model well mimicked several important characteristics of BBB compared with the mono-culture BBB model, including better barrier function and in vivo/in vitro correlation. The use of human-derived immortalized cells made the model construction process faster and more efficient and had a better in vivo correlation without the complications of species differences. This model is expected to be a useful high-throughput evaluation tool for CNS drug development.

Moreover, the authors used a variety of experiments to prove that the triple co-culture model also reflected the interactions between NVU cells, including promoting endothelial cell proliferation and the formation of intercellular junctions. Interestingly, the authors found that neurons also released GDNF to promote barrier properties of brain endothelial cells, as most current research has focused on the promoting effect of astrocytes-derived GDNF on BBB. Meanwhile, the author also validated the functions of GDNF for BBB integrity in vivo by silencing GDNF in mouse brains. Overall, the experiments and data presented support the claim that neurons, alongside astrocytes, contribute to the promoting effects of the barrier function of endothelial cells through GDNF secretion.

Weaknesses:

While the authors explained that the use of human-derived immortalized cells has been justified as more reproducible and efficient in constructing the model, the TEER value of the triple co-culture model remains lower than that of the physiological statement. Future research may need to explore additional methods to further enhance the barrier function of the model.

Reviewer #2 (Public review):

Summary:

Yang and colleagues developed a new in vitro blood-brain barrier model that is relatively simple yet outperforms previous models. By incorporating a neuroblastoma cell line, they demonstrated increased electrical resistance and decreased permeability to small molecules

Strengths:

The authors initially elucidated the soluble mediator responsible for enhancing endothelial functionality, namely GDNF. Subsequently, they elucidated the mechanisms by which GDNF upregulates the expression of VE-cadherin and Claudin-5. They further validated these findings in vivo, and demonstrated predictive value for molecular permeability as well. The study is meticulously conducted and easily comprehensible. The conclusions are firmly supported by the data, and the objectives are successfully achieved. This research is poised to advance future investigations in BBB permeability, leakage, dysfunction, disease modeling, and drug delivery, particularly in high-throughput experiments. I anticipate an enthusiastic reception from the community interested in this area. While other studies have produced similar results with tri-cultures (PMID: 25630899), this study notably enhances electrical resistance compared to previous attempts.

Weaknesses:

The power of this system lies in its simplicity, which is enough to study BBB permeability. However, it also lacks some other important cell-cell interactions such as those involving pericytes. Nonetheless, this is still a valuable tool for high throughput screening.

As with many other similar systems, it has lower TEER values compared to the in vivo counterpart, this is an issue that researchers in the field will have to address in future studies

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this manuscript, the authors established an in vitro triple co-culture BBB model and demonstrated its advantages compared with the mono or double co-culture BBB model. Further, the authors used their established in vitro BBB model and combined it with other methodologies to investigate the specific mechanism that co-culture with astrocytes but also neurons enhanced the integrity of endothelial cells.

Strengths:

The results persuasively showed the established triple co-culture BBB model well mimicked several important characteristics of BBB compared with the mono-culture BBB model, including better barrier function and in vivo/in vitro correlation. The human-derived immortalized cells used made the model construction process faster and more efficient, and have a better in vivo correlation without species differences. This model is expected to be a useful high-throughput evaluation tool in the development of CNS drugs.

Based on the previous experimental results, detailed studies investigated how co-culture with neurons and astrocytes promoted claudin-5 and VE-cadherin in endothelial cells, and the specific signaling mechanisms were also studied. Interestingly, the authors found that neurons also released GDNF to promote barrier properties of brain endothelial cells, as most current research has focused on the promoting effect of astrocytes-derived GDNF on BBB. Meanwhile, the author also validated the functions of GDNF for BBB integrity in vivo by silencing GDNF in mouse brains. Overall, the experiments and data presented support their claim that, in addition to astrocytes, neurons also have a promoting effect on the barrier function of endothelial cells through GDNF secretion.

Weaknesses:

Although the authors demonstrated a highly usable for predicting the BBB permeability, recorded TEER measurements are still far from the human BBB in vivo reported measurements of TEER, and expression of transporters was not promoted by co-culture, which may lead to the model being unsuitable for studying drug transport mediated by transporters on BBB.

Thank the reviewer very much for the opportunity to improve our manuscript. The immortalized human cell lines, hCMEC/D3 cell, have poor barrier properties and differences in the expression of some transporters and metabolic enzymes as well as TEER compared to human physiological BBB. However, the use of human primary BMECs may be restricted by the acquisition of materials and ethical approval. Isolation and purification of human primary BMECs are time-consuming and laborious. Moreover, culture conditions can alter transcriptional activity (PMID: 37076016). All limit the establishment of BBB models based on primary human BMECs for high-throughput screening. Thus, hCMEC/D3 is still widely used to study characteristics of drug transport across BBB and the effects of certain diseases on BBB (PMID: 37076016; 38711118; 31163193) as it is easy to culture and can express a large number of transporters and metabolic enzymes in its physiological state. Therefore, hCMEC/D3 cells were selected to develop our in vitro BBB model.

Reviewer #1 (Recommendations For The Authors):

Point 1: The authors claim that GDNF is mainly released by human neuroblastoma SH-SY5Y cells in the in vitro BBB model, but there are still some differences between the characteristics of cell lines and neurons. The authors should discuss or provide evidence about the distribution and source of GDNF in the brain to support this conclusion.

We greatly appreciate your helpful suggestions. According to your advice, we have revised the “Discussion” in the revised manuscript as follows:

In “Discussion”:

“GDNF is mainly expressed in astrocytes and neurons (Lonka-Nevalaita et al., 2010; Pochon et al., 1997). In adult animals, GDNF is mainly secreted by striatal neurons rather than astrocytes and microglial cells (Hidalgo-Figueroa et al., 2012). The present study also shows that GDNF mRNA levels in SH-SY5Y cells were significantly higher than that in U251 cells. GDNF was also detected in conditioned medium from SH-SY5Y cells. All these results demonstrate that neurons may secrete GDNF”.

Point 2: The authors found that co-culture induced the proliferation of endothelial cells (Figure 1H). I suggest the authors discuss whether the proliferation of endothelial cells would affect their permeability.

Thanks for your suggestion. According to your advice, we have investigated the effect of cell proliferation on the leakage of the cell layer and included the results in Figure 1—figure supplement 1. The present study showed that basic fibroblast growth factor (bFGF) increased cell proliferation of hCMEC/D3 cells but little affected the expression of both claudin-5 and VE-cadherin (in Figure 2F). The hCMEC/D3 cells were incubated with different doses of bFGF and permeabilities of fluorescein (NaF) and FITC-Dextran 3–5 kDa across hCMEC/D3 cell monolayer were measured. The results showed that incubation with bFGF increased cell proliferation and reduced permeabilities of fluorescein and FITC-Dextran across hCMEC/D3 cell monolayer. However, the permeability reduction was less than that by double co-culture with U251 cells or triple co-culture. These results inferred that contribution of cell proliferation to the barrier function of hCMEC/D3 cells was minor. We have made the modifications in “Results” of our manuscript as follows:

In “Result”:

“Furthermore, hCMEC/D3 cells were incubated with basic fibroblast growth factor (bFGF), which promotes cell proliferation without affecting both claudin-5 and VE-cadherin expression (Figure 2F). The results showed that incubation with bFGF increased cell proliferation and reduced permeabilities of fluorescein and FITC-Dex across hCMEC/D3 cell monolayer. However, the permeability reduction was less than that by double co-culture with U251 cells or triple co-culture. These results inferred that contribution of cell proliferation to the barrier function of hCMEC/D3 was minor (Figure 1—figure supplement 1)”.

Point 3: The authors claimed that GDNF induced the expression of claudin-5 and VE-cadherin separately. However, Andrea Taddei et al. reported that VE-cadherin itself also regulates claudin-5 through the inhibitory activity of FoxO1 (Andrea Taddei et al., 2008). The authors did not consider whether the upregulation of claudin-5 is associated with the increase of VE-cadherin.

Thank you for your suggestion. We also investigated whether VE-cadherin affected claudin-5 expression in hCMEC/D3 cells transfected with VE-cadherin siRNA. It was not consistent with the report by Taddei et al. that silencing VE-cadherin only slightly decreased the mRNA level of claudin-5 without significant difference. Furthermore, basal and GDNF-induced claudin-5 protein levels were unaltered by silencing VE-cadherin. The discrepancies may come from characteristics of the tested cells. Endothelial cells derived from murine embryonic stem cells with homozygous null mutation were used in Taddei’s study, while we transfected immortalized brain microvascular endothelial cells with siRNA. Several reports have demonstrated different mechanisms regulating expression of claudin-5 and VE-cadherin. In retinal endothelial cells, hyperglycemia remarkably reduced claudin-5 expression (but not VE-cadherin) (PMID: 24594192). However, in hCMEC/D3 cells, hypoglycemia significantly decreased claudin-5 (not VE-cadherin) expression but hyperglycemia increased VE-cadherin expression (not claudin 5) (PMID: 24708805). Therefore, the roles of VE-cadherin in regulation of claudin-5 in BBB should be further investigated.

Following your valuable suggestion, we have modified the “Results”, “Discussion” and “Figure 4—figure supplement 1” in the revised manuscript as follows:

In “Result”:

“It was reported that VE-cadherin also upregulates claudin-5 via inhibiting FOXO1 activities (Taddei et al, 2008). Effect of VE-cadherin on claudin-5 was studied in hCMEC/D3 cells silencing VE-cadherin. It was not consistent with the report by Taddei et al. that silencing VE-cadherin only slightly decreased the mRNA level of claudin-5 without significant difference. Furthermore, basal and GDNF-induced claudin-5 protein levels were unaltered by silencing VE-cadherin (Figure 4—figure supplement 1). Thus, the roles of VE-cadherin in regulation of claudin-5 in BBB should be further investigated.”

In “Discussion”:

“Claudin-5 expression is also regulated by VE-cadherin (Taddei et al., 2008). Differing from the previous reports, silencing VE-cadherin with siRNA only slightly affected basal and GDNF-induced claudin-5 expression. The discrepancies may come from different characteristics of the tested cells. Several reports have supported the above deduction. In retinal endothelial cells, hyperglycemia remarkably reduced claudin-5 expression (but not VE-cadherin) (Saker et al., 2014). However, in hCMEC/D3 cells, hypoglycemia significantly decreased claudin-5 expression but hyperglycemia increased VE-cadherin expression (Sajja et al., 2014)”.

“Figure 4—figure supplement 1: The contribution of VE-Cadherin on the GDNF-induced claudin-5 expression. Effects of the VE-Cadherin siRNA (siVE-Cad) on mRNA expression of VE-cadherin (A) and claudin-5 (B). Effects of siVE-Cad and GDNF on claudin-5 and VE-cadherin protein expression (C). NC: negative control plasmids. The above data are shown as the mean ± SEM. Four biological replicates per group. Two technical replicates for A and B, and one technical replicate for C. Statistical significance was determined using unpaired Student’s t-test or one-way ANOVA test followed by Fisher’s LSD test.”

Point 4:  The annotation of significance with the p-values in the figures might not be visually concise and clear. It is recommended to provide the p-values in the legends or raw data.

Thank you for your valuable suggestion. We have revised our figures in our revised manuscript. The specific p-values and statistical methods were summarized in the source data files of each figure.

Point 5: The authors need to note the material of the Transwell membrane used to increase the reproducibility of experiments, because different materials may cause differences in permeability and TEER (DianeM. Wuest et al., 2013).

We greatly appreciate your valuable suggestions. According to your advice, we have provided the information on the material of the Transwell membrane in the “Materials and Methods” in the revised manuscript as follows:

In “Materials and Methods”:

“U251 cells were seeded at 2 × 104 cells/cm2 on the bottom of Transwell inserts (PET, 0.4 µm pore size, SPL Life Sciences, Pocheon, Korea) coated with rat-tail collagen (Corning Inc., Corning, NY, USA)”.

Point 6: It is not necessary to abbreviate "in vitro/in vivo correlation" in the legend of Figure 7 as it was not mentioned again in the following text.

Thank you for your valuable suggestion. We have deleted the abbreviation of "Figure 7" of the revised manuscript.

In “Figure 7”

“Figure 7. In vitro/in vivo correlation assay of BBB permeability."

Reviewer #2 (Public Review):

Summary:

Yang and colleagues developed a new in vitro blood-brain barrier model that is relatively simple yet outperforms previous models. By incorporating a neuroblastoma cell line, they demonstrated increased electrical resistance and decreased permeability to small molecules.

Strengths:

The authors initially elucidated the soluble mediator responsible for enhancing endothelial functionality, namely GDNF. Subsequently, they elucidated the mechanisms by which GDNF upregulates the expression of VE-cadherin and Claudin-5. They further validated these findings in vivo, and demonstrated predictive value for molecular permeability as well. The study is meticulously conducted and easily comprehensible. The conclusions are firmly supported by the data, and the objectives are successfully achieved. This research is poised to advance future investigations in BBB permeability, leakage, dysfunction, disease modeling, and drug delivery, particularly in high-throughput experiments. I anticipate an enthusiastic reception from the community interested in this area. While other studies have produced similar results with tri-cultures (PMID: 25630899), this study notably enhances electrical resistance compared to previous attempts.

Weaknesses:

(A) Considerable effort has been directed towards developing in vitro models that more closely resemble their in vivo counterparts, utilizing stem cell-derived NVU cells. Although these examples are currently rudimentary, they offer better BBB mimicry than Yang's study.

Thank you very much for your valuable comments. Indeed, hCMEC/D3 cells, have poor barrier properties and low TEER compared to human physiological BBB. The human pluripotent stem cells BBB models (hPSC-BBB models) make it possible to provide a robust and scalable cell source for BBB modeling, although many challenges remain, particularly concerning reproducibility and recreation of multifaceted phenotypes in vitro with increasing complexity. Moreover, the hPSC-derived BBB models are highly dependent upon the heterogeneous incorporation of hPSC-derived BMEC origins, cells derived from different protocols are not well validated and standardized in the BBB models. Thus, the hPSC-BBB models are still being developed and their clinic applications are still at an early stage (PMID: 34815809; 35755780). The hCMEC/D3 cell line is still widely used to study characteristics of drug transport across BBB and the effects of certain diseases on BBB (PMID: 37076016; 38711118; 31163193) as it is easy to culture and can express a large number of transporters and metabolic enzymes in its physiological state. Therefore, hCMEC/D3 cells were selected to develop our in vitro BBB model.

(B) Additionally, some instances might benefit from more robust statistical tests; nonetheless, I do not think this would significantly alter the experimental conclusions.

Thank you for your valuable suggestions on the statistical methods used in our study, which made us realize our lack of rigor in selecting statistical methods. We have made modifications to statistical methods, and all statistical results showed the manuscript have been updated accordingly.

(C) Similar experiments with tri-cultures yielding analogous results have been reported by other authors (PMID: 25630899). TEER values are a bit higher than the aforementioned experiments; however, this study has values at least one order of magnitude lower than physiological levels.

Thank your advice. We also noticed that TEER values in the present study were different from previous reports, which may come from types of BEMCs, astrocytes, and neurons.

Reviewer #2 (Recommendations For The Authors):

Point 1: If you've already decided to enhance the model by incorporating additional cell types, why not include pericytes as well? As mentioned in the public review, other studies have explored tri-culture models; adding pericytes or other cell types could provide valuable insights.

We greatly appreciate your helpful suggestions. As you mentioned, the barrier function of our model still needs further improvement, which is also a limitation of our current model. In our future research, we will aim to optimize our model by incorporating other NVU cells. Beyond drug screening, we also hope that our in vitro BBB model can serve as a versatile tool to investigate underlying factors associated with neuropathological disorders. According to your advice, we have modified “Discussion” in the revised manuscript as follows:

In “Discussion”:

“However, the study also has some limitations. In addition to neurons and astrocytes, other cells such as microglia, pericytes, and vascular smooth muscle cells, especially pericytes, may also affect BBB function. How pericytes affect BBB function and interaction among neurons, astrocytes, and pericytes needs further investigation.”

Point 2: The decline in TEER after 6 days is concerning. Have you extended your experiments beyond day 7? If so, what were the outcomes? Did the system degrade, leading to decreased resistance, or did cell death occur?

We greatly appreciate your helpful recommendation. We also observed that the TEER of our culture system began to decline on day 7. To ensure the reliability of our experiments, our experiments were conducted on day 6 of co-cultivation and did not extend beyond day 7. We speculate that the reason for the decrease in TEER values may be due to excessive cell contact, which could inhibit cell proliferation and long-term cultivation may lead to cell aging. Similar results showing a decrease in TEER of i_n vitro_ BBB models after prolonged culture have been reported in other studies (PMID: 31079318; 8470770). To eliminate misunderstandings, we have made the following modifications to our manuscript:

In “Result”:

“TEER values were measured during the co-culture (Figure 1B). TEER values of the four in vitro BBB models gradually increased until day 6. On day 7, the TEER values showed a decreasing trend. Thus, six-day co-culture period was used for subsequent experiments”.

In “In vitro BBB permeability study” of “Materials and Methods”:

“On day 7, the TEER values of BBB models showed a decreasing trend. Therefore, the subsequent experiments were all completed on day 6”.

Point 3: It is standard practice for figures to be referenced in the order they appear in the manuscript. However, Figures 1A and 1B are not mentioned until the end of the methods section. Adding a brief sentence at the beginning of the main body referencing these figures would improve the clarity of the experimental approach.

Thank you for your valuable suggestion. We had made modifications to Figure 1, and the details of the cell model establishment process had been included in Figure 9 which is mentioned in the “Materials and Methods” section.

Point 4: To strengthen the evidence supporting the proliferative effect of GDNF, consider incorporating additional measures beyond cell count alone. While an increase in cell count could be attributed to reduced cell death (given GDNF's pro-survival properties), proliferation effects have also been shown (PMID: 28878618). I suggest demonstrating proliferation with markers or cell cycle analysis would provide more robust evidence.

Thank you for your helpful suggestion. We used EdU incorporation and CCK-8 assays to further detect the proliferation of hCMEC/D3 cells, and corresponding results were added in the revised Figure 1H and Figure 1I. The description of results is shown as follows:

In “Results”:

“Co-culture with SH-SY5Y, U251, and U251 + SH-SY5Y cells also enhanced the proliferation of hCMEC/D3 cells. Moreover, the promoting effect of SH-SY5Y cells was stronger than that of U251 cells (Figure 1G-1I).”

Point 5: Could you specify the use of technical replicates in your experiments? How many?

Thank you for your helpful suggestion, and we apologize for the issue you pointed out. We have now specified the technical replicates of experiments in the legends of the revised manuscript. In general, the technical replicate number of ELISA and qPCR is two, and that of the rest experiments is one. And we have also made the following modifications to our manuscript:

In “Statistical analyses” of “Materials and Methods”:

“All results are presented as mean ± SEM. The average of technical replicates generated a single independent value that contributes to the n value used for comparative statistical analysis”.

Point 6: Given the sample size of 4 in most experiments, it may be insufficient for passing a normality test. Therefore, it's advisable to employ non-parametric tests such as the Kruskal-Wallis test, followed by appropriate post-hoc tests.

Thank you for your valuable and useful suggestion. We apologize for our initial oversight regarding statistics. Based on your suggestion, we have thoroughly reviewed and revised the statistical methods and statistical results in the manuscript. Referring to the ‘Statistics Guide’ of GraphPad (H. J. Motulsky, "The power of nonparametric tests", GraphPad Statistics Guide. Accessed 20 June 2024. https://www.graphpad.com/guides/prism/latest/statistics/stat_the_power_of_nonparametric_tes.htm), the Kruskal-Wallis test is more robust when the data does not follow a normal distribution or homogeneity of variance. However, due to its reliance on ranks, it may have lower sensitivity in detecting small differences. If the total sample size is tiny, the Kruskal-Wallis test will always give a P value greater than 0.05 no matter how much the groups differ. To address this, we first used the Shapiro-Wilk test to assume whether the samples come from Gaussian distributions. For samples meeting this criterion, parametric tests were employed. For samples that do not follow the Gaussian distribution, as per your advice, we utilized the non-parametric tests. We have modified the “Statistical analyses” in the revised manuscript as follows:

In “Statistical analyses” of “Materials and Methods”:

“The data were assessed for Gaussian distributions using Shapiro-Wilk test. Brown-Forsythe test was employed to evaluate the homogeneity of variance between groups. For comparisons between two groups, statistical significance was determined by unpaired 2-tailed t-test. The acquired data with significant variation were tested using unpaired t-test with Welch's correction, and non-Gaussian distributed data were tested using Mann-Whitney test. For multiple group comparisons, one-way ANOVA followed by Fisher’s LSD test was used to determine statistical significance. The acquired data with significant variation were tested using Welch's ANOVA test, and non-Gaussian distributed data were tested using Kruskal-Wallis test. P < 0.05 was considered statistically significant. The simple linear regression analysis was used to examine the presence of a linear relationship between two variables. Data were analyzed using GraphPad Prism software version 8.0.2 (GraphPad Software, La Jolla, CA, USA)”.

eLife assessment

The present study provides valuable evidence on the neurochemical mechanisms underlying working memory in obesity. The authors' approach considering specific working memory operations (maintenance, updating) and putative dopaminergic genes is solid, though the inclusion of a more direct measure of dopamine signaling would have strengthened the work.

Reviewer #1 (Public review):

Herzog and colleagues investigated the interactions between working memory (WM) task condition (updating, maintenance) and BMI (body-mass-index), while considering selected dopaminergic genes (COMT, Taq1A, C957T, DARPP-32). Emerging evidence suggest that there might be a specific negative association with BMI in the updating but not maintenance condition, with potential bearings to reversal reward learning in obesity. The inclusion of multiple dopaminergic genes is a strength in the present study, considering the complexity of the interactions between tonic and phasic dopamine across the brain that may distinctly associate with the component processes of WM. Here, the finding was that BMI was negatively associated with WM performance regardless of the condition (updating, maintenance), but in models including moderation by either Taq1A or DARPP-32 (but not by COMT and C957T) an interaction by task condition was observed. Furthermore, a two-way interaction effect between BMI and genotype was observed exclusively in the updating condition. These findings are in line with the accounts by which striatal dopamine as reflected by Taq1A and DARPP-32 play an important role in working memory updating, while cortical dopamine as reflected by COMT is mainly associated with maintenance. The authors conclude that the genetic moderation reflects a compound effect of having high BMI and an advantageous allele in Taq1A or DARPP-32 to working memory updating specifically.

These data increment the accumulating evidence that the dopamine system plays an important role in obesity. The result that Taq1A and DARPP-32 moderated the interaction between WM condition and BMI required intricate post hoc analysis to understand the bearings to updating. The authors found that Taq1A or DARPP-32 genotype moderated the negative association between BMI and WM exclusively in update condition (significant two-way interaction effect), suggesting that the BMI-WM associations in other conditions were similar across genotypes. Importantly, visual inspection of the relationship between WM and BMI (Fig 4 & 5) suggests more prevalent positive effects of the putatively advantageous Taq1A-A1 and DARPP-32-AA genotypes to the overall negative relationship between WM and BMI in updating, but not in the other conditions. Given that an overall negative relationship was statistically supported across all conditions (model 1), a plausible interpretation would be that updating condition stands out in terms of a positive moderation by putative advantageous genotypes, rather than compound negative consequences of BMI and genotype in updating. Statistical testing stratified by Taq1A genotype confirmed that the interaction with task condition was driven by the carriers of the advantageous genotype, whereas stratification by DARPP-32 genotype revealed a significant task-condition interaction in both A/A- and G-carriers. Taken together, the present results highlight inter-subject variability in the associations between obesity, dopamine, and working memory, which can sometimes be captured using blood-based dopamine markers. This finding indicates that not all individuals with obesity show the same patterns of dopamine-related alterations and underscores the necessity to address inter-individual variability in future research and treatment efforts.

Reviewer #2 (Public review):

Summary:

The authors investigated if obesity is associated with elevated working memory deficits. Prior theorizing would suggest that individuals with a higher BMI would be worse at working memory updating, potentially due to impaired dopaminergic signaling in the striatum. However, the authors find that higher BMI was associated with worse working memory performance, irrespective of having to ignore or update new information. To further explore the putative dopaminergic mechanisms, participants are stratified according to genetic polymorphisms in COMT, Taq1A, DARPP and C957T and the ratio of the amino acids phenylalanine and tyrosine, all implicated in dopamine-signaling. They find that carrying specific alleles of Taq1A and DARPP, but not of COMT and C957T, mitigated the otherwise negative relationship between BMI and working memory for updating, but not for maintenance.

The authors put forward several possible mechanistic explanations of these observations, including imbalances in the striatal go/no-go dopamine pathways. However, only future, more direct measures of dopamine signaling can provide a confirmation of these hypotheses.

Strengths:

Differentiating between working memory maintenance (ignoring) and updating is a powerful way to get a deeper insight into specific working memory deficits in individuals with obesity. This way of assessing working memory could potentially be applied to various populations at risk for cognitive or working memory deficits.

By pooling data from three studies, the authors reached a relatively large sample of 320 participants, which enables the assessment of more subtle effects on working memory, including the differentiation between updating and ignoring.

Working memory gating has long implicated striatal dopamine signaling. This paper shows that a specific combination of a high BMI and specific dopamine-related genotypes can selectively moderate working memory updating. More insight into how these risk factors interact can ultimately lead to more tailor-made treatments.

Weaknesses:

The introduction mentions that specific alleles can alter dopamine signaling in various ways. However, the authors are less clear on how they expect these alterations to subsequently affect working memory updating and maintenance in the current study. While I understand that the complexity of these mechanisms might make it challenging to form specific predictions, it would be helpful if the authors acknowledged this uncertainty and clarified that their analyses are exploratory in nature, and they will therefore refrain from any directional hypotheses regarding the genotypes.

The majority of participants seems to fall within the normal BMI-range, whereas the interaction between BMI and genetic variations or amino acid ratio particularly surfaces at higher BMI. As genetic variations are usually associated with small effect sizes, the effective sample size, although large for a behavioral analysis only, might have been too small to detect meaningful effects of particular alleles of COMT and C957T.

The relationships between genetic variations, BMI and specific disturbances in dopamine signaling are complex, as compensating mechanisms might be at play to mitigate any detrimental effects. Future studies that apply more direct measures or manipulations of dopaminergic processes could therefore aid in mechanistically explaining the results.

Author response:

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

Reviewer #1 (Public Review):

In particular, theoretical analysis of the extant evidence and formulation of the hypothesis remains elusive in terms of the potential mechanisms of updating/maintaining balance in obesity

We thank the reviewer for their feedback regarding the theoretical analysis and hypothesis formulation in our manuscript. We have attempted to build our hypothesis based on established correlations between dopamine levels and working memory capabilities, as seen in various populations affected by dopaminerelated changes (e.g. Parkinson’s disease (Fallon et al. 2017), older individuals (Podell et al., 2012), or more generally, in individuals with lower dopamine synthesis capacity (Colzato et al., 2013)). Our hypothesis — that individuals with higher BMI might show impaired updating — is an extrapolation from observed patterns in these conditions. We recognize that the evidence connecting obesity to similar neuropsychological profiles may seem preliminary. We have tried to elaborate more clearly on how we reached our hypotheses in the revised version of the introduction. 

“Based on the above considerations these inconsistencies may be due to prior studies not clearly differentiating between distractor-resistant maintenance and updating in the context of working memory. This distinction may be crucial, however, as indirect evidence hints at potential specific alteration in these two sub-processes in obesity. For instance, obesity has been associated with aberrant dopamine transmission, with there being an abundance of literature linking obesity to changes in D2 receptor availability in the striatum (see e.g. Horstmann et al., 2015). However, results are not consensual, with studies reporting decreased, increased, or unchanged D2 receptor availability in obesity (Ribeiro et al., 2023; Janssen & Horstmann, 2022; see Darcey et al. (2023) for a potential explanation). Additionally, there are reports of differences in dopamine transporter (DAT) availability in both obese humans (Chen et al., 2008; but also see Pak et al., 2023) and rodents (Narayanaswami et al., 2013; Jones et al., 2021; Hamamah et al., 2023). The observed changes in dopamine are often interpreted as being due to chronic dopaminergic overstimulation resulting from overeating (Volkow & Wise, 2005; Volkow et al., 2008) and altered reward sensitivity as a consequence thereof (Blum et al., 1996). Considering that working memory gating is highly dependent on dopamine signaling, such changes could theoretically alter the balance between maintenance and updating processes in obesity. Next to this, obesity has frequently been associated with functional and structural changes in WM gating-related brain areas, implying another pathway through which working memory gating might get affected. At the level of the prefrontal cortex (PFC), studies have reported reduced gray matter volume and compromised white matter microstructure in individuals with obesity (Debette et al., 2014; Kullmann et al., 2016; Morys et al., 2024; Lv et al., 2024), and functional changes become evident with frequent reports of decreased activity in the dorsolateral PFC during tasks requiring cognitive control (e.g., Morys et al., 2018; Xu et al., 2017). Notably, Han et al. (2022) observed significantly lower spontaneous dlPFC activity during rest, potentially indicating reduced baseline dlPFC activity in obesity. On the level of the striatum, gray matter volume seems to correlate positively with measures of obesity (Horstmann et al., 2011), and individuals with obesity show greater activation of the dorsal striatum in response to high-calorie food stimuli compared to normal-weight individuals, indicating a stronger dopamine-dependent reward response to food cues (Stice et al., 2008; Small et al., 2003). Additionally, changes in connectivity between and within the striatum and PFC in obesity, both structurally (Li et al., 2023) and functionally (Verdejo-Román et al., 2017a, 2017b; Contreras-Rodríguez et al., 2017) have been reported. Although these studies mostly investigate brain function in relation to food and reward processing, changes in these areas may also impair the ability to adequately engage in working memory gating processes, as activity in affective (reward) and cognitive fronto-striatal loops immensely overlap (Janssen et al., 2019). On the behavioral level, individuals with obesity consistently demonstrate impairments in food-specific (Janssen et al., 2017) but also non-food specific goal-directed behavioral control (Janssen et al., 2020) and reinforcement learning (Weydmann et al., 2023). It seems that difficulties with integrating negative feedback may be central to these alterations (Mathar et al., 2017; Kastner et al., 2017), which could explain a potential insensitivity to the negative consequences associated with (over) eating. Crucially, in humans, a substantial contribution to (reward) learning is mediated by working memory processes (Moustafa et al., 2008; Collins & Frank, 2012, 2018; Collins et al., 2014, 2017; Westbrook et al., 2024). The observed difficulties in reward learning in obesity may hence partly be rooted in a failure to update working memory with new reward information, suggesting cognitive issues that extend beyond mere difficulties in valuation processes. However, empirical support for this interpretation is currently lacking. A more nuanced understanding of the effects of obesity on working memory is crucial, however, as it could lead to more targeted intervention options.”

The result that Taq1A and DARPP-32 moderated the interaction between WM condition and BMI requires intricate post hoc analysis to understand the bearings to update. The authors found that Taq1A or DARPP32 genotype moderated the negative association between BMI and WM exclusively in the update condition (significant two-way interaction effect), suggesting that the BMI-WM associations in other conditions were similar across genotypes. Importantly, visual inspection of the relationship between WM and BMI (Fig 4 & 5) suggests more prevalent positive effects of the putatively advantageous Taq1A-A1 and DARPP-32-AA genotypes to the overall negative relationship between WM and BMI in updating, but not in the other conditions. Given that an overall negative relationship was statistically supported across all conditions (model 1), a plausible interpretation would be that the updating condition stands out in terms of a positive moderation by putative advantageous genotypes, rather than compound negative consequences of BMI and genotype in updating. Critically, this interpretation stands in stark contrast with the interpretation put forth by the authors suggesting a specifically negative association between BMI and WM updating.

We are grateful for the reviewers’ thorough review and insightful comments. We appreciate the attention to detail and the opportunity to improve our manuscript. We agree that further examination of the relationship between Taq1A, DARPP-32, and BMI, particularly in the update condition, is crucial for a comprehensive understanding of our results. In response to your feedback, we have conducted additional post hoc analyses, which indeed revealed the effects anticipated by the reviewer. Accordingly, we have revisited our discussion and conclusions to ensure that they accurately reflect the complexities of our findings, particularly regarding the positive moderation by putative advantageous genotypes in the update condition. Once again, we appreciate your thoughtful review and are grateful for the opportunity to strengthen the manuscript based on your feedback.

In the results section we added: 

“Further post hoc examination of the effects on updating revealed that, the association between BMI and performance was significant for A1-carriers (95%CIs: -0.488 to -0.190), with 33.9% lower probability to score correctly per unit change in BMI, but non-significant for non-A1-carriers (95%CIs: -0.153 to 0.129; 1.22% lower probability). Interestingly, compared to all other conditions, in the update condition, the negative association between BMI and task performance was weakest for non-A1-carriers (estimate = -0.012, SE = 0.072, but strongest for A1-carriers (estimate = -0.339, SE = 0.076; see Figure 3 and Table S6), emphasizing that genotype impacts this condition the most. To further check if this difference in slope was statistically significant across conditions, we stratified the sample into Taq1A subgroups (A1+ vs. A1-) and assessed whether BMI affected task performance differently across conditions separately for each subgroup. This analysis revealed no significant difference in the relationship between BMI and task performance across conditions among A1+ individuals (pBMI*condition = 0.219). However, within the A1- subgroup, a significant interaction effect between BMI and condition emerged (pBMI*condition = 0.049). Collectively, these findings suggest that the absence of the A1-allele is linked to improved task performance, particularly in the context of updating, where it seems to mitigate the otherwise negative effects of BMI.” 

“Once more, further examination of the observed DARPP-32, BMI, and condition interaction showed that, in the update condition, the negative association between BMI and task performance was weakest and nonsignificant for A/A (estimate = -0.044, SE = 0.066; 95%CIs: -0.174 to 0.086), but strongest and significant for G-carrying individuals (estimate = -0.324, SE = 0.079; 95%CIs: -0.478 to – 0.170). See Table S7 and Figure 5.  Splitting the sample in to DARPP subgroups (A/A vs. G-carrier) revealed that in both subgroups, there was significant interaction effect of BMI and condition on task performance (pA/A = 0.034, pG-carrier = 0.003). In the case of DARPP, it hence appears that carrying the disadvantageous G-allele could exacerbate the negative effects of BMI, while the more advantageous allele (A/A) might mitigate them - once again particularly in the context of updating.” 

Following from this, we added the following text snippets to the discussion:

“Noteworthy, our data revealed that differences in updating appeared to be driven by the non-risk allele groups. Despite increasing BMI, performance remained stable.” 

“However, as BMI increases, the possession of a greater D2 receptor density seems to become advantageous, as evidenced by the lack of a negative correlation between BMI and updating performance in non-A carriers. We speculate that this phenomenon could potentially be attributed to the compensating effects of this genotype. While individuals with fewer D2 receptors (A1+) may have quicker saturation of receptors regardless of dopamine levels, in those with more D2 receptors (A1-) saturation may be slower. This could contribute to a more finely tuned balance between "go" and "no-go" signaling, despite potential alterations in dopamine tone in obesity (Horstmann et al., 2015; but also see Darcey et al., 2023 or Janssen & Horstmann, 2022). Clearly, the current data cannot provide empirical evidence for these speculations, and further discrete research is needed to establish firm conclusions. 

Regarding DARPP, we found that carrying the G-allele significantly exacerbated the negative effects of BMI, while the more advantageous allele (A/A) mitigated them, once again particularly in the context of updating.”

“Collectively, our observations hint at the potential of advantageous genotypes to moderate the adverse impacts of high BMI on cognitive functions.” 

In conclusion, in its current form the title of the present work is ambivalent in terms of 1) the use of the term "impaired" in the context of cognitively normal individuals, 2) a BMI group difference specifically in the updating condition, and 3) the dopaminergic mechanisms based on observational data

Given the results of the additional post hoc analyses, we agree with the reviewer and have refined the title of our work to be less misleading. The title now reads:     

“Working Memory Gating in Obesity is Moderated by Striatal Dopaminergic Gene Variants” 

Reviewer #1 (Recommendations for the Authors):

Beyond the issues raised in the public review, I recommend the authors adjust the use of pathologizing terminology in the context of a clinically healthy population. In particular, terms like "dopaminergic abnormalities" and "working memory deficits/impairment" seem pathologizing in a healthy, non-morbidly obese cohort. To that end, despite a negative continuous association between BMI and WM, there are high and low-performing individuals in all BMI segments, and group differences (high vs low BMI; not reported) do not seem as dramatic as between healthy controls and say Parkinson's disease patients. Furthermore, owing to the observational design of the present study the authors should pay attention to the use of terms suggesting causal relationships, such as "influence" in the context of statistical associations. Also, sentences like "Our study is the first to show such selective effects" seem problematic not only in terms of claims of primacy, but also in terms of the selectivity of the effects (associations). See the public review for an alternative interpretation of selectivity to updating conditions.   

Of minor importance are the occasional spelling errors, that should be carefully checked by the authors. Also, I would like the authors to double-check the model configurations reported in the main text and the supplementary material. According to the supplement model 1 contains task condition by subject as a random effect (random slope model), whereas the main text states that this model configuration didn't converge and therefore only subject-specific intercepts are included. Hence, there seems to be discordance between the model descriptions in the main text and supplement. To that end, it would seem appropriate to briefly motivate the use of LME and the random effect for subject (within-subject correlation between conditions). Also, the origin of the odds ratios (OR) reported in the results section is not explicitly defined in the methods or results.

We appreciate the reviewer's thoughtful recommendations and have taken several steps to address the concerns raised:

(1) We have revised our manuscript to ensure that the language is less pathologizing and avoids suggesting causal relationships where only associations are indicated.  

For example: 

In the abstract, we replaced “abnormalities” with “alterations”:   

“Dopaminergic alterations have emerged as a potential mediator. However, current models suggest these alterations should only shift the balance in working memory tasks, not produce overall deficits”

In the introduction we replaced “impairments” with “alterations”:               

“This distinction may be crucial, however, as indirect evidence hints at potential specific alteration in these two sub-processes in obesity.

Generally, we took care to replace terms like 'dopaminergic abnormalities' and 'working memory deficits/impairments' with more neutral descriptors suitable for a clinically healthy population in the whole manuscript. 

(2) We have modified primacy statements to be more nuanced. In the discussion, for example, we now say “This finding is compelling as it demonstrates a rarely observed selective effect.” Instead of “This finding is compelling as we are the first to show such selective effects.”

(3) We have conducted an additional thorough review of our manuscript to correct any spelling errors.

(4) Upon reevaluation, we corrected the inconsistencies with respect to the random structure of model 1. We therefore have revised the supplementary material to now accurately reflect that the model did not converge when including condition as a random factor, and thus, only subject-specific intercepts are included.

(5) We have expanded our methods section to better explain the use of linear mixed effects models (LMEs) and the inclusion of random effects for subjects to account for within-subject correlation between conditions. We added the following text:

“Given the within-subject design of our study, we used generalized linear mixed models (GLM) […]” and

“The random structure of the model was thus reduced to include the factor ‘subject’ only, thereby accounting for the repeated measures taken from each subject.”

(6) We have clearly defined the derivation of the odds ratios reported in our results in the methods section of our manuscript. We added the following text to the methods section:

“Reported odds ratios (OR) are retrieved from exponentiating the log-odds coefficients called with the summary() function.”

Reviewer #2 (Public Review):

The majority of participants seem to fall within the normal BMI range, whereas the interaction between BMI and genetic variations or amino acid ratio particularly surfaces at higher BMI. As genetic variations are usually associated with small effect sizes, the effective sample size, although large for a behavioral analysis only, might have been too small to detect meaningful effects of risk alleles of COMT and C957T.

We thank the reviewer for the valuable feedback. We concur that the effective sample size may have posed a limitation in detecting meaningful effects of COMT and C957T, particularly given the skewness of our data towards participants within the normal BMI range. In response to the reviewer’s comments, we have refined the relevant paragraph in the limitations section of our manuscript, emphasizing the importance of recruiting a more balanced sample, including individuals with higher BMI, in future studies.

“Furthermore, an additional limitation is that our data is slightly skewed towards participants within the normal BMI range. The effective sample size to detect meaningful genotype effects (e.g. for COMT or C957T) might thus have been too small, particularly at higher BMI levels. Future studies may address this limitation by recruiting a more balanced sample, including more individuals with higher BMI.”

The relationships between genetic variations, BMI, and specific disturbances in dopamine signaling are complex, as compensating mechanisms might be at play to mitigate any detrimental effects. The results would therefore benefit from more direct measures or manipulations of dopaminergic processes.

We thank the reviewer for this valuable input. We acknowledge the potential benefits of employing a more direct measure, or ideally, a dopaminergic manipulation, to establish a clearer causal link between dopamine processes and working memory gating in the context of obesity. In response to the reviewers' constructive feedback, we have addressed this limitation in the discussion section of our manuscript, emphasizing the need for further research in this area:

“Additionally, the correlational nature of our findings highlights the need for more direct experimental manipulations of dopaminergic processes in obesity. Previous studies have established a causal link between dopamine and WM gating through drug manipulations (Fallon et al., 2017, 2019). Applying a similar approach to an obese sample could help establish a clearer causal link between dopamine activity and WM gating in the context of obesity.”

The introduction could benefit from a more elaborate description of the predicted effects: into which direction (better or worse updating) would the authors predict each effect to go and why? This is clearly explained for COMT, but not for e.g. DARPP-32.

We thank the reviewer for their valuable feedback. We appreciate the suggestion to provide a more detailed description of the predicted effects for each genetic marker in the introduction. We would like to note, however, that the analyses involving markers such as DARPP-32 were inherently exploratory in nature. Consequently, we intentionally refrained from formulating directed hypotheses, as our primary aim was to observe and report any emergent patterns.

Reviewer #2 (Recommendations for the Authors):              

To what extent are the polymorphisms or amino acid ratios associated with BMI? For example, when including C957T polymorphism in the analysis, the detrimental effect of BMI on working memory is no longer statistically significant. Could this be due to a relatively strong relationship between C957T polymorphism and BMI? Could the authors provide figures showing how BMI relates to the genetic polymorphisms and amino acid ratio?

We appreciate the reviewer's insightful comment and have thoroughly investigated the potential relationship between the polymorphism and BMI. Our analysis did not reveal any direct association between C957T and BMI. We have included this analysis in our manuscript. The reviewer’s comment strengthened the comprehensiveness of our study.

“Because the main effect of BMI dissipated when including C957T in the model, we ran an additional exploratory analysis to check whether this polymorphism directly related to BMI. Linear regression, predicting BMI by genotype, showed no association between the two (p = 0.2432), indicating that BMI effect is probably not masked by the presence of the C957T polymorphism. See Table S8.”

eLife assessment

This valuable manuscript reports alterations in autophagy present in dopaminergic neurons differentiated from iPSCs of patients with WDR45 mutations. The authors identified compounds that improved the defects present in mutant cells by generating isogenic iPSC without the mutation and performing an automated drug screening. The methodological approaches are solid, but the claims still need to be completed; showing the effects of the identified compounds on iron-related alterations is crucial. The effects of these drugs in vivo would be a great addition to the study.

Reviewer #1 (Public Review):

In the current study, Papandreou et al. developed an iPSC-based midbrain dopaminergic neuronal cell model of Beta-Propeller Protein-Associated Neurodegeneration (BPAN), which is caused by mutations in the WDR45 gene and is known to impair autophagy. They also noted defective autophagy and abnormal BPAN-related gene expression signatures. Further, they performed a drug screening and identified five cardiac glycosides. Treatment with these drugs effectively in improved autophagy defects and restored gene expression. Seeing the autophagy defects and impaired expression of BPAN-related genes adds strength to this study. Importantly, this work shows the value of iPSC-based modeling in studying disease and finding therapeutic strategies for genetic disorders, including BPAN.

Reviewer #2 (Public Review):

Summary:

In this manuscript, the authors aim to demonstrate that cardiac glycosides restore autophagy flux in an iPSC-derived mDA neuronal model of WDR45 deficiency. They established a patient-derived induced pluripotent stem cell (iPSC)-based midbrain dopaminergic (mDA) neuronal model and performed a medium-throughput drug screen using high-content imaging-based IF analysis. Several compounds were identified that ameliorate disease-specific phenotypes in vitro.

Strengths:

This manuscript engaged in an important topic and yielded some interesting data.

Author response:

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

eLife assessment 

This valuable manuscript reports alterations in autophagy present in dopaminergic neurons differentiated from iPSCs in patients with WDR45 mutations. The authors identified compounds that improved the defects present in mutant cells by generating isogenic iPSC without the mutation and performing an automated drug screening. The methodological approaches are solid, but the claims still need to be completed: showing the effects of the identified compounds on iron-related alterations is crucial. The effects of these drugs in vivo would be a great addition to the study. 

Thank you for this assessment. We agree that further hit validation would be a great addition to the study. At present, we provide this through RNAseq data but not at the protein level. Further validation using in vivo models would also be warranted but is beyond the scope of the current work.

Public Reviews:

Reviewer #1 (Public Review): 

Summary: 

In the current study, Papandreou et al. developed an iPSC-based midbrain dopaminergic neuronal cell model of Beta-Propeller Protein-Associated Neurodegeneration (BPAN), which is caused by mutations in the WDR45 gene and is known to impair autophagy. They also noted defective autophagy and abnormal BPAN-related gene expression signatures. Further, they performed a drug screening and identified five cardiac glycosides. Treatment with these drugs effectively in improved autophagy defects and restored gene expression. 

Strengths: 

Seeing the autophagy defects and impaired expression of BPAN-related genes adds strength to this study. Importantly, this work shows the value of iPSC-based modeling in studying disease and finding therapeutic strategies for genetic disorders, including BPAN. 

Weaknesses: 

It is unclear whether these cells show iron metabolism defects and whether treatment with these drugs can ameliorate the iron metabolism phenotypes. 

We are pleased to ascertain that the reviewer feels the work is an important step in the field for BPAN. We also absolutely agree that secondary hit validation assays showing cardiac glycoside efficacy in restoring patient-related in vitro phenotypes would be very valuable. 

We set up  assays to investigate iron metabolism phenotypes, including  western blotting for Ferritin Heavy Chain 1, Transferrin and Ferroportin 1 (SLC40A1) at day 65 of differentiation, but found no significant difference when comparing patient lines to controls (data not shown). 

We also performed cell viability studies using the Alamar Blue assay on Day 11 ventral midbrain progenitors after 24 hour exposure to a) glucose starvation, b) media with no antioxidants (L-ascorbic acid and B-27 supplement), c) oxidative stressors MPP+ 1mM and FeCl3 100 uM (MPP+ and FeCl3 as suggested by  Seibler et al  (Brain 2018 PMID: 30169597). We found no difference in cell viability between patients, age-matched controls and CRISPR lines (data not shown). Additionally, we examined lysosomal function in BPAN Day 11 progenitors (2 age-matched controls, 3 patient lines, 2 isogenic controls); again, using the autophagy flux treatments mentioned above) via LAMP1 high content imaging immunofluorescence. We have seen no difference in LAMP1 puncta production between patient lines and controls and, therefore, have not included this data in our revision.

Overall, we agree with the reviewer that  more validation of the compound hits’ ability to restore robust BPAN-related in vitro and in vivo phenotypes (including studies of iron metabolism/ homeostasis) will be needed in the future – this could be undertaken in more mature 2D culture systems, 3D organoid models and disease-relevant animal models.

Reviewer #2 (Public Review): 

Summary: 

In this manuscript, the authors aim to demonstrate that cardiac glycosides restore autophagy flux in an iPSC-derived mDA neuronal model of WDR45 deficiency. They established a patientderived induced pluripotent stem cell (iPSC)-based midbrain dopaminergic (mDA) neuronal model and performed a medium-throughput drug screen using high-content imaging-based IF analysis. Several compounds were identified to ameliorate disease-specific phenotypes in vitro. 

Strengths: 

This manuscript engaged in an important topic and yielded some interesting data. 

Weaknesses: 

This manuscript failed to provide solid evidence to support the conclusion. 

We are pleased that the reviewer assesses the work as conceptually important and interesting. We also agree that more work to understand the pathophysiology underpinning BPAN, and the mechanisms through which cardiac glycosides help restore affected intracellular pathways are warranted. More validation of the compound hits’ ability to restore broader disease-specific in vitro and in vivo phenotypes is also needed in future studies. 

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Overall, this is a nicely executed study. Here are my suggestions:

(1) Showing the iron phenotypes in these cells and testing if treatment with these drugs rescues iron-related phenotypes will add significant value to this work. 

We absolutely agree that secondary hit validation assays showing  glycoside efficacy in restoring disease-related in vitro phenotypes is warranted. The main issue here is identifying how WDR45 deficiency leads to cellular dysfunction or dyshomeostasis and early death. Unfortunately, the mechanism by which this happens is not yet delineated, and more relevant future work is needed. 

In our lab, we set up such assays. Regarding iron metabolism-related phenotypes, we performed western blotting for Ferritin Heavy Chain 1, Transferrin and Ferroportin 1 (SLC40A1) but found no significant difference when comparing patient lines to controls (data not shown). We also performed cell viability studies using the Alamar Blue assay on Day 11 ventral midbrain progenitors after 24 hour exposure to a) glucose starvation, b) media with no antioxidants (L-ascorbic acid and B-27 supplement), c) oxidative stressors MPP+ 1mM and FeCl3 100 uM (MPP+ and FeCl3, as suggested by the Seibler et al paper, Brain 2018 PMID: 30169597). We found no difference in cell viability between patients, age-matched controls and CRISPR lines (data not shown). Additionally, we examined lysosomal function in BPAN Day 11 progenitors (2 age-matched controls, 3 patient lines, 2 isogenic controls; again, using the autophagy flux treatments mentioned above) via LAMP1 high content imaging immunofluorescence. We have seen no difference in LAMP1 puncta production between patient lines and controls and, therefore, have not included this data in our revision.

(2) Assessing the effects of these drugs in an in vivo model will strengthen this study. 

This is a valid point, and we agree that further validation using in vivo models such as the reported BPAN mouse models, would be warranted in the future.

Reviewer #2 (Recommendations For The Authors): 

While this manuscript engaged in an important topic and yielded exciting data, there are still some concerns for the authors to address. 

(1) The biggest concern is that the characterization of autophagic flux solely with LC3 is not convincing enough. Although ATG2A and ATG2B are required for phagophore formation during autophagy, their interaction with WDR45 seems dispensable for phagophore formation for a mild autophagy defect observed in WDR45 knockout cell models and mouse models. All wdr45/- mice are born normally and survive the postnatal starvation period, unlike mice lacking essential ATG proteins, like ATG5, ATG7, and VMP1. The functional relevance of WDR45 and autophagy remains to be fully established. Overall, this manuscript failed to provide solid evidence to support the conclusion. 

This is a valid point. We have looked at autophagy flux in fibroblasts and Day 11 ventral midbrain stage. For fibroblasts, 1 control line and three patient lines were used; for Day 11 progenitors, 2 control lines, 2 patient lines and one isogenic control were used. Cells from different lines were cultured on the same 96-well plates, at the same plating density, and treated concurrently to minimise fluctuations in flux due to unaccounted factors, e.g., confluence, incubator temperature etc. Treatments consisted of a) DMSO (basal condition), b) Bafilomycin A1 (flux inhibition via autophagosome/ lysosome fusion blockage), c) Torin A1 (mTOR inhibitor, flux inducer) and d) combination of Bafilomycin A1 and Torin 1, for a total of 3 hours. In all these conditions, LC3 puncta production in BPAN lines was reduced when compared to controls. We believe that these results indicate defective autophagy flux in BPAN in different cell types.

Moreover, we have demonstrated defects in autophagy-related gene (ATG) expression through RNA sequencing, that is restored after CRISPR/Cas9-mediated correction of the disease-causing mutation in a patient derived line, but also after treatments with torin 1 and digoxin. These results suggest a dysregulated ATG network in WDR45 deficiency. 

(2) WDR45 is linked to BPAN. Do the authors detect any iron accumulation in DA progenitors or mDA neurons? 

Regarding iron metabolism-related phenotypes, we performed western blotting for Ferritin Heavy Chain 1, Transferrin and Ferroportin 1 (SLC40A1) but found no significant difference when comparing patient lines to controls (data not shown). We agree that more studies into the links between WDR45 deficiency, iron metabolism and neurodegeneration are needed. 

(3) It is necessary to detect LC3 protein levels by western blot to distinguish LC3I and LC3II and gain a more accurate understanding for the process of LC3 - marked autophagosome. 

Thank you for this valid point. 

Due to the very dynamic nature of autophagy, and many factors influencing flux , we have not been able to meaningfully examine autophagy-related markers in an iPSC-derived system that is also inherently prone to variability.  Therefore, LC3 and p62 values exhibited high variability, and hence we are unable to adequately interpret them (data not shown). Instead, in this manuscript we have focused on high-content assays with cells cultured and treated simultaneously at Day 11 of differentiation, which have shown autophagy flux defects.

We have looked at autophagy flux in fibroblasts and at Day 11 ventral midbrain stage. For fibroblasts, 1 control line and three patient lines were used; for Day 11 progenitors, 2 control lines, 2 patient lines and one isogenic control were used. Cells from different lines were cultured on the same 96-well plates, at the same plating density, and treated concurrently to minimise fluctuations in flux due to unaccounted factors, e.g., confluence, incubator temperature etc. Treatments consisted of a) DMSO (basal condition), b) Bafilomycin A1 (flux inhibition via autophagosome/ lysosome fusion blockage), c) Torin A1 (mTOR inhibitor, flux inducer) and d) combination of Bafilomycin A1 and Torin 1, for a total of 3 hours. In all these conditions, LC3 puncta production in BPAN lines was reduced when compared to controls. We believe that these results indicate defective autophagy flux in BPAN in different cell types.

(4)  Some methodological details need to be included - detailed descriptions of various quantifications for IF staining should be provided. For example, it is unclear how "% cells+ ve for marker combination" (Fig.1B) was quantified, and there are many unconventional units such as "% cells+ ve for marker combination "; please check and correct them. 

Thank you for pointing this out. We have changed the legends in Figure 1B and Supplementary Figure 2C to ‘percentage of cells positive for marker combination’. Moreover, in our Methods section (Immunocytochemistry sub-section), we have updated the text as follows, to give more clarification on the process of marker quantification (Page 25, Paragraph 2): ‘For quantification, 4 random fields were imaged from each independent experiment. Subsequently, 1200 to 1800 randomly selected nuclei were quantified using ImageJ (National Institutes of Health). Manual counting for nuclear (DAPI) staining and co-staining with the marker of interest was performed, and percentages of cells expressing combinations of markers were calculated as needed.’

(5) In Figure 3 and Figure 4, the quantifications for IF images were inconsistent with the shown IF image, for example, the representative IF image for detection of LC3 with Tor1 treatment. 

Due to space restrictions, we have not included representative images from all patient lines, and every treatment condition depicted in the graphs. In Figure 3 (describing the set-up of the LC3 screening assay), only one control line and one patient line is shown in basal (DMSO-treated) conditions. In Supplementary Figure 4D, only one patient line and the corresponding isogenic control line are depicted after Torin 1 treatments.

Quantification of the LC3 puncta in this assay (20 fields per well, each condition in a technical duplicate, n=8 biological replicates) was automated, using ImageJ and R Studio, with subsequent statistical significance calculation on GraphPad Prism. Hence, the immunofluorescence figures depict a reduction in LC3 puncta per nuclei numbers in patient-derived lines versus controls, but not the exact difference after automated image analysis. We have detailed this in the Methods section (High content imaging-based immunofluorescence subsection) of our manuscript (Page 26, Paragraph 2): ‘For all high content imaging-based experiments, the PerkinElmer Opera Phenix microscope was used for imaging. 20 fields were imaged per well, at 40 x magnification, Numerical Aperture 1.1, Binning 1. Image analysis was performed using ImageJ and R Studio.60 For the drug screen, puncta values were normalised according to positive and negative controls from each plate and Z-scores for each compound screened were generated.  Statistical significances were calculated on GraphPad Prism V.

8.1.2. software (GraphPad Software, Inc.; https://www.graphpad.com/scientific-software/prism/).’

(6)  In Figure 4C, LC3 should be co-stain with the DA progenitor maker to indicate that the intercellular LC3 level within the projectors. 

Thank you for raising this point. The images from Figure 4C were obtained during the medium throughput drug screen, where the FOXA2 co-stain was not used. The FOXA2 stain was only used during the initial set-up of the LC3 screening assay, to confirm that the Day 11 cells had ventral midbrain identities. Indeed, most of the Day 11 cells used in the high content imaging-related experiments were FOXA2-positive, as shown in Figure 3 and Supplementary Figure 4.

(7) Examining P62, one of the most important indicators for autophagic flux, should be parallel with LC3 detection. In Figure 5A, P62 accumulation seems not significant in patient 02 Day 11 ventral midbrain projectors; how about that in Day 65? 

The reviewer is raising a valid point. We have not examined p62 and LC3 staining in parallel in high content imaging-based experiments but agree that this would be good to examine in future studies. 

Some other minor points 

(8) It needs to give a more detailed description of the tested compounds you mentioned in the text. 

Thank you for this point. We have elaborated on the contents of the Prestwick library used for the screening, as below (Page 9, Paragraph 3): ‘We then utilised this high-content imaging LC3 assay to identify novel compounds of potential therapeutic interest for BPAN by screening the Prestwick Chemical Library containing 1,280 compounds, of which more than 95% FDA/ EMA approved.’

In the Methods Section, Page 25, Paragraph 5, we also detail the library as follows: ‘For drug screening, the Prestwick Chemical Library (1,280 compounds, 95% FDA/ EMA approved, 10 mM in DMSO, https://www.prestwickchemical.com/screening-libraries/prestwick-chemical-library/) was used; cells were treated with compounds for 24 hours at 10 μM final concentration.’

(9) Please pay attention to the abbreviation; many gene names only have abbreviations without full names when they first appear in the context. 

Thank you for this point. We have corrected this in various places throughout the manuscript and especially in the introduction section.

(10) Almost all figures have the problem of insufficient image resolution, or the font of the indicated words needs to be bigger to be distinguished clearly, like in Fig.1B, 1C, 1E. 

Thank you for this point, we have ensured that all figures have adequate image resolution as specified by the journal requirements. 

(11) The sample size or biological repeated times should be given in figure legends. 

Thank you for this point. We have now indicated numbers of biological replicates where appropriate.

eLife assessment

The aim of this valuable study is to identify novel genes involved in sleep regulation and memory consolidation. It combines transcriptomic approaches following memory induction with measurements of sleep and memory to discover molecular pathways underlying these interlinked behaviors. The authors explore transcriptional changes in specific mushroom body neurons and suggest roles for two genes involved in RNA processing, Polr1F and Regnase-1, in the regulation of sleep and memory. Although this work exploits convincing and validated methodology, the strength of the evidence is incomplete to support the main claim that these two genes establish a definitive link between sleep and memory consolidation.

Reviewer #2 (Public review):

Prior work by the Sehgal group has shown that a small group of neurons in the fly brain (anterior posterior (ap) α'β' mushroom body neurons (MBNs)) promote sleep and sleep-dependent appetitive memory specifically under fed conditions (Chouhan et al., (2021) Nature). Here, Li, Chouhan et al. combine cell-specific transcriptomics with measurements of sleep and memory to identify molecular processes underlying this phenomenon. They define transcriptional changes in ap α'β' MBNs and suggest a role for two genes downregulated following memory induction (Polr1F and Regnase-1) in regulating sleep and memory.

The transcriptional analyses in this manuscript are impressive. The authors have now included additional experiments that define acute and developmental roles for Polr1F and Regnase-1 respectively in regulating sleep. They have also provided additional data to strengthen their conclusion that Polr1F knockdown in α'β' mushroom body neurons enhances sleep.

The resubmitted work represents a convincing investigation of two novel sleep-regulatory proteins that may also play important roles in memory formation.

The authors have comprehensively addressed my comments, which I very much appreciate. I congratulate them on this excellent work.

Reviewer #3 (Public review):

Previous work (Chouhan et al., 2022) from the Sehgal group investigated the relationship between sleep and long-term memory formation by dissecting the role of mushroom body intrinsic neurons, extrinsic neurons, and output neurons during sleep-dependent and sleep-independent memory consolidation. In this manuscript, Li et al., profiled transcriptome in the anterior-posterior (ap) α'/β' neurons and identified genes that are differentially expressed after training in fed condition, which supports sleep-dependent memory formation. By knocking down candidate genes systematically, the authors identified Polr1F and Regnase-1 as two important hits that play potential roles in sleep and memory formation. What is the function of sleep and how to create a memory are two long-standing questions in science. The present study used a new approach to identify novel components that may link sleep and memory consolidation in a specific type of neuron. Importantly, these components implicated that RNA processing may play a role in these processes.

While I am enthusiastic about the innovative approach employed to identify RNA processing genes involved in sleep regulation and memory consolidation, I feel that the data presented in the manuscript is insufficient to support the claim that these two genes establish a definitive link between sleep and memory consolidation. First, the developmental role of Regnase-1 in reducing sleep remains unclear because knocking down Regnase-1 using the GeneSwitch system produced neither acute nor chronic sleep loss phenotype. In the revised manuscript, the author used the Gal80ts to restrict the knockdown of Regnase-1 in adult animals and concluded that Regnase-1 RNAi appears to affect sleep through development. Conducting overexpression experiments of Regnase-1 would lend some credibility to the phenotypes, however, this is not pursued in the revised manuscript. Second, while constitutive Regnase-1 knockdown produced robust phenotypes for both sleep-dependent and sleep-independent memory, it also led to a severe short-term memory phenotype. This raises the possibility that flies with constitutive Regnase-1 knockdown are poor learners, thereby having little memory to consolidate. The defect in learning could be simply caused by chronic sleep loss before training. Thus, this set of results does not substantiate a strong link between sleep and long-term memory consolidation. Lastly, the discussion on the sequential function of training, sleep, and RNA processing on memory consolidation appears speculative based on the present data.

Reviewer #4 (Public review):

Summary:

Li and Chouhan et al. follow up on a previous publication describing the role of anterior-posterior (ap) and medial (m) ɑ′/β′ Kenyon cells in mediating sleep-dependent and sleep-independent memory consolidation, respectively, based on feeding state in Drosophila melanogaster. The authors sequenced bulk RNA of ap ɑ′/β′ Kenyon cells 1h after flies were either trained-fed, trained-starved or untrained-fed and find a small number of genes (59) differentially expressed (3 upregulated, 56 downregulated) between trained-fed and trained-starved conditions. Many of these genes encode proteins involved in the regulation of gene expression. The authors then screened these differentially expressed genes for sleep phenotypes by expressing RNAi hairpins constitutively in ap ɑ′/β′ Kenyon cells and measuring sleep patterns. Two hits were selected for further analysis: Polr1F, which promoted sleep, and Regnase-1, which reduced sleep. The pan-neuronal expression of Polr1F and Regnase-1 RNAi constructs was then temporally restricted to adult flies using the GeneSwitch system. Polr1F sleep phenotypes were still observed, while Regnase-1 sleep phenotypes were not, indicating developmental defects. Appetitive memory was then assessed in flies with constitutive knockdown of Polr1F and Regnase-1 in ap ɑ′/β′ Kenyon cells. Polr1F knockdown did not affect sleep-dependent or sleep-independent memory, while Regnase-1 knockdown disrupted sleep-dependent memory, sleep-independent memory, as well as learning. Polr1F knockdown increased pre-ribosomal RNA transcripts in the brain, as measured by qPCR, in line with its predicted role as part of the RNA polymerase I complex. A puromycin incorporation assay to fluorescently label newly synthesized proteins also indicated higher levels of bulk translation upon Polr1F knockdown. Regnase-1 knockdown did not lead to observable changes in measurements of bulk translation.

Strengths:

The proposed involvement of RNA processing genes in regulating sleep and memory processes is interesting, and relatively unexplored. The methods are satisfactory.

Weaknesses:

The main weakness of the paper is in the overinterpretation of their results, particularly relating to the proposed link between sleep and memory consolidation, as stated in the title. Constitutive Polr1F knockdown in ap ɑ′/β′ Kenyon cells had no effect on appetitive long-term memory, while constitutive Regnase-1 knockdown affected both learning and memory. Since the effects of constitutive Regnase-1 knockdown on sleep could be attributed to developmental defects, it is quite plausible that these same developmental defects are what drive the observed learning and memory phenotypes. In this case, an alternative explanation of the authors' findings is that constitutive Regnase-1 knockdown disrupts the entire functioning of ap ɑ′/β′ Kenyon cells, and as a consequence behaviors involving these neurons (i.e. learning, memory and sleep) are disrupted. It will be important to provide further evidence of the function of RNA processing genes in memory in order to substantiate the memory link proposed by the authors.

Author response:

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

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Below, I will list the points that should be addressed by the authors:

(1) Line 139: The authors conclude that the lack of a phenotype induced by knockdown of Polr1F is due to reduced baseline sleep because of the leakiness of the Genswitch system. However, it is not clear why the argument of the SybGS being leaky should not apply to all experiments done with this tool. The authors should comment on that aspect. Furthermore, this claim is testable since it should be detectable against genetic controls. An alternative explanation to the proposed scenario is that the Polr1F sleep phenotype observed in the constitutive knockdown experiment is based on developmental defects. The authors should provide additional evidence to explain the discrepancy.

We appreciate the reviewer’s insightful feedback. We assume the reviewer is referring to Regnase-1 RNAi (and not Polr1F) as Regnase-1 RNAi flies exhibit reduced sleep before dusk, potentially hindering further detection of sleep reduction. The leaky sleep reduction was based upon comparison with genetic controls in that experiment. Nevertheless, to discern whether our observations stem from developmental effects, we conducted adult-specific knockdowns of both Polr1F and Regnase-1 using the TARGET system. We generated the R35B12-Gal4:TubGal80ts line and crossed it with the UAS-Polr1FRNAi and UAS-Regnase-1RNAi lines. We confirmed that Polr1F RNAi promotes sleep when knocked down in adults (Figure 3 - supplemental figure 1). Conversely, Regnase-1 showed no effect on sleep in the adult stage, which is consistent with our nSyb-GS experiments, and suggests, as noted by the reviewer, that the Regnase-1 RNAi sleep effect is likely developmental (Figure 3 – supplemental figure 3).

(2) Line 170: Regnase1 knockdown affects all memory types, including short-term and long-term memory. The authors conclude that these genes are involved in consolidation. However, besides consolidation, it has been shown that α′β′ KCs are involved in short-term appetitive memory retrieval. Thus, an equally possible explanation is that the knockdown impairs the neuronal function per se, which would lead to a defect in all behaviors related to α′β′ KCs, rather than a specific role for consolidation. The authors have to provide additional evidence to substantiate their claim.

The exact role of Regnase-1 in the α′β′ KCs remains unclear.  We acknowledge the reviewer’s concern and have amended our conclusion to include this potential explanation suggested by the reviewer.

(3) Line 87-88: For the protocol used, it was reported that GFPnls cannot be used for FACS sorting. The authors might want to comment/clarify that aspect. https://star-protocols.cell.com/protocols/1669.

For our RNA-seq experiments, we conducted single cell isolation by FACS sorting cells, instead of nuclei, labeled with GFP.nls. The protocol mentioned that GFP.nls is not effective for single nuclear RNA-seq as it is not specific for nuclei, but for our cell sorting purposes that did not matter.

(4) Line 131: The authors should report the concentration of RU486.

Sorry, this is now in methods.

(5) Line 155: Is that really 42 hours? This might be a typo. If not, it would be good to justify the prolonged re-starvation period.

Flies fed after training form sleep-dependent memories but did not show robust long-term memory after 30 h of restarvation. As starvation is a requisite for appetitive memory retrieval (Krashes and Waddell 2008), the low memory scores after 30 h could be due to inadequate starvation. Therefore, we starved flies for 42h, which is similar to the sleep-independent memory paradigm in which flies are starved for 18 h before training and then tested 24 h after training; this protocol resulted in robust long-term memory performance. These flies were fine and able to make choices in a T-maze after 42 h starvation.

(6) I will be listing mistakes/unclear points in the figures. However, all figures should be checked very carefully for clarity.

Thanks for these valuable comments. We have gone over the figures carefully and fixed any issues we found.

(7) Figure 1C: It is not entirely clear to me how this heatmap was created and what the values mean.

The 59 differentially expressed genes (DEGs) were selected based on DESeq2 described in the methods. For the heatmap, Transcripts per million (TPM) of these 59 DEGs were log-transformed and then scaled row-wise and plotted with IDEP v0.95 (http://bioinformatics.sdstate.edu/idep95/).

(8) Figures 2A and 2B: The units might be missing. For Supplementary Figure 2, it is not clear what the different groups are without looking at the main figure.

Fixed.

(9) Figure 3: The panel arrangement is confusing. Furthermore, the "B)" is cut. The same issue is present in the Supplementary Figure.

Sorry! We rearranged the panels, and fixed the issue in both figures.

(10) Figure 5B: It is not clear what the scale bar means.

Now indicated

(11) Line 119: The citation "Marygold et al n.d."?

Fixed

(12) Line 620: I'm not sure that the rate and localization of nascent peptide synthesis are measured.

Great point. We used the puromycin assay to estimate significant changes in translation. However, we did not measure the absolute translational rate or the localization of newly synthesized proteins. We rephrased this in the updated manuscript.

(13) Line 627, the authors should give the NA of the objective, further the authors should double-check the information they provide on the resolution.

Fixed, it was 20X.

(14) Line 629 "Fuji" is unclear, it might refer to the Fiji software, and in that case, it should be listed in the used software. Further, the authors have to check on the information they provide on the intensity, e.g. is that GFP fluorescence?

Yes, it was Fiji and GFP. The manuscript has been updated accordingly.

(15) Line 634, It is stated that two concentrations of CX-5461 are used, however, as far as I can see only data for the 0.2 mM.

We apologize for the confusion. Data are indeed only shown for 0.2 mM. We also tested 0.4 mM and 0.6 mM under fed conditions once and 0.1 mM under starved conditions twice. Since all effects were not significant, we only presented the complete 0.2 mM results in the supplementary figure.

(16) Line 352 "Marygold et al nd" is probably a glitch in the citation?

It’s a citation tool issue and has been fixed.

(17) The authors use apostrophe rather than a prime in describing the α "prime" β "prime" KCs

We have corrected this.

Reviewer #2 (Recommendations For The Authors):

The authors have generated an interesting study that promises to advance the understanding of how context-dependent changes in sleep and memory are executed at the molecular level. The manuscript is well-written and the statistical analyses appear robust. Major and minor comments are detailed below.

Overall, I would suggest that the authors try to obtain additional evidence that Pol1rF modulates sleep and test the effect of acute adult-stage knockdown of Polr1F and Regnase-1 specifically in ap α'β' MBNs rather than pan-neuronally.

Major comments

(1) In Figures 2 and 3 and associated supplemental figures, the authors first test for a role for Polr1F and Regnase-1 specifically in ap α'β' MBNs (Fig. 2), then test for an acute role for these proteins via pan-neuronal drug inducible expression (Fig. 3). Because the former manipulation is cell-specific and the latter is pan-neuronal, it is hard for the reader to draw conclusions pertaining to ap α'β' MBNs from the second dataset. Perhaps Regnase-1 indeed acutely regulates sleep in ap α'β' MBNs, but that effect is masked by counteracting roles in other neurons? Conversely, it remains possible that Polr1F and Regnase-1 act during development in ap α'β' MBNs to modulate sleep. Indeed, since silencing the output of ap α'β' MBNs using temperature-sensitive shibire does not alter baseline sleep (Chouhan et al., (2021) Nature), the notion that Regnase-1 could act acutely in ap α'β' MBNs to reduce baseline sleep is somewhat surprising.

The authors could address this by using a method such as TARGET (temperature-sensitive GAL80) to acutely reduce Polr1F and Regnase-1 expression specifically in ap α'β' MBNs and test how this impacts sleep.

Thanks for the very helpful suggestions. We have done the suggested experiments and discuss them above in response to Reviewer 1. They are included in the manuscript as Figure 3 – supplemental figure 1 and figure 3 – supplemental figure 3.

(2) Figure 4 presents data examining whether Polr1F and Regnase-1 knockdown suppresses training-induced increases in sleep. For the untrained flies, based on the data in Fig. 2C, E I expected that Polr1F knockdown flies would exhibit more sleep than their respective controls (Fig. 4E), but this was not the case. These data suggest that more evidence may be warranted to strengthen the link between Polr1F (and potentially Regnase-1) knockdown and sleep. Could the authors use independent RNAi constructs or cell-specific CRISPR (all available from current stock centres) to validate their current results? Related to this, it would be useful to know whether the authors outcrossed any of their transgenic reagents into a defined genetic background.

The untrained flies in figure 4E are not equivalent to flies tested for Polr1F effects on sleep in figure 2C. In Figure 4E, flies were starved for 18 h and then exposed to sucrose without an odor at ZT6. Following sucrose exposure, flies were moved to sucrose locomotor tubes, and sleep was assessed only in the ZT8-12 interval. Sleep was not significantly different between untrained R35B12>Polr1FRNAi and Polr1FRNAi/+ flies, and while it was higher in R35B12>Polr1FRNAi than in R35B12/+ untrained flies, the data overall indicate that Polr1F downregulation has no impact on sleep under these conditions and at this time. Similarly, in fully satiated settings (Figure 2C), we found no difference in sleep during the ZT8-12 period between R35B12>Polr1FRNAi flies and genetic controls. We did not outcross our transgenic lines but have now tested another available Polr1F RNAi (VDRC: v103392) (Figure 3 – supplemental figure 1). As shown in the figure, adult-specific knockdown of Polr1F by this RNAi line promoted sleep, as did the initial RNAi line.

(3) Could the authors provide additional evidence that Polr1F knockdown in ap α'β' MBNs does not enhance sleep by reducing movement? A separate assay such as climbing would be beneficial. Alternatively, examining peak activity levels at dawn/dusk from the 12L: 12D DAM data.

We checked the peak activity per minute per day for adult specific knockdown of PorlF1 and Regnase-1 (data shown in Figure 3 – supplemental figure 4). The results show that Polr1F knockdown in ap α'β' MBNs does not enhance sleep by reducing movement.

(4) In terms of validating their proposed model, over-expressing of Polr1F during appetitive training might be predicted to suppress training-induced sleep increases and potentially long-term memory. Do the authors have any evidence for this?

We were unable to find any Pol1rF overexpression line. However, we obtained the Regnase-1 over-expression line from Dr. Ryuya Fukunaga’s lab and found that Regnase-1 OE does not affect sleep (Figure 4 – supplemental figure 1).

Minor comments

(1) Abstract: can the authors please define 'ap' as anterior posterior?

Fixed.

(2) Figure 2 Supplemental 1: can the authors please denote the genotypes each color refers to in?

Fixed.

(3) In Figure 3 Supplemental 1, the authors state that acute Regnase-1 knockdown did not reduce sleep, but sleep during the night period does appear to be reduced (panel A). Was this quantified?

We quantified this, and it was not significant.

(4) Discussion, line 234: the heading of this section is 'Polr1F regulates ribosome RNA synthesis and memory' but the data presented in Figure 4 suggests that Polr1F does not affect memory. Can the authors clarify this?

We made an adjustment to the title and acknowledge that at the present time we cannot say Polr1F affects memory.

(5) Methods, Key Resource Table: can the authors please identify which fly lines were used for Polr1F and Regnase-1 knockdown experiments?

Fixed. Fly line BDSC64553 was used for Polr1F RNAi except in Figure 3 – supplemental figure 1 and 4, where VDRC 103392 was used. VDRC 27330 was used for Regnase-1 knockdown experiments.

Reviewer #3 (Recommendations For The Authors):

(1) Figure 1B: This plot is currently labelled as PCA of DEGs, which I believe is inaccurate, as such a plot is a quality control that examines the overall clustering of samples by using all read counts (not just the DEGs). In addition, the color key value of this Figure 1B is not provided.

Thank you for the insightful suggestion. The reviewer’s comment here that typically PCA plots are used for overall clustering of RNA-seq samples is indeed valid. We've acknowledged that our samples, due to their high similarity in cell populations and mild treatments, do not exhibit clear separation when we use all genes. However, we show a PathwayPCA plot of all DEGs. We aim to highlight that RNA processing pathways enriched among the DEGs account for much of the separation of the groups.

(2) A reviewer token is not provided to examine the sequencing data set.

The RNA-seq data has been submitted to the Sequence Read Archive (SRA) with NCBI BioProject accession number PRJNA1132369. The reviewer token is https://dataview.ncbi.nlm.nih.gov/object/PRJNA1132369?reviewer=cvqkddp8rjuebsjefk0f19556r.

(3) In the discussion, the author pointed out that many of the 59 DEGs have implicated functions in RNA processing. To strengthen the statement, it would be beneficial to conduct the Gene Ontology analysis to test whether the DEGs are enriched for RNA processing-related GO terms.

We have included the GO analysis results in Figure1 and another GO analysis of all DEGs in Figure 1 – supplemental figure 1.

(4) Figure 4E presents an intriguing finding because it shows that the untrained R35B12>Polr1FRNAi flies exhibit reduced sleep (instead of increased sleep) when compared to untrained Polr1/+ control flies.

Please see above response to reviewer #2 question2.

(5) For the memory assay method, the identity of odor A and odor B is not provided.

We used 4-methylcyclohexanol and 3-octanol; this information has been added into the methods section.

(6) Female flies were used for the sleep assay. However, it is not clear whether only female flies were used for the memory assay.

Mixed sexes are used for memory assays because a huge number of files is needed for these experiments. We added this information in the methods.

(7) It is important to provide olfactory acuity data on control and experimental animals to rule out that the learning/memory phenotype is caused by defects in sensing the odor used for training and testing.

Since Polr1F RNAi flies perform well, odor acuity is not an issue. Regnase1RNAi affects both short-term and long-term memories, but this seems to be a developmental issue, so we did not do the odor acuity experiments here.

(8) Line 20: "ap alpha'/beta'" neurons should be spelled as "anterior posterior (ap) alpha'/beta' neurons", as this is the first time that this anatomical name appears in this manuscript.

Fixed.

(9) Figure 2C and 2D labelling: R35B12>control; UAS control should be changed to R35B12/+ control; UAS-RNAi/+ control.

Fixed.

(10) Line 155: it is unclear why the flies were re-starved for 42hr before testing. Is this a different protocol from the 30hr re-starvation that was used by Chouhan et al., 2021?

We have explained the rationale above. The starvation period was increased to get better memory scores.

(11) Line 160: it is stated that knocking down Polr1F did not affect memory, which is consistent with Polr1f levels typically decreasing during memory consolidation. Is there a reference demonstrating that Polr1f levels typically decrease during memory consolidation?

It’s from our RNA-seq dataset from Figure1C. The level of Polr1F decreased in fed trained flies compared with other control flies.

(12)  Genotype labeling in Figure 4F is inconsistent with the rest of the manuscript.

Fixed.

eLife assessment

Through anchored phylogenomic analyses, this important study offers fresh insights into the evolutionary history of the plant diet and geographic distribution of Belidae weevil beetles. Employing robust methodological approaches, the authors propose that certain belid lineages have maintained a continuous association with Araucaria hosts since the Mesozoic era. Although the biogeographical analysis is somewhat limited by uncertainties in vicariance explanations, this convincing study enhances our understanding of Belidae's evolutionary dynamics and provides new perspectives on ancient community ecology.

Reviewer #1 (Public review):

This is a very nice study of Belidae weevils using anchored phylogenomics that presents a new backbone for the family and explores, despite a limited taxon sampling, several evolutionary aspects of the group. I find that the methodology is appropriate, and all analytical steps are well presented. The paper is well written and presents interesting aspects of Belidae systematics and evolution. The major weakness of the study being the very limited taxon sampling that has deep implications for the discussion of ancestral estimations.

Reviewer #2 (Public review):

Summary:

The authors used a combination of anchored hybrid enrichment and Sanger sequencing to construct a phylogenomic data set for the weevil family Belidae. Using evidence from fossils and previous studies they are able to estimate a phylogenetic tree with a range of dates for each node - a timetree. They use this to reconstruct the history of the belids' geographic distributions and associations with their hostplants. They infer that the belids' association with conifers pre-dates the rise of the angiosperms. They offer an interpretation of belid history in terms of the breakup of Gondwanaland, but acknowledge that they cannot rule out alternative interpretations that invoke dispersal.

Strengths:

The strength of any molecular-phylogenetic study hinges on four things: the extent of the sampling of taxa; the extent of the sampling of loci (DNA sequences) per genome; the quality of the analysis; and - most subjectively - the importance and interest of the evolutionary questions the study allows the authors to address. The first two of these, sampling of taxa and loci, impose a tradeoff: with finite resources, do you add more taxa or more loci? The authors follow a reasonable compromise here, obtaining a solid anchored-enrichment phylogenomic data set (423 genes, >97 kpb) for 33 taxa, but also doing additional analyses that included 13 additional taxa from which only Sanger sequencing data from 4 genes was available. The taxon sampling was pretty solid, including all 7 tribes and a majority of genera in the group. The analyses also seemed to be solid - exemplary, even, given the data available.

This leaves the subjective question of how interesting the results are. The very scale of the task that faces systematists in general, and beetle systematists in particular, presents a daunting challenge to the reader's attention: there are so many taxa, and even a sophisticated reader may never have heard of any of them. Thus it's often the case that such studies are ignored by virtually everyone outside a tiny cadre of fellow specialists. The authors of the present study make an unusually strong case for the broader interest and importance of their investigation and of its focal taxon, the belid weevils.

The belids are of special interest because - in a world churning with change and upheaval, geologically and evolutionarily - relatively little seems to have been going on with them, at least with some of them, for the last hundred million years or so. The authors make a good case that the Araucaria-feeding belid lineages found in present-day Australasia and South America have been feeding on Araucaria continuously since the days when it was a dominant tree taxon nearly worldwide, before it was largely replaced by angiosperms. Thus these lineages plausibly offer a modern glimpse of an ancient ecological community.

Comments on current version:

The MS was already in pretty good shape last time around, and the authors have made most of the minor revisions and copy-edits suggested by the reviewers. There may be a few remaining points of disagreement with the reviewers, but these seem to be minor matters of opinion and nothing that ought to delay publication.