Author response:

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

Public Reviews (consolidated):

In the microglia research community, it is accepted that microglia change their shape both gradually and acutely along a continuum that is influenced by external factors both in their microenvironments and in circulation. Ideally, a given morphological state reflects a functional state that provides insight into a microglia's role in physiological and pathological conditions. The current manuscript introduces MorphoCellSorter, an open-source tool designed for automated morphometric analysis of microglia. This method adds to the many programs and platforms available to assess the characteristics of microglial morphology; however, MorphoCellSorter is unique in that it uses Andrew's plotting to rank populations of cells together (in control and experimental groups) and presents "big picture" views of how entire populations of microglia alter under different conditions. Notably, MorphoCellSorter is versatile, as it can be used across a wide array of imaging techniques and equipment. For example, the authors use MorphoCellSorter on images of fixed and live tissues representing different biological contexts such as embryonic stages, Alzheimer's disease models, stroke, and primary cell cultures.

This manuscript outlines a strategy for efficiently ranking microglia beyond the classical homeostatic vs. active morphological states. The outcome offers only a minor improvement over the already available strategies that have the same challenge: how to interpret the ranking functionally.

We would like to thank the reviewers for their careful reading and constructive comments and questions. While MorphoCellSorter currently does not rank cells functionally based on their morphology, its broad range of application, ease of use and capacity to handle large datasets provide a solid foundation. Combined with advances in single-cell transcriptomics, MorphoCellSorter could potentially enable the future prediction of cell functions based on morphology.

Strengths and Weaknesses:

(1) The authors offer an alternative perspective on microglia morphology, exploring the option to rank microglia instead of categorizing them with means of clusterings like k-means, which should better reflect the concept of a microglia morphology continuum. They demonstrate that these ranked representations of morphology can be illustrated using histograms across the entire population, allowing the identification of potential shifts between experimental groups. Although the idea of using Andrews curves is innovative, the distance between ranked morphologies is challenging to measure, raising the question of whether the authors oversimplify the problem.

We have access to the distance between cells through the Andrew’s score of each cell. However, the challenge is that these distances are relative values and specific to each dataset. While we believe that these distances could provide valuable information, we have not yet determined the most effective way to represent and utilize this data in a meaningful manner.

Also, the discussion about the pipeline's uniqueness does not go into the details of alternative models.The introduction remains weak in outlining the limitations of current methods (L90). Acknowledging this limitation will be necessary.

Thank you for these insightful comments. The discussion about alternative methods was already present in the discussion L586-598 but to answer the request of the reviewers, we have revised the introduction and discussion sections to more clearly address the limitations of current methods, as well as discussed the uniqueness of the pipeline. Additionally, we have reorganized Figure 1 to more effectively highlight the main caveats associated with clustering, the primary method currently in use.

(2) The manuscript suffers from several overstatements and simplifications, which need to be resolved. For example:

a)  L40: The authors talk about "accurately ranked cells". Based on their results, the term "accuracy" is still unclear in this context.

Thank you for this comment. Our use of the term "accurately" was intended to convey that the ranking was correct based on comparison with human experts, though we agree that it may have been overstated. We have removed "accurately" and propose to replace it with "properly" to better reflect the intended meaning.

b) L50: Microglial processes are not necessarily evenly distributed in the healthy brain. Depending on their embedded environment, they can have longer process extensions (e.g., frontal cortex versus cerebellum).

Thank you for raising this point to our attention. We removed evenly to be more inclusive on the various morphologies of microglia cells in this introductory sentence

c)  L69: The term "metabolic challenge" is very broad, ranging from glycolysis/FAO switches to ATP-mediated morphological adaptations, and it needs further clarification about the author's intended meaning.

Thank you for this comment, indeed we clarified to specify that we were talking about the metabolic challenge triggered by ischemia and added a reference as well.

d) L75: Is morphology truly "easy" to obtain?

Yes, it is in comparison to other parameters such as transcripts or metabolism, but we understand the point made by the reviewer and we found another way of writing it. As an alternative we propose: “morphology is an indicator accessible through…”

e) L80: The sentence structure implies that clustering or artificial intelligence (AI) are parameters, which is incorrect. Furthermore, the authors should clarify the term "AI" in their intended context of morphological analysis.

We apologize for this confusing writing, we reformulated the sentence as follows: “Artificial intelligence (AI) approaches such as machine learning have also been used to categorize morphologies (Leyh et al., 2021)”.

f) L390f: An assumption is made that the contralateral hemisphere is a non-pathological condition. How confident are the authors about this statement? The brain is still exposed to a pathological condition, which does not stop at one brain hemisphere.

We did not say that the contralateral is non-pathological but that the microglial cells have a non-pathological morphology which is slightly different. The contralateral side in ischemic experiments is classically used as a control (Rutkai et al 2022). Although It has been reported that differences in transcript levels can be found between sham operated animals and contralateral hemisphere in tMCAO mice (Filippenkov et al 2022) https://doi.org/10.3390/ijms23137308 showing that indeed the contralateral side is in a different state that sham controls, no report have been made on differences in term of morphology.

We have removed “non-pathological” to avoid misinterpretations

g)  Methodological questions:

a) L299: An inversion operation was applied to specific parameters. The description needs to clarify the necessity of this since the PCA does not require it.

Indeed, we are sorry for this lack of explanation. Some morphological indexes rank cells from the least to the most ramified, while others rank them in the opposite order. By inverting certain parameters, we can standardize the ranking direction across all parameters, simplifying data interpretation. This clarification has been added to the revised manuscript as follows:

“Lacunarity, roundness factor, convex hull radii ratio, processes cell areas ratio and skeleton processes ratio were subjected to an inversion operation in order to homogenize the parameters before conducting the PCA: indeed, some parameters rank cells from the least to the most ramified, while others rank them in the opposite order. By inverting certain parameters, we can standardize the ranking direction across all parameters, thus simplifying data interpretation.”

b) Different biological samples have been collected across different species (rat, mouse) and disease conditions (stroke, Alzheimer's disease). Sex is a relevant component in microglia morphology. At first glance, information on sex is missing for several of the samples. The authors should always refer to Table 1 in their manuscript to avoid this confusion. Furthermore, how many biological animals have been analyzed? It would be beneficial for the study to compare different sexes and see how accurate Andrew's ranking would be in ranking differences between males and females. If they have a rationale for choosing one sex, this should be explained.

As reported in the literature, we acknowledge the presence of sex differences in microglial cell morphology. Due to ethical considerations and our commitment to reducing animal use, we did not conduct dedicated experiments specifically for developing MorphoCellSorter. Instead, we relied on existing brain sections provided by collaborators, which were already prepared and included tissue from only one sex—either female or male—except in the case of newborn pups, whose sex is not easily determined. Consequently, we were unable to evaluate whether MorphoCellSorter is sensitive enough to detect morphological differences in microglia attributable to sex. Although assessing this aspect is feasible, we are uncertain if it would yield additional insights relevant to MorphoCellSorter’s design and intended applications.

To address this, we have included additional references in Table 1 of the revised manuscript and clearly indicated the sex of the animals from which each dataset was obtained.

c) In the methodology, the slice thickness has been given in a range. Is there a particular reason for this variability?

We could not spot any range in the text, we usually used 30µm thick sections in order to have entire or close to entire microglia cells.

Although the thickness of the sections was identical for all the sections of a given dataset, only the plans containing the cells of interest were selected during the imaging for both of the ischemic stroke model. This explains why depending on how the cell is distributed in Z the range of the plans acquired vary.

Also, the slice thickness is inadequate to cover the entire microglia morphology. How do the authors include this limitation of their strategy? Did the authors define a cut-off for incomplete microglia?

We found that 30 µm sections provide an effective balance, capturing entire or nearly entire microglial cells (consistent with what we observe in vivo) while allowing sufficient antibody penetration to ensure strong signal quality, even at the section's center. In our segmentation process, we excluded microglia located near the section edges (i.e., cells with processes visible on the first or last plane of image acquisition, as well as those close to the field of view’s boundary). Although our analysis pipeline should also function with thicker sections (>30 µm), we confirmed that thinner sections (15 µm or less) are inadequate for detecting morphological differences, as tested initially on the AD model. Segmented, incomplete microglia lack the necessary structural information to accurately reflect morphological differences thus impairing the detection of existing morphological differences.

c) The manuscript outlines that the authors have used different preprocessing pipelines, which is great for being transparent about this process. Yet, it would be relevant to provide a rationale for the different imaging processing and segmentation pipelines and platform usages (Supplementary Figure 7). For example, it is not clear why the Z maximum projection is performed at the end for the Alzheimer's Disease model, while it's done at the beginning of the others.

The same holds through for cropping, filter values, etc. Would it be possible to analyze the images with the same pipelines and compare whether a specific pipeline should be preferable to others?

The pre-processing steps depend on the quality of the images in each dataset. For example, in the AD dataset, images acquired with a wide-field microscope were considerably noisier compared to those obtained via confocal microscopy. In this case, reducing noise plane-by-plane was more effective than applying noise reduction on a Z-projection, as we would typically do for confocal images. Given that accurate segmentation is essential for reliable analysis in MorphoCellSorter, we chose to tailor the segmentation approach for each dataset individually. We recommend future users of MorphoCellSorter take a similar approach. This clarification has been added to the discussion.

On a note, Matlab is not open-access,

This is correct. We are currently translating this Matlab script in Python, this will be available soon on Github. https://github.com/Pascuallab/MorphCellSorter.

This also includes combining the different animals to see which insights could be gained using the proposed pipelines.

Because of what we have been explaining earlier, having a common segmentation process for very diverse types of acquisitions (magnification, resolution and type of images) is not optimal in terms of segmentation and accuracy in the analysis. Although we could feed MorphoCellSorter with all this data from a unique segmentation pipeline, the results might be very difficult to interprete.

d) L227: Performing manual thresholding isn't ideal because it implies the preprocessing could be improved. Additionally, it is important to consider that morphology may vary depending on the thresholding parameters. Comparing different acquisitions that have been binarized using different criteria could introduce biases.

As noted earlier, segmentation is not the main focus of this paper, and we leave it to users to select the segmentation method best suited to their datasets. Although we acknowledge that automated thresholding would be in theory ideal, we were confronted toimage acquisitions that were not uniform, even within the same sample. For instance, in ischemic brain samples, lipofuscin from cell death introduces background noise that can artificially impact threshold levels. We tested global and local algorithms to automatically binarize the cells but these approaches resulted often on imperfect and not optimized segmentation for every cell. In our experience, manually adjusting the threshold provides a more accurate, reliable, and comparable selection of cellular elements, even though it introduces some subjectivity. To ensure consistency in segmentation, we recommend that the same person performs the analysis across all conditions. This clarification has been added to the discussion.

e) Parameter choices: L375: When using k-means clustering, it is good practice to determine the number of clusters (k) using silhouette or elbow scores. Simply selecting a value of k based on its previous usage in the literature is not rigorous, as the optimal number of clusters depends on the specific data structure. If they are seeking a more objective clustering approach, they could also consider employing other unsupervised techniques, (e.g. HDBSCAN) (L403f).

We do agree with the referee’s comment but, the purpose of the k-mean we used was just to illustrate the fact that the clusters generated are artificial and do not correspond to the reality of the continuum of microglia morphology. In the course of the study we used the elbow score to determine the k means but this did not work well because no clear elbow was visible in some datasets (probably because of the continuum of microglia morphologies). Anyway, using whatever k value will not change the problem that those clusters are quite artificial and that the boundaries of those clusters are quite arbitrary whatever the way k is determined manually or mathematically.

L373: A rationale for the choice of the 20 non-dimensional parameters as well as a detailed explanation of their computation such as the skeleton process ratio is missing. Also, how strongly correlated are those parameters, and how might this correlation bias the data outcomes?

Thank you for raising this point. There is no specific rationale beyond our goal of being as exhaustive as possible, incorporating most of the parameters found in the literature, as well as some additional ones that we believed could provide a more thorough description of microglial morphology.

Indeed, some of these parameters are correlated. Initially, we considered this might be problematic, but we quickly found that these correlations essentially act as factors that help assign more weight to certain parameters, reflecting their likely greater importance in a given dataset. Rather than being a limitation, the correlated parameters actually enhance the ranking. We tested removing some of these parameters in earlier versions of MorphoCellSorter, and found that doing so reduced the accuracy of the tool.

Differences between circularity and roundness factors are not coming across and require further clarification.

These are two distinct ways of characterizing morphological complexity, and we borrowed these parameters and kept the name from the existing literature, not necessarily in the context of microglia. In our case, these parameters are used to describe the overall shape of the cell. The advantage of using different metrics to calculate similar parameters is that, depending on the dataset, one method may be better suited to capture specific morphological features of a given dataset. MorphoCellSorter selects the parameter that best explains the greatest dispersion in the data, allowing for a more accurate characterization of the morphology. In Author response image 1 you will see how circularity and roundness describe differently cells

Author response image 1.

Correlation between Circularity and Roundness Factor in the Alzheimer disease dataset. A second order polynomial correlation exists between the two parameters in our dataset. Indeed (1) a single maximum is shared between both parameters. However, Circularity and Roundness Factor are not entirely redundant, as examplified by (2) the possible variety of Roundness Factors for a given Circularity as well as (3) the very different morphology minima of these two parameters.

One is applied to the soma and the other to the cell, but why is neither circularity nor loudness factor applied to both?

None of the parameters concern the cell body by itself. The cell body is always relative to another metric(s). Because these parameters and what they represent does not seem to be very clear we have added a graphic representation of the type of measurements and measure they provide in the revised version of the manuscript (Supplemental figure 8).

f) PCA analysis:

The authors spend a lot of text to describe the basic principles of PCA. PCA is mathematically well-described and does not require such depth in the description and would be sufficient with references.

Thank you for this comment indeed the description of PCA may be too exhaustive, we will simplify the text.

Furthermore, there are the following points that require attention:

L321: PC1 is the most important part of the data could be an incorrect statement because the highest dispersion could be noise, which would not be the most relevant part of the data. Therefore, the term "important" has to be clarified.

We are not sure in the case of segmented images the noise would represent most of the data, as by doing segmentation we also remove most of the noise, but maybe the reviewer is concerned about another type of noise? Nonetheless, we thank the reviewer for his comment and we propose the following change, that should solve this potential issue.

“PC<sub>1<.sub> is the direction in which data is most dispersed.”

L323: As before, it's not given that the first two components hold all the information.

Thank you for this comment we modified this statement as follows: “The two first components represent most of the information (about 70%), hence we can consider the plan PC₁, PC₂ as the principal plan reducing the dataset to a two dimensional space”

L327 and L331 contain mistakes in the nomenclature: Mix up of "wi" should be "wn" because "i" does not refer to anything. The same for "phi i = arctan(yn/wn)" should be "phi n".

Thanks a lot for these comments. We have made the changes in the text as proposed by the reviewer.

L348: Spearman's correlation measures monotonic correlation, not linear correlation. Either the authors used Pearson Correlation for linearity or Spearman correlation for monotonic. This needs to be clarified to avoid misunderstandings.

Sorry for the misunderstanding, we did use Spearman correlation which is monotonic, we thus changed linear by monotonic in the text. Thanks a lot for the careful reading.

g) If the authors find no morphological alteration, how can they ensure that the algorithm is sensitive enough to detect them? When morphologies are similar, it's harder to spot differences. In cases where morphological differences are more apparent, like stroke, classification is more straightforward.

We are not entirely sure we fully understand the reviewer's comment. When data are similar or nearly identical, MorphoCellSorter performs comparably to human experts (see Table 1). However, the advantage of using MorphoCellSorter is that it ranks cells do.much faster while achieving accuracy similar to that of human experts AND gives them a value on an axis (andrews score), which a human expert certainly can't. For example, in the case of mouse embryos, MorphoCellSorter’s ranking was as accurate as that made by human experts. Based on this ranking, the distributions were similar, suggesting that the morphologies are generally consistent across samples.

The algorithm itself does not detect anything—it simply ranks cells according to the provided parameters. Therefore, it is unlikely that sensitivity is an issue; the algorithm ranks the cells based on existing data. The most critical factor in the analysis is the segmentation step, which is not the focus of our paper. However, the more accurate the segmentation, the more distinct the parameters will be if actual differences exist. Thus, sensitivity concerns are more related to the quality of image acquisition or the segmentation process rather than the ranking itself. Once MorphoCellSorter receives the parameters, it ranks the cells accordingly. When cells are very similar, the ranking process becomes more complex, as reflected in the correlation values comparing expert rankings to those from MorphoCellSorter (Table 1).

Moreover, MorphoCellSorter does not only provide a ranking: the morphological indexes automatically computed offer useful information to compare the cells’ morphology between groups.

h) Minor aspects:

% notation requires to include (weight/volume) annotation.

This has been done in the revised version of the manuscript

Citation/source of the different mouse lines should be included in the method sections (e.g. L117).

The reference of the mouse line has been added (RRID:IMSR_JAX:005582) to the revised version of the manuscript.

L125: The length of the single housing should be specified to ensure no variability in this context.

The mice were kept 24h00 individually, this is now stated in the text

L673: Typo to the reference to the figure.

This has been corrected, thank you for your thoughtful reading.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Methods

(1) Alzheimer's disease model: was a perfusion performed and then an hour later brains extracted? Please clarify.

This is indeed what has been done.

(2) For in vitro microglial studies: was a percoll gradient used for the separation of immune cells? What percentage percoll was used? Was there separation of myelin and associated debris with the percoll centrifugation? Please clarify the protocol as it is not completely clear how these cells were separated from the initial brain lysate suspension. What cell density was plated?

The protocol has been completed, as followed: “Myelin and debris were then eliminated thanks to a Percoll® PLUS solution (E0414, Sigma-Aldrich) diluted with DPBS10X (14200075, Gibco) and enriched in MgCl₂ and CaCl₂ (for 50 mL of myelin separation buffer: 90 mL of Percoll PLUS, 10 mL of DPBS10X, 90 μL of 1 M CaCl₂ solution, and 50 μL of 1 M MgCl₂ solution).”. Thank you for your feedback.

(3) How are the microglia "automatically cropped" in FIJI (for the Phox2b mutant)? Is there a function/macro in the program you used? This is very important for the workflow and needs to be clarified. The methods section of this manuscript is a guide for future users of this workflow and should be as descriptive as possible. It would be useful to give detailed information on the manual classification process, perhaps as a supplement. The authors do a nice job pointing out that these older methods are not effective in categorizing microglia that don't necessarily fit into a predefined phenotype.

The protocol has been completed, as follows “. Briefly, the centroid of each detected object (i.e. microglia), except the ones on the borders, were detected, and a crop of 300x300 pixels around the objects were generated. Then, the pixels belonging to neighboring cells were manually removed on each generated crop.

(4) Please address the concern that manual tuning and thresholding are required for this method's accuracy. Is this easily reproducible?

Yes, it is easily reproducible for a given experimenter and is better suited than automatic thresholding. Although segmentation is not the primary focus of this paper, we leave it to users to choose the segmentation method that best fits their datasets.

To address your question, we acknowledge that automated thresholding would theoretically be ideal. However, we encountered challenges due to non-uniform image acquisitions, even within the same sample. For instance, in ischemic brain samples, lipofuscin resulting from cell death introduced background noise that could artificially influence threshold levels. We tested both global and local algorithms for automatic binarization of cells, but these approaches often produced suboptimal segmentation results for individual cells.

Based on our experience, manually adjusting the threshold provided more accurate, reliable, and consistent selection of cellular elements, even though it introduces a degree of subjectivity. To maintain consistency, we recommend that the same individual perform the analysis across all conditions.

This clarification has been incorporated into the discussion as follows: “Although, automated thresholding would be ideal. In our case, image acquisitions were not entirely uniform, even within the same sample. For instance, in ischemic brain samples, lipofuscin from cell death introduces background noise that can artificially impact threshold levels. This effect is observed even when comparing contralateral and ipsilateral sides of the same brain. In our experience, manually adjusting the threshold provides a more accurate, reliable, and comparable selection of cellular elements, even though it introduces some subjectivity. To ensure consistency in segmentation, we recommend that the same person performs the analysis across all conditions. “

(5) How are the authors performing the PCA---what program (e.g .R)? Again, please be explicit about how these mathematical operations were computed. (lines 302-345).

The PCA was made in Matlab, the code can be found on Github (https://github.com/Pascuallab/MorphCellSorter), as stated in the discussion.

Other:

(1) Can the authors comment on the challenges of the in vitro microglial analyses? The correlation of the experts v. MorphoCellSorter is much less than the fixed tissue. This is not addressed in the manuscript.

In vitro, microglial cells exhibit a narrower range of morphological diversity compared to ex vivo or in vivo conditions. A higher proportion of cells share similar morphologies or morphologies with comparable complexities, which makes establishing a precise ranking more challenging. Consequently, the rank of many cells could be adjusted without significantly affecting the overall quality of the ranking.

This explains why the rankings tend to show slightly greater divergence between experts. Interestingly, the ranking generated by MorphoCellSorter, which is objective and not subject to human bias, lies roughly midway between the rankings of the two experts.

(2) You point out that the MorphoCellSorter may not be suited for embryonic/prenatal microglial analysis.

This must be a misunderstanding because it is not what we concluded; we found that the ranking was correct but that we could not spot any differences due to transgenic alteration.

The lack of differences observed in the embryonic microglia (Figure 5) is not necessarily surprising, as embryonic microglia have diverse morphological characteristics--- immature microglia do not possess highly ramified processes until postnatal development [see Hirosawa et al. (2005) https://doi.org/10.1002/jnr.20480 -they use an Iba1-GFP transgenic mouse to visualize prenatal microglia]. Also, see Bennett et al. (2016) [https://doi.org/10.1073/pnas.1525528113] which shows mature microglia not appearing until 14 days postnatal.

We agree with the reviewer on that point nonetheless MorphoCellSorter provides an information on the fact that the population is homogeneous and that the mutation has no effect on the morphology.

(3) Although a semantic issue, Figure 1's categorization of microglia shows predefined groups of microglia do not necessarily usefully bin many cells. Is still possible to categorize the microglia without using hotly debated categorization methods? The literature review in the current manuscript correctly points out the spectrum phenomenon of microglial activation states, though some of the suggestions from Paolicelli et al. (2022) are not put into action. The use of "activated" only further perpetuates the oversimplified classification of microglia. Perhaps the authors could consider using the term "reactive", as it is recognized by the Microglial nomenclature paper cited above. Are "amoeboid microglia" not "activated microglia"? "Reactive" is a less loaded term and is a recommended descriptor. Amoeboid microglia are commonly understood to be indicative of a highly proinflammatory environment, though you could potentially use "hyper-reactive" to differentiate them from the slightly ramified "reactive" cells.

We changed activated microglia to reactive microglia as requested by the reviewer in the text. Thanks a lot for your comment

(4) The graphs in Figures 3 B-D are visually difficult to interpret. The better color contrast between the MorphoCellSorter/Expert and Expert1/Expert2 would be useful--- perhaps a color for Expert 1 and a different color for Expert 2. Is this the ranking from the same data in Figure 1 (lines 420-421)? It is unclear what the x-axis represents in 3B-D. E-G is much more intuitive.

We believe the confusion stems more from Figure 1 than Figure 3, as both figures use similar representations for entirely different analyses (clustering vs. ranking). To address this, we have provided an updated version of Figure 1 to help clarify this distinction and avoid any potential misinterpretation.

Regarding Figure 3B-D, we do not fully see the need for changing the colors. These panels are histograms that display the distribution of rank differences either between experts and MorphoCellSorter or between the two experts. Assigning specific colors to the experts or MorphoCellSorter would be challenging, as the histograms represent comparative distributions involving both an expert and MorphoCellSorter or the ranking differences between the two experts.

The same reasoning applies to Figures 3E-G. In these scatter plots, each point is defined by an ordinate (ranking value for one expert) and an abscissa (ranking value for either the other expert or MorphoCellSorter). Therefore, it would not be straightforward or meaningful to assign distinct colors to these elements within this context.

(5) Line 217: use the term "imaged" rather than "generated" ... or "images were generated of clusters of microglia located .... using MICROSOPE and Zen software." You aren't generating microglia, rather, you are generating images.

Thanks a lot for raising this problem, we changed the sentence as followed: “For the AD model, crops of individual microglial cells located in the secondary visual cortex were extracted from images using the Zen software (v3.5, Zeiss) and exported to the Tif image format.

(6) Elaborate on how an "inversion operation" was applied to Lacunarity, roundness factor, convex hull radii ratio, processes cell areas ratio, and skeleton processes. (Lines 299-300) Furthermore, a paragraph separation would be useful if the "inversion operation" is not what is described in the text immediately after this description.

Indeed, we are sorry for this lack of explanation. Some morphological indexes rank cells from the least to the most ramified, while others rank them in the opposite order. By inverting certain parameters, we can standardize the ranking direction across all parameters, simplifying data interpretation. This clarification has been added to the revised manuscript as follows:

“Lacunarity, roundness factor, convex hull radii ratio, processes cell areas ratio and skeleton processes ratio were subjected to an inversion operation in order to homogenize the parameters before conducting the PCA: indeed, some parameters rank cells from the least to the most ramified, while others rank them in the opposite order. By inverting certain parameters, we can standardize the ranking direction across all parameters, thus simplifying data interpretation.”

(7) Line 560: "measureclarke" seems to be an error associated with the reference. Please correct.

Thanks a lot, this has been corrected

(8) Discussion: compare MorphoCellSorter to the MIC-MAC program used by Salamanca et al. (2019). They use a similar approach, albeit not Andrew's plot.

We have added the Salamanca reference

Reviewer #2 (Recommendations for the authors):

While it's not expected that the authors address the significance of the morphology in relation to function here, they could help highlight the issue and produce data that would enhance the paper's significance. Therefore, I recommend a small-scale and straightforward study where the authors couple their analysis with a marker (e.g. Lysotracker or Mitotracker) to produce data that link their morphometric analysis to more functional readouts. Furthermore, I encourage the authors to elaborate on the practical applications of these morphometric tools and the implications of their measurements, as this would provide context for their work, which, as it stands, feels like just another tool.

We would like to thank the reviewer for their thoughtful comment and suggestion. Indeed, MorphoCellSorter is simply another tool, but one that offers a more convenient and efficient approach, producing a variety of results tailored to specific research needs. We strongly believe that MorphoCellSorter should be used in conjunction with other tools, depending on the specific research question.

In our view, MorphoCellSorter is particularly well-suited for researchers who need a quick and efficient way to determine whether their treatment, gene invalidation, or other experimental conditions affect microglial morphology. In this context, MorphoCellSorter is fast, user-friendly, and highly effective. However, for those who aim to uncover detailed differences in cell morphology, other tools requiring more time-intensive, full reconstructions of the cells would be more appropriate.

Providing additional data on the relationship between cellular function and morphology could certainly pave the way for new questions and more robust evidence. For instance, combining single-cell transcriptomics with morphological analysis would be an excellent approach to exploring the relationship between function and morphology. However, this would involve significant time, expense, and effort, and it represents a different line of inquiry altogether.

While it would be ideal to clearly demonstrate the link between morphology and function, we are concerned that pursuing such a goal would considerably delay the implementation and adoption of our tool, potentially raising additional questions beyond the scope of this study.!

Minor comments:

(1) Can MorphCellSorter be adapted for use with other cell types (e.g., astrocytes)?

Yes it could, we have made some pretty conclusive analysis on astrocytes but some parameters have to be adapted before being released.

(2) What modifications would be necessary? If it is not applicable, would a name that includes "Microglia" be more descriptive?

Modification would be quite minor, it is mainly the parameters being considered that would change, this is the reason why we will keep the MorphoCellSorter name. Thank you for the suggestion!

(3) A common challenge with such tools is the technical expertise required to use them. Could a user-friendly interface be developed to better fulfill its intended purpose and benefit the community?

This is a good point thank you, and the answer is yes, we will translate our Matlab code to Python to open it to a wider audience and we will certainly work on a friendly user interface!

(4) Given that this tool relies on imaging, can users trace a cell (or group of cells) back to the original image?

Yes, it is possible if each crop is annotated with the spatial coordinates during the segmentation step. It is not yet implemented in the actual version of the software but mainly depend on the way segmentation is performed, which is not the topic of the paper.

(5)  Line 36: The "biologically relevant" statement is central and needs to be expanded.

This is not easy as it is the abstract with a word limit. What we mean by this sentence is that when classifying cells we force them by mathematical tools to enter in a group of cells based on metrics that have not necessarily a biological meaning. We suggest the following modification “However, this classification may lack biological relevance, as microglial morphologies represent a continuum rather than distinct, separate groups, and do not correspond to mathematically defined, clusters irrelevant of microglial cells function.”

(6) Line 49-50: Provide reference and elaborate. For example, does this apply during early life?

We have slightly changed the sentence and added a reference.

(7) Line 69: Provide reference.

The reference, Hubert et al 2021 has been added

(8) Lines 78-88: A table summarizing other efforts in morphometric characterization of microglia would be helpful in distinguishing your work from others.

This has already been done in some review articles; we thus added the references to address readers to these reviews. Here is the revised version of the sentence: “ To date, the literature contains a wide variety of criteria to quantitatively describe microglial morphology, ranging from descriptive measures such as cell body surface area, perimeter, and process length to indices calculating different parameters such as circularity, roundness, branching index, and clustering (Adaikkan et al., 2019; Heindl et al., 2018; Kongsui, Beynon, Johnson, & Walker, 2014; Morrison et al., 2017; Young & Morrison, 2018)”

(9) Lines 130, 145: Please provide complete genotype information and the sources of the animals used.

It has been done

(10) Materials and Methods:

(1) Standardize the presentation of products (e.g., using # consistently).

It has been done

(2) Provide versions of software used.

We have modified accordingly

(3) Lines 372-373: A table listing the 20 parameters with brief explanations (as partially done in Materials and Methods) would greatly improve readability.

This is done in supp figure 8

(4) Since nomenclature is a critical issue in the literature, you used specific definitions (lines 376-383). However, please indicate (with a reference) why you use the term "activated," as it implies that the others are non-activated. Alternatively, define "activated" cluster differently.

We change activated microglia to reactive microglia as requested by the reviewer #1.

(4) Figure 1: In my opinion placing this figure as the first main figure is problematic as it confuses the message of the paper. Since the authors are introducing a new approach for morphological characterization in Figure 2, I recommend the latter for the sake of readability and clarity should be the first main image, while Figure 1 can move the supplements.

We do agree with the reviewer, we thus changed figure one as explained earlier to reviewer 1. Nonetheless because it is an important step of our reflection process we believe it can stay as a figure. We hope the change made in figure one clarifies the message of the paper.

(5) Figure 1: Please indicate on the figure the marker for the analysis.

Figure 2 has been changed

(6) No funding agencies are communicated.

This has been corrected

Author response:

The following is the authors’ response to the original reviews

Reviewer #1:

(1) Line numbers are missing.

Added

(2) VR classroom. Was this a completely custom design based on Unity, or was this developed on top of some pre-existing code? Many aspects of the VR classroom scenario are only introduced (e.g., how was the lip-speech synchronisation done exactly?). Additional detail is required. Also, is or will the experiment code be shared publicly with appropriate documentation? It would also be useful to share brief example video-clips.

We have added details about the VR classroom programming to the methods section (p. 6-7), and we have now included a video-example as supplementary material.

“Development and programming of the VR classroom were done primarily in-house, using assets (avatars and environment) were sourced from pre-existing databases. The classroom environment was adapted from assets provided by Tirgames on TurboSquid (https://www.turbosquid.com/Search/Artists/Tirgames) and modified to meet the experimental needs. The avatars and their basic animations were sourced from the Mixamo library, which at the time of development supported legacy avatars with facial blendshapes (this functionality is no longer available in current versions of Mixamo). A brief video example of the VR classroom is available at: https://osf.io/rf6t8.

“To achieve realistic lip-speech synchronization, the teacher’s lip movements were controlled by the temporal envelope of the speech, adjusting both timing and mouth size dynamically. His body motions were animated using natural talking gestures.”

While we do intent to make the dataset publicly available for other researchers, at this point we are not making the code for the VR classroom public. However, we are happy to share it on an individual-basis with other researchers who might find it useful for their own research in the future.

(3) "normalized to the same loudness level using the software Audacity". Please specify the Audacity function and parameters.

We have added these details (p.7)

“All sound-events were normalized to the same loudness level using the Normalize function in the audio-editing software Audacity (theaudacityteam.org, ver 3.4), with the peak amplitude parameter set to -5 dB, and trimmed to a duration of 300 milliseconds.“

(4) Did the authors check if the participants were already familiar with some of the content in the mini-lectures?

This is a good point. Since the mini-lectures spanned many different topics, we did not pre-screen participants for familiarity with the topics, and it is possible that some of the participants had some pre-existing knowledge.

In hindsight, it would have been good to have added some reflective questions regarding participants prior knowledge as well as other questions such as level of interest in the topic and/or how well they understood the content. These are elements that we hope to include in future versions of the VR classroom.

(5) "Independent Component Analysis (ICA) was then used to further remove components associated with horizontal or vertical eye movements and heartbeats". Please specify how this selection was carried out.

Selection of ICA components was done manually based on visual inspection of their time-course patterns and topographical distributions, to identify components characteristic of blinks, horizontal eye-movements and heartbeats). Examples of these distinct components are provided in Author response image 1 below. These is now specified in the methods section.

Author response image 1.

(6) "EEG data was further bandpass filtered between 0.8 and 20 Hz". If I understand correctly, the data was filtered a second time. If that's the case, please do not do that, as that will introduce additional and unnecessary filtering artifacts. Instead, the authors should replace the original filter with this one (so, filtering the data only once). Please see de Cheveigne and Nelkn, Neuron, 2019 for an explanation. Also, please provide an explanation of the rationale for further restricting the cut-off bands in the methods section. Finally, further details on the filters should be included (filter type and order, for example).

Yes, the data was indeed filtered twice. The first filter is done as part of the preprocessing procedure, in order to remove extremely high- and low- frequency noise but retain most activity within the range of “neural” activity. This broad range is mostly important for the ICA procedure, so as to adequately separate between ocular and neural contribution to the recorded signal.

However, since both the speech tracking responses and ERPs are typically less broadband and are comprised mostly of lower frequencies (e.g., those that make up the speech-envelope), a second narrower filter was applied to improve TRF model-fit and make ERPs more interpretable.

In both cases we used a fourth order zero-phase Butterworth IIR filter with 1-seconds of padding, as implemented in the Fieldtrip toolbox. We have added these details to the manuscript.

(7) "(~ 5 minutes of data in total), which is insufficient for deriving reliable TRFs". That is a bit pessimistic and vague. What does "reliable" mean? I would tend to agree when talking about individual subject TRFs, which 5 min per participant can be enough at the group level. Also, this depends on the specific speech material. If the features are univariate or multivariate. Etc. Please narrow down and clarify this statement.

We determined that the data in the Quiet condition (~5 min) was insufficient for performing reliable TRF analysis, by assessing whether its predictive-power was significantly better than chance. As shown in Author response image 2 below, the predictive power achieved using this data was not higher than values obtained in permuted data (p = 0.43). Therefore, we did not feel that it was appropriate to include TRF analysis of the Quiet condition in this manuscript. We have now clarified this in the manuscript (p. 10)

Author response image 2.

(8) "Based on previous research in by our group (Kaufman & Zion Golumbic 2023), we chose to use a constant regularization ridge parameter (λ= 100) for all participants and conditions". This is an insufficient explanation. I understand that there is a previous paper involved. However, such an unconventional choice that goes against the original definition and typical use of these methods should be clearly reported in this manuscript.

We apologize for not clarifying this point sufficiently, and have added an explanation of this methodological choice (p.11):

“The mTRF toolbox uses a ridge-regression approach for L2 regularization of the model to ensure better generalization to new data. We tested a range of ridge parameter values (λ's) and used a leave-one-out cross-validation procedure to assess the model’s predictive power, whereby in each iteration, all but one trials are used to train the model, and it is then applied to the left-out trial. The predictive power of the model (for each λ) is estimated as the Pearson’s correlation between the predicted neural responses and the actual neural responses, separately for each electrode, averages across all iterations. We report results of the model with the λ the yielded the highest predictive power at the group-level (rather than selecting a different λ for each participant which can lead to incomparable TRF models across participants; see discussion in Kaufman & Zion Golumbic 2023).”

Assuming that the explanation will be sufficiently convincing, which is not a trivial case to make, the next issue that I will bring up is that the lambda value depends on the magnitude of input and output vectors. While the input features are normalised, I don't see that described for the EEG signals. So I assume they are not normalized. In that case, the lambda would have at least to be adapted between subjects to account for their different magnitude.

We apologize for omitting this detail – yes, the EEG signals were normalized prior to conducting the TRF analysis. We have updated the methods section to explicitly state this pre-processing step (p.10).

Another clarification, is that value (i.e., 100) would not be comparable either across subjects or across studies. But maybe the authors have a simple explanation for that choice? (note that this point is very important as this could lead others to use TRF methods in an inappropriate way - but I understand that the authors might have specific reasons to do so here). Note that, if the issue is finding a reliable lambda per subject, a more reasonable choice would be to use a fixed lambda selected on a generic (i.e., group-level) model. However selecting an arbitrary lambda could be problematic (e.g., would the results replicate with another lambda; and similarly, what if a different EEG system was used, with different overall magnitude, hence the different impact of the regularisation).

We fully agree that selecting an arbitrary lambda is problematic (esp across studies). As clarified above, the group-level lambda chosen here for the encoding more was data-driven, optimized based on group-level predictive power.

(9) "L2 regularization of the model, to reduce its complexity". Could the authors explain what "reduce its complexity" refers to?

Our intension here was to state that the L2 regularization constrains the model’s weights so that it can better generalize between to left-out data. However, for clarity we have now removed this statement.

(10) The same lambda value was used for the decoding model. From personal experience, that is very unlikely to be the optimal selection. Decoding models typically require a different (usually larger) lambda than forward models, which can be due to different reasons (different SNR of "input" of the model and, crucially, very different dimensionality).

We agree with the reviewer that treatment of regularization parameters might not be identical for encoding and decoding models. Our initial search of lambda parameters was limited to λ= 0.01 - 100, with λ= 100 showing the best reconstruction correlations. However, following the reviewer’s suggestion we have now broadened the range and found that, in fact reconstruction correlations are further improved and the best lambda is λ= 1000 (see Author response image 3 below, left panel). Importantly, the difference in decoding reconstruction correlations between the groups is maintained regardless of the choice of lambda (although the effect-size varies; see Author response image 3, right panel). We have now updated the text to reflect results of the model with λ= 1000.

Author response image 3.

(11) Skin conductance analysis. Additional details are required. For example, how was the linear interpolation done exactly? The raw data was downsampled, sure. But was an anti-aliasing filter applied? What filter exactly? What implementation for the CDA was run exactly?

We have added the following details to the methods section (p. 14):

“The Skin Conductance (SC) signal was analyzed using the Ledalab MATLAB toolbox (version 3.4.9; Benedek and Kaernbach, 2010; http://www.ledalab.de/) and custom-written scripts. The raw data was downsampled to 16Hz using FieldTrip's ft_resampledata function, which applies a built-in anti-aliasing low-pass filter to prevent aliasing artifacts. Data were inspected manually for any noticeable artifacts (large ‘jumps’), and if present were corrected using linear interpolation in Ledalab. A continuous decomposition analysis (CDA) was employed to separate the tonic and phasic SC responses for each participant. The CDA was conducted using the 'sdeco' mode (signal decomposition), which iteratively optimizes the separation of tonic and phasic components using the default regularization settings.”

(12) "N1- and P2 peaks of the speech tracking response". Have the authors considered using the N1-P2 complex rather than the two peaks separately? Just a thought.

This is an interesting suggestion, and we know that this has been used sometimes in more traditional ERP literature. In this case, since neither peak was modulated across groups, we did not think this would yield different results. However, it is a good point to keep in mind for future work.

(13) Figure 4B. The ticks are missing. From what I can see (but it's hard without the ticks), the N1 seems later than in other speech-EEG tracking experiments (where is closer to ~80ms). Could the authors comment on that? Or maybe this looks similar to some of the authors' previous work?

We apologize for this and have added ticks to the figure.

In terms of time-course, a N1 peak at around 100ms is compatible with many of our previous studies, as well as those from other groups.

(14) Figure 4C. Strange thin vertical grey bar to remove.

Fixed.

(15) Figure 4B: What about the topographies for the TRF weights? Could the authors show that for the main components?

Yes. The topographies of the main TRF components are similar to those of the predictive power and are compatible with auditory responses. We have added them to Figure 4B.

(16) Figure 4B: I just noticed that this is a grand average TRF. That is ok (but not ideal) only because the referencing is to the mastoids. The more appropriate way of doing this is to look at the GFP, instead, which estimates the presence of dipoles. And then look at topographies of the components. Averaging across channels makes the plotted TRF weaker and noisier. I suggest adding the GFP to the plot. Also, the colour scale in Figure 4A is deceiving, as blue is usually used for +/- in plots of the weights. While that is a heatmap, where using a single colour or even yellow to red would be less deceiving at first look. Only cosmetics, indeed. The result is interesting nonetheless!

We apologize for this, and agree with the reviewer that it is better not to average across EEG channels. In the revised Figure, we now show the TRFs based on the average of electrodes FC1, FC2, and FCz, which exhibited the strongest activity for the two main components.

Following the previous comment, we have also included the topographical representation of the TRF main components, to give readers a whole-head perspective of the TRF.

We have also fixed the color-scales.

We are glad that the reviewer finds this result interesting!

(17) Figure 4C. This looks like a missed opportunity. That metric shows a significant difference overall. But is that underpinned but a generally lower envelope reconstruction correlation, or by a larger deviation in those correlations (so, that metric is as for the control in some moments, but it drops more frequently due to distractibility)?

We understand the reviewer’s point here, and ideally would like to be able to address this in a more fine-grained analysis, for example on a trial-by-trial basis. However, the design of the current experiment was not optimized for this, in terms of (for example) number of trials, the distribution of sound-events and behavioral outcomes. We hope to be able to address this issue in our future research.

(18) I am not a fan of the term "accuracy" for indicating envelope reconstruction correlations. Accuracy is a term typically associated with classification. Regression models are typically measured through errors, loss, and sometimes correlations. 'Accuracy' is inaccurate (no joke intended).

We accept this comment and now used the term “reconstruction correlation”.

(19) Discussion. "The most robust finding in". I suggest using more precise terminology. For example, "largest effect-size".

We agree and have changed the terminology (p. 31).

(20) "individuals who exhibited higher alpha-power [...]". I probably missed this. But could the authors clarify this result? From what I can see, alpha did not show an effect on the group. Is this referring to Table 2? Could the authors elaborate on that? How does that reconcile with the non-significant effect of the group? In that same sentence, do you mean "and were more likely"? If that's the case, and they were more likely to report attentional difficulties, how is it that there is no group-effect when studying alpha?

Yes, this sentence refers to the linear regression models described in Figure 10 and in Table 2. As the reviewer correctly points out, this is one place where there is a discrepancy between the results of the between-group analysis (ADHD diagnosis yes/no) and the regression analysis, which treats ADHD symptoms as a continuum, across both groups. The same is true for the gaze-shift data, which also did not show a significance between-group effect but was identified in the regression analysis as contributing to explaining the variance in ADHD symptoms.

We discuss this point on pages 30-31, noting that “although the two groups are clearly separable from each other, they are far from uniform in the severity of symptoms experienced”, which motivated the inclusion of both analyses in this paper.

At the bottom of p. 31 we specifically address the similarities and differences between the between-group and regression-based results. In our opinion, this pattern emphasizes that while neither approach is ‘conclusive’, looking at the data through both lenses contributes to an overall better understanding of the contributing factors, as well as highlighting that “no single neurophysiological measure alone is sufficient for explaining differences between the individuals – whether through the lens of clinical diagnosis or through report of symptoms”.

(21) "why in the latter case the neural speech-decoding accuracy did not contribute to explaining ASRS scores [...]". My previous point 1 on separating overall envelope decoding from its deviation could help there. The envelope decoding correlation might go up and down due to SNR, while you might be more interested in the dynamics over time (i.e., looking at the reconstructions over time).

Again, we appreciate this comment, but believe that this additional analysis is outside the scope of what would be reliably-feasible with the current dataset. However, since the data will be made publicly available, perhaps other researchers will have better ideas as to how to do this.

(22) Data and code sharing should be discussed. Also, specific links/names and version numbers should be included for the various libraries used.

We are currently working on organizing the data to make it publicly available on the Open Science Project.

We have updated links and version numbers for the various toolboxes/software used, throughout the manuscript.

Reviewer #2:

(1) While it is highly appreciated to study selective attention in a naturalistic context, the readers would expect to see whether there are any potential similarities or differences in the cognitive and neural mechanisms between contexts. Whether the classic findings about selective attention would be challenged, rebutted, or confirmed? Whether we should expect any novel findings in such a novel context? Moreover, there are some studies on selective attention in the naturalistic context though not in the classroom, it would be better to formulate specific hypotheses based on previous findings both in the strictly controlled and naturalistic contexts.

Yes, we fully agree that comparing results across different contexts would be extremely beneficial and important.

The current paper serves as an important proof-first-concept demonstrating the plausibility and scientific potential of using combined EEG-VR-eyetracking to study neurophysiological aspects of attention and distractibility, but is also the basis for formulating specific hypothesis that will be tested in follow-up studies.

If fact, a follow up study is already ongoing in our lab, where we are looking into this point, by testing users in different VR scenarios (e.g., classroom, café, office etc.), and assessing whether similar neurophysiological patterns are observed across contexts and to what degree they are replicable within and across individuals. We hope to share these data with the community in the near future.

(2) Previous studies suggest handedness and hemispheric dominance might impact the processing of information in each hemisphere. Whether these issues have been taken into consideration and appropriately addressed?

This is an interesting point. In this study we did not specifically control for handedness/hemispheric dominance, since most of the neurophysiological measured used here are sensory/auditory in their nature, and therefore potentially invariant to handedness. Moreover, the EEG signal is typically not very sensitive to hemispheric dominance, at least for the measures used here. However, this might be something to consider more explicitly in future studies. Nonetheless, we have added handedness information to the Methods section (p. 5): “46 right-handed, 3 left-handed”

(3) It would be interesting to know how students felt about the Virtual Classroom context, whether it is indeed close to the real classroom or to some extent different.

Yes, we agree. Obviously, the VR classroom differs in many ways from a real classroom, in terms of the perceptual experience, social aspects and interactive possibilities. We did ask participants about their VR experience after the experiment, and most reported feeling highly immersed in the VR environment and engaged in the task, with a strong sense of presence in the virtual-classroom.

We note that, in parallel to the VR studies in our lab, we are also conducting experiments in real classrooms, and we hope that the cross-study comparison will be able to shed more light on these similarities/differences.

(4) One intriguing issue is whether neural tracking of the teacher's speech can index students' attention, as the tracking of speech may be relevant to various factors such as sound processing without semantic access.

Another excellent point. While separating the ‘acoustic’ and ‘semantic’ contributions to the speech tracking response is non-trivial, we are currently working on methodological approaches to do this (again, in future studies) following, for example, the hierarchical TRF approach used by Brodbeck et al. and others.

(5) There are many results associated with various metrics, and many results did not show a significant difference between the ADHD group and the control group. It is difficult to find the crucial information that supports the conclusion. I suggest the authors reorganize the results section and report the significant results first, and to which comparison(s) the readers should pay attention.

We apologize if the organization of the results section was difficult to follow. This is indeed a challenge when collecting so many different neurophysiological metrics.

To facilitate this, we have now added a paragraph at the beginning of the result section, clarifying its structure (p.16):

The current dataset is extremely rich, consisting of many different behavioral, neural and physiological responses. In reporting these results, we have separated between metrics that are associated with paying attention to the teacher (behavioral performance, neural tracking of the teacher’s speech, and looking at the teacher), those capturing responses to the irrelevant sound-events (ERPs and event-related changes in SC and gaze); as well as more global neurophysiological measures that may be associated with the listeners’ overall ‘state’ of attention or arousal (alpha- and beta-power and tonic SC).

Moreover, within each section we have ordered the analysis such that the ones with significant effects are first. We hope that this contributes to the clarity of the results section.

(6) The difference between artificial and non-verbal humans should be introduced earlier in the introduction and let the readers know what should be expected and why.

We have added this to the Introduction (p. 4)

(7) It would be better to discuss the results against a theoretical background rather than majorly focusing on technical aspects.

We appreciate this comment. In our opinion, the discussion does contain a substantial theoretical component, both regarding theories of attention and attention-deficits, and also regarding their potential neural correlates. However, we agree that there is always room for more in depth discussion.

Reviewer #3:

Major:

(1) While the study introduced a well-designed experiment with comprehensive physiological measures and thorough analyses, the key insights derived from the experiment are unclear. For example, does the high ecological validity provide a more sensitive biomarker or a new physiological measure of attention deficit compared to previous studies? Or does the study shed light on new mechanisms of attention deficit, such as the simultaneous presence of inattention and distraction (as mentioned in the Conclusion)? The authors should clearly articulate their contributions.

Thanks for this comment.

We would not say that this paper is able to provide a ‘more sensitive biomarker’ or a ‘new physiological measure of attention’ – in order to make those type of grand statements we would need to have much more converging evidence from multiple studies and using both replication and generalization approaches.

Rather, from our perspective, the key contribution of this work is in broadening the scope of research regarding the neurophysiological mechanisms involved in attention and distraction.

Specifically, this work:

(1) Offers a significant methodological advancement of the field – demonstrating the plausibility and scientific potential of using combined EEG-VR-eyetracking to study neurophysiological aspects of attention and distractibility in contexts that ‘mimic’ real-life situations (rather than highly controlled computerized tasks).

(2) Provides a solid basis formulating specific mechanistic hypothesis regarding the neurophysiological metrics associated with attention and distraction, the interplay between them, and their potential relation to ADHD-symptoms. Rather than being an end-point, we see these results as a start-point for future studies that emphasize ecological validity and generalizability across contexts, that will hopefully lead to improved mechanisms understanding and potential biomarkers of real-life attentional capabilities (see also response to Rev #2 comment #1 above).

(3) Highlights differences and similarities between the current results and those obtained in traditional ‘highly controlled’ studies of attention (e.g., in the way ERPs to sound-events differ between ADHD and controls; variability in gaze and alpha-power; and more broadly about whether ADHD symptoms do or don’t map onto specific neurophysiological metrics). Again, we do not claim to give a definitive ’answer’ to these issues, but rather to provide a new type of data that can expands the conversation and address the ecological validity gap in attention research.

(2) Based on the multivariate analyses, ASRS scores correlate better with the physiological measures rather than the binary deficit category. It may be worthwhile to report the correlation between physiological measures and ASRS scores for the univariate analyses. Additionally, the correlation between physiological measures and behavioral accuracy might also be interesting.

Thanks for this. The beta-values reported for the regression analysis reflect the correlations between the different physiological measures and the ASRS scores (p. 30). From a statistical perspective, it is better to report these values rather than the univariate correlation-coefficients, since these represent the ‘unique’ relationship with each factor, after controlling for all the others.

The univariate correlations between the physiological measures themselves, as well as with behavioral accuracy, are reported in Figure 10

(3) For the TRF and decoding analysis, the authors used a constant regularization parameter per a previous study. However, the optimal regularization parameter is data-dependent and may differ between encoding and decoding analyses. Furthermore, the authors did not conduct TRF analysis for the quiet condition due to the limited ~5 minutes of data. However, such a data duration is generally sufficient to derive a stable TRF with significant predictive power (Mesik and Wojtczak, 2023).

The reviewer raises two important points, also raised by Rev #1 (see above).

Regarding the choice of regularization parameters, we have now clarified that although we used a common lambda value for all participants, it was selected in a data-driven manner, so as to achieve an optimal predictive power at the group-level.

See revised methods section:

“The mTRF toolbox uses a ridge-regression approach for L2 regularization of the model to ensure better generalization to new data. We tested a range of ridge parameter values (λ's) and used a leave-one-out cross-validation procedure to assess the model’s predictive power, whereby in each iteration, all but one trials are used to train the model, and it is then applied to the left-out trial. The predictive power of the model (for each λ) is estimated as the Pearson’s correlation between the predicted neural responses and the actual neural responses, separately for each electrode, averages across all iterations. We report results of the model with the λ the yielded the highest predictive power at the group-level (rather than selecting a different λ for each participant which can lead to incomparable TRF models across participants; see discussion in Kaufman & Zion Golumbic 2023).”

Regarding whether data was sufficient in the Quiet condition for performing TRF analysis – we are aware of the important work by Mesik & Wojtczak, and had initially used this estimate when designing our study. However, when assessing the predictive-power of the TRF model trained on data from the Quiet condition, we found that it was not significantly better than chance (see Author response image 2, ‘real’ predictive power vs. permuted data). Therefore, we ultimately did not feel that it was appropriate to include TRF analysis of the Quiet condition in this manuscript. We have now clarified this in the manuscript (p. 10)

(4) As shown in Figure 4, for ADHD participants, decoding accuracy appears to be lower than the predictive power of TRF. This result is surprising because more data (i.e., data from all electrodes) is used in the decoding analysis.

This is an interesting point – however, in our experience it is not necessarily the case that decoding accuracy (i.e., reconstruction correlation with the stimulus) is higher than encoding predictive-power. While both metrics use Pearson’s’ correlations, they quantify the similarity between two different types of signals (the EEG and the speech-envelope). Although the decoding procedure does use data from all electrodes, many of them don’t actually contain meaningful information regarding the stimulus, and thus could just as well hinder the overall performance of the decoding.

(5) Beyond the current analyses, the authors may consider analyzing inter-subject correlation, especially for the gaze signal analysis. Given that the area of interest during the lesson changes dynamically, the teacher might not always be the focal point. Therefore, the correlation of gaze locations between subjects might be better than the percentage of gaze duration on the teacher.

Thanks for this suggestion. We have tried to look into this, however working with eye-gaze in a 3-D space is extremely complex and we are not able to calculate reliable correlations between participants.

(6) Some preprocessing steps relied on visual and subjective inspection. For instance, " Visual inspection was performed to identify and remove gross artifacts (excluding eye movements) " (P9); " The raw data was downsampled to 16Hz and inspected for any noticeable artifacts " (P13). Please consider using objective processes or provide standards for subjective inspections.

We are aware of the possible differences between objective methods of artifact rejection vs. use of manual visual inspection, however we still prefer the manual (subjective) approach. As noted, in this case only very large artifacts were removed, exceeding ~ 4 SD of the amplitude variability, so as to preserve as many full-length trials as possible.

(7) Numerous significance testing methods were employed in the manuscript. While I appreciate the detailed information provided, describing these methods in a separate section within the Methods would be more general and clearer. Additionally, the authors may consider using a linear mixed-effects model, which is more widely adopted in current neuroscience studies and can account for random subject effects.

Indeed, there are many statistical tests in the paper, given the diverse types of neurophysiological data collected here. We actually thought that describing the statistics per method rather than in a separate “general” section would be easier to follow, but we understand that readers might diverge in their preferences.

Regarding the use of mixed-effect models – this is indeed a great approach. However, it requires deriving reliable metrics on a per-trial basis, and while this might be plausible for some of our metrics, the EEG and GSR metrics are less reliable at this level. This is why we ultimately chose to aggregate across trials and use a regular regression model rather than mixed-effects.

(8) Some participant information is missing, such as their academic majors. Given that only two lesson topics were used, the participants' majors may be a relevant factor.

To clarify – the mini-lectures presented here actually covered a large variety of topics, broadly falling within the domains of history, science and social-science and technology. Regarding participants’ academic majors, these were relatively diverse, as can be seen in Author response table 1 and Author response image 4.

Author response table 1.

Author response image 4.

(9) Did the multiple regression model include cross-validation? Please provide details regarding this.

Yes, we used a leave-one-out cross validation procedure. We have now clarified this in the methods section which now reads:

“The mTRF toolbox uses a ridge-regression approach for L2 regularization of the model to ensure better generalization to new data. We tested a range of ridge parameter values (λ's) and used a leave-one-out cross-validation procedure to assess the model’s predictive power, whereby in each iteration, all but one trials are used to train the model, and it is then applied to the left-out trial. The predictive power of the model (for each λ) is estimated as the Pearson’s correlation between the predicted neural responses and the actual neural responses, separately for each electrode, averages across all iterations. We report results of the model with the λ the yielded the highest predictive power at the group-level (rather than selecting a different λ for each participant which can lead to incomparable TRF models across participants; see discussion in Kaufman & Zion Golumbic 2023).”

Minor:

(10) Typographical errors: P5, "forty-nine 49 participants"; P21, "$ref"; P26, "Table X"; P4, please provide the full name for "SC" when first mentioned.

Thanks! corrected

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Hippocampal place cells display a sequence of firing activities when the animal travels through a spatial trajectory at a behavioral time scale of seconds to tens of seconds. Interestingly, parts of the firing sequence also occur at a much shorter time scale: ~120 ms within individual cycles of theta oscillation. These so-called theta sequences are originally thought to naturally result from the phenomenon of theta phase precession. However, there is evidence that theta sequences do not always occur even when theta phase precession is present, for example, during the early experience of a novel maze. The question is then how they emerge with experience (theta sequence development). This study presents evidence that a special group of place cells, those tuned to fast-gamma oscillations, may play a key role in theta sequence development.

The authors analyzed place cells, LFPs, and theta sequences as rats traveled a circular maze in repeated laps. They found that a group of place cells were significantly tuned to a particular phase of fast-gamma (FG-cells), in contrast to others that did not show such tunning (NFG-cells). The authors then omitted FG-cells or the same number of NFG-cells, in their algorithm of theta sequence detection and found that the quality of theta sequences, quantified by a weighted correlation, was worse with the FG-cell omission, compared to that with the NFG-cell omission, during later laps, but not during early laps. What made the FG-cells special for theta sequences? The authors found that FG-cells, but not NFG-cells, displayed phase recession to slow-gamma (25 - 45 Hz) oscillations (within theta cycles) during early laps (both FG- and NFG-cells showed slow-gamma phase precession during later laps). Overall, the authors conclude that FG-cells contribute to theta sequence development through slow-gamma phase precession during early laps.

How theta sequences are formed and developed during experience is an important question, because these sequences have been implicated in several cognitive functions of place cells, including memory-guided spatial navigation. The identification of FG-cells in this study is straightforward. Evidence is also presented for the role of these cells in theta sequence development. However, given several concerns elaborated below, whether the evidence is sufficiently strong for the conclusion needs further clarification, perhaps, in future studies.

We thank the reviewer for these positive comments.

(1) The results in Figure 3 and Figure 8 seems contradictory. In Figure 8, all theta sequences displayed a seemingly significant weighted correlation (above 0) even in early laps, which was mostly due to FG-cell sequences but not NFG-cell sequences (correlation for NFG-sequences appeared below 0). However, in Figure 3H, omitting FG-cells and omitting NFG-cells did not produce significant differences in the correlation. Conversely, FG-cell and NFG-cell sequences were similar in later laps in Figure 8 (NFG-cell sequences appeared even better than FG-cell sequences), yet omitting NFG-cells produced a better correlation than omitting FG-cells. This confusion may be related to how "FG-cell-dominant sequences" were defined, which is unclear in the manuscript. Nevertheless, the different results are not easy to understand.

We thank the reviewer for pointing out this important problem.  The potential contradictory can be interpreted by different sequence dataset included in Fig3 and Fig8, described as follows.

(1) In Fig 3, all sequences decoded without either FG or NFG cells were included, defined as exFG-sequences and exNFG sequences, so that we couldn’t observe sequence development at early phase and thus the weighted correlation was low.  (2) In Fig8, however, the sequences with either FG or NFG cells firing across at least 3 slow gamma cycles were included, defined as FG-cell sequences and NFG-cell sequences.  This criterion ensures to investigate the relationship between sequence development and slow gamma phase precession, so that these sequences were contributed by cells likely to show slow gamma phase precession.  These definitions have been updated to the “Theta sequences detection” section of the Methods (Line 606-619).

At early phase, there’s still no difference of weighted correlation between FG-cell sequences and NFG-cell sequences (Author response image 1A, Student’s t test, t(65)=0.2, p=0.8, Cohen's D=0.1), but the FG-cell sequences contained high proportion of slow gamma phase precession (Fig8F).  At late phase, both FG-cell sequences and NFG-cell sequences exhibited slow gamma phase precession, so that their weighted correlation were high with no difference (Author response image 1B, Student’s t test, t(62)=-1.1, p=0.3, Cohen's D=0.3).  This result further indicates that the theta sequence development requires slow gamma phase precession, especially for FG cells during early phase.

Author response image 1.

(2) The different contributions between FG-cells and NFG-cells to theta sequences are supposed not to be caused by their different firing properties (Figure 5). However, Figure 5D and E showed a large effect size (Cohen's D = 07, 0.8), although not significant (P = 0.09, 0.06). But the seemingly non-significant P values could be simply due to smaller N's (~20). In other parts of the manuscript, the effect sizes were comparable or even smaller (e.g. D = 0.5 in Figure 7B), but interpreted as positive results: P values were significant with large N's (~480 in Fig. 7B). Drawing a conclusion purely based on a P value while N is large often renders the conclusion only statistical, with unclear physical meaning. Although this is common in neuroscience publications, it makes more sense to at least make multiple inferences using similar sample sizes in the same study.

We thank the reviewer for this kind suggestion.  We made multiple inferences using similar sample sizes as much as possible.  In Fig7B, we did the statistical analysis with sessions as samples, and we found the significant conclusion was maintained.  These results have been updated to the revised manuscript (Lines 269-270).and the Fig7B has been replaced correspondingly.

(3) In supplementary Figure 2 - S2, FG-cells displayed stronger theta phase precession than NFG-cells, which could be a major reason why FG-cells impacted theta sequences more than NFG cells. Although factors other than theta phase precession may contribute to or interfere with theta sequences, stronger theta phase precession itself (without the interference of other factors), by definition, can lead to stronger theta sequences.

This is a very good point.  The finding that FG-cells displayed stronger theta phase precession than NFG-cells was consistent with the finding of Guardamagna et al., 2023 Cell Rep, that the theta phase precession pattern emerged with strong fast gamma.  Since slow gamma phase precession occurred within theta cycles, it is hard to consider the contribution of these factors to theta sequences development, without taking theta phase precession into account.  But one should be noted that the theta sequences could not be developed even if theta phase precession existed from the very beginning of the exploration (Feng et al., 2025 J Neurosci).  These findings suggest that theta phase precession, together with other factors, impact theta sequence development.  However, the weight of each factor and their interaction still need to be further investigated.  We have discussed this possibility in the Discussion section (Lines 361- 373).

(4) The slow-gamma phase precession of FG-cells during early laps is supposed to mediate or contribute to the emergence of theta sequences during late laps (Figure 1). The logic of this model is unclear. The slow-gamma phase precession was present in both early and late laps for FG-cells, but only present in late laps for NFG-cells. It seems more straightforward to hypothesize that the difference in theta sequences between early and later laps is due to the difference in slow-gamma phase precession of NFG cells between early and late laps. Although this is not necessarily the case, the argument presented in the manuscript is not easy to follow.

We thank the reviewer for pointing this out.  The slow gamma phase precession was first found in my previous publication (Zheng et al., 2016 Neuron), which indicates a temporally compressed manner for coding spatial information related to memory retrieval.  In this case, we would expect that slow gamma phase precession occurred in all cells during late laps, because spatial information was retrieved when rats have been familiar with the environment.  However, during early laps when novel information was just encoded, there would be balance between fast gamma and slow gamma modulation of cells for upcoming encoding-retrieval transition.  A possibility is that FG-cells support this balance by receiving modulation of both fast gamma and slow gamma, but with distinct phase-coding modes (fast gamma phase locking and slow gamma phase precession) in a temporally coordinated manner.  We have discussed this possibility in the Discussion section (Lines 415- 428).

(5) There are several questions on the description of methods, which could be addressed to clarify or strengthen the conclusions.

(i) Were the identified fast- and slow-gamma episodes mutually exclusive?

Yes, the fast- and slow-gamma episodes are mutually exclusive. We have added descriptions in the “Detection of gamma episodes” section in the Methods part (Lines 538-550).

(ii) Was the task novel when the data were acquired? How many days (from the 1st day of the task) were included in the analysis? When the development of the theta sequence was mentioned, did it mean the development in a novel environment, in a novel task, or purely in a sense of early laps (Lap 1, 2) on each day?

We thank the reviewer for pointing this out.  The task was not novel to rats in this dataset, because only days with good enough recording quality for sequence decoding were included in this paper, which were about day2-day10 for each rat.  However, we still observed the process of sequence formation because of the rat’s exploration interest during early laps.  Thus, when the development of the theta sequence was mentioned, it meant a sense of early laps on each day.

(iii) How were the animals' behavioral parameters equalized between early and later laps? For example, speed or head direction could potentially produce the differences in theta sequences.

This is a very good point.  In terms of the effect of running speed on theta sequences, we quantified the running speeds during theta sequences across trials 1-5.  We found that the rats were running at stable running speed, which has been reported in Fig.3F.  In terms of the effect of head direction on theta sequences, we measured the angle difference between head direction and running direction.  We found that the angle difference for each lap was distributed around 0, with no significant difference across laps (Fig.S3, Watson-Williams multi-sample test, F(4,55)=0.2, p=0.9, partial η²= 0.01).  These results indicate that the differences in theta sequences across trials cannot be interpreted by the variability of behavioral parameters.  We have updated these results and corresponding methods in the revised manuscript (Lines 172-175, Lines 507-511, with a new Fig.S3).

Reviewer #2 (Public Review):

This manuscript addresses an important question that has not yet been solved in the field, what is the contribution of different gamma oscillatory inputs to the development of "theta sequences" in the hippocampal CA1 region? Theta sequences have received much attention due to their proposed roles in encoding short-term behavioral predictions, mediating synaptic plasticity, and guiding flexible decision-making. Gamma oscillations in CA1 offer a readout of different inputs to this region and have been proposed to synchronize neuronal assemblies and modulate spike timing and temporal coding. However, the interactions between these two important phenomena have not been sufficiently investigated. The authors conducted place cell and local field potential (LFP) recordings in the CA1 region of rats running on a circular track. They then analyzed the phase locking of place cell spikes to slow and fast gamma rhythms, the evolution of theta sequences during behavior, and the interaction between these two phenomena. They found that place cells with the strongest modulation by fast gamma oscillations were the most important contributors to the early development of theta sequences and that they also displayed a faster form of phase precession within slow gamma cycles nested with theta. The results reported are interesting and support the main conclusions of the authors. However, the manuscript needs significant improvement in several aspects regarding data analysis, description of both experimental and analytical methods, and alternative interpretations, as I detail below.

• The experimental paradigm and recordings should be explained at the beginning of the Results section. Right now, there is no description whatsoever which makes it harder to understand the design of the study.

We thank the reviewer for this kind suggestion.  The description of experimental paradigm and recordings has been added to the beginning of the results section (Lines 114-119).

• An important issue that needs to be addressed is the very small fraction of CA1 cells phased-locked to slow gamma rhythms (3.7%). This fraction is much lower than in many previous studies, that typically report it in the range of 20-50%. However, this discrepancy is not discussed by the authors. This needs to be explained and additional analysis considered. One analysis that I would suggest, although there are also other valid approaches, is to, instead of just analyzing the phase locking in two discrete frequency bands, compute the phase locking will all LFP frequencies from 25-100 Hz. This will offer a more comprehensive and unbiased view of the gamma modulation of place cell firing. Alternative metrics to mean vector length that is less sensitive to firing rates, such as pairwise phase consistency index (Vinck et a., Neuroimage, 2010), could be implemented. This may reveal whether the low fraction of phase-locked cells could be due to a low number of spikes entering the analysis.

We thank the reviewer for this constructive suggestion.  A previous work also on Long-Evans rats showed that the proportion of slow gamma phase-locked cells during novelty exploration was ~20%, however it dropped to ~10% during familiar exploration (Fig.4E, Kitanishi et al., 2015 Neuron).  This suggests that the proportion of slow gamma phase-locked cells may decreased with familiarity of the environment, which supports our data.  In addition, we also calculated the pairwise phase consistency index in terms of the effect of spike counts on MVL.  We could observe that the tendency of PPC (Author response image 2A) and MVL (Author response image 2B) along frequency bands were consistent across different subsets of cells, suggesting that the determination of cell subsets by MVL metric was not biased by the low number of spikes.  These results further shed light to the contribution of slow gamma phase precession of place cells to theta sequence development.

Author response image 2.

• From the methods, it is not clear to me whether the reference LFP channel was consistently selected to be a different one that where the spikes analyzed were taken. This is the better practice to reduce the contribution of spike leakage that could substantially inflate the coupling with faster gamma frequencies. These analyses need to be described in more detail.

We thank the reviewer for pointing this out.  In the main manuscript, we used local LFPs as the cells were recorded from the same tetrode.  In addition, we selected an individual tetrode which located at stratum pyramidale and at the center of the drive bundle for each rat.  We detected a similar proportion of FG-cells by using LFPs on this tetrode, compared with that using local LFPs (Author response image 3A-B, Chi-squared test, χ²= 0.9, p=0.4, Cramer V=0.03).  We further found that the PPC measurement of FG- and NFG-cells were different at fast gamma band by using central LFPs (Author response image 3D), consistent with that by using local LFPs (Author response image 3C).  Therefore, these results suggest that the findings related to fast gamma was not due to the contribution of spike leakage in the local LFPs.  We have updated the description in the manuscript (Lines 553-557, 566-568).

Author response image 3.

• The initial framework of the authors of classifying cells into fast gamma and not fast gamma modulated implies a bimodality that may be artificial. The authors should discuss the nuances and limitations of this framework. For example, several previous work has shown that the same place cell can couple to different gamma oscillations (e.g., Lastoczni et al., Neuron, 2016; Fernandez-Ruiz et al., Neuron, 2017; Sharif et al., Neuron,2021).

We thank the reviewer for this kind suggestion.  We have cited these references and discussed the possibility of bimodal phase-locking in the manuscript (Lines 430-433).

• It would be useful to provide a more thorough characterization of the physiological properties of FG and NFG cells, as this distinction is the basis of the paper. Only very little characterization of some place cell properties is provided in Figure 5. Important characteristics that should be very feasible to compare include average firing rate, burstiness, estimated location within the layer (i.e., deep vs superficial sublayers) and along the transverse axis (i.e., proximal vs distal), theta oscillation frequency, phase precession metrics (given their fundamental relationship with theta sequences), etc.

We thank the reviewer for this constructive suggestion.  In addition to the characterizations shown in Fig5, we also analyzed firing rate, anatomical location and theta modulation to compare the physiological properties of FG- and NFG-cells.

In terms of the firing properties of both types of cells, we found that the mean firing rate of FG-cell was higher than NFG-cell (Fig. 5A, Student's t-test, t(22) = 2.1, p = 0.04, Cohen's D = 0.9), which was consistent with the previous study that the firing rate was higher during fast gamma than during slow gamma (Zheng et al., 2015 Hippocampus).  However, the spike counts of excluded FG- and NFG-cells for decoding were similar (Fig. 5B, Student's t-test, t(22) = 1.2, p = 0.3, Cohen's D = 0.5), suggesting that the differences found in theta sequences cannot be accounted for by different decoding quality related to spike counts.  In addition, we measured the burstiness based on the distribution of inter-spike-intervals, and we found that the bursting probability of spikes was not significantly different between FG and NFG cells (Author response image 4A, Student's t-test, t(22) = 0.6, p=0.5, Cohen's d=0.3).

In terms of theta modulation of cells, we first compared the theta frequency related to the firing of FG and NFG cells.  We detected the instantaneous theta frequency at each spike timing of FG and NFG cells, and found that it was not significantly different between cell types (Author response image 4B, Student's t-test, t(22) = -0.5, p=0.6, Cohen's d=0.2).  In addition, we found the proportion of cells with significant theta phase precession was greater in FG-cells than in NFG-cells (Fig. S2E).  However, the slope and starting phase of theta phase precession was not significantly different between FG and NFG cells (Author response image 4C, Student's t-test, t(21) = 0.3, p=0.8, Cohen's d=0.1; Author response image 4D, Watson-Williams test, F(1,21)=0.5, p=0.5, partial η²=0.02).

In terms of the anatomical location of FG and NFG cells, we identified tetrode traces in slices for each cell.  We found that both FG and NFG cells were recorded from the deep layer of dorsal CA1, with no difference of proportions between cell types (Author response image 4E, Chi-squared test, χ²=0.5, p=0.5, Cramer V=0.05).  The distribution of FG-cells he NFG-cells along the transverse axis was also similar between cell types (Author response image 4F, χ²=0.08, p=0.8, Cramer V=0.02).

Author response image 4.

• It is not clear to me how the analysis in Figure 6 was performed. In Figure 6B I would think that the grey line should connect with the bottom white dot in the third panel, which would be the interpretation of the results.

We thank the reviewer for raising this good point.  The grey line was just for intuitional observation, not a quantitative analysis.  We have removed the grey lines from all heat maps in Fig.6.

Reviewer #3 (Public Review):

[Editors' note: This review contains many criticisms that apply to the whole sub-field of slow/fast gamma oscillations in the hippocampus, as opposed to this particular paper. In the editors' view, these comments are beyond the scope of any single paper. However, they represent a view that, if true, should contextualise the interpretation of this paper and all papers in the sub-field. In doing so, they highlight an ongoing debate within the broader field.]

Summary:

The authors aimed to elucidate the role of dynamic gamma modulation in the development of hippocampal theta sequences, utilizing the traditional framework of "two gammas," a slow and a fast rhythm. This framework is currently being challenged, necessitating further analyses to establish and secure the assumed premises before substantiating the claims made in the present article.

The results are too preliminary and need to integrate contemporary literature. New analyses are required to address these concerns. However, by addressing these issues, it may be possible to produce an impactful manuscript.

We thank the reviewer for raising these important questions in the hippocampal gamma field.  We have done a lot of new analyses according to the comments to strengthen our manuscript.

I. Introduction

Within the introduction, multiple broad assertions are conveyed that serve as the premise for the research. However, equally important citations that are not mentioned potentially contradict the ideas that serve as the foundation. Instances of these are described below:

(1) Are there multiple gammas? The authors launched the study on the premise that two different gamma bands are communicated from CA3 and the entorhinal cortex. However, recent literature suggests otherwise, offering that the slow gamma component may be related to theta harmonics:

From a review by Etter, Carmichael and Williams (2023)

"Gamma-based coherence has been a prominent model for communication across the hippocampal-entorhinal circuit and has classically focused on slow and fast gamma oscillations originating in CA3 and medial entorhinal cortex, respectively. These two distinct gammas are then hypothesized to be integrated into hippocampal CA1 with theta oscillations on a cycle-to-cycle basis (Colgin et al., 2009; Schomburg et al., 2014). This would suggest that theta oscillations in CA1 could serve to partition temporal windows that enable the integration of inputs from these upstream regions using alternating gamma waves (Vinck et al., 2023). However, these models have largely been based on correlations between shifting CA3 and medial entorhinal cortex to CA1 coherence in theta and gamma bands. In vivo, excitatory inputs from the entorhinal cortex to the dentate gyrus are most coherent in the theta band, while gamma oscillations would be generated locally from presumed local inhibitory inputs (Pernía-Andrade and Jonas, 2014). This predominance of theta over gamma coherence has also been reported between hippocampal CA1 and the medial entorhinal cortex (Zhou et al., 2022). Another potential pitfall in the communication-through-coherence hypothesis is that theta oscillations harmonics could overlap with higher frequency bands (Czurkó et al., 1999; Terrazas et al., 2005), including slow gamma (Petersen and Buzsáki, 2020). The asymmetry of theta oscillations (Belluscio et al., 2012) can lead to harmonics that extend into the slow gamma range (Scheffer-Teixeira and Tort, 2016), which may lead to a misattribution as to the origin of slow-gamma coherence and the degree of spike modulation in the gamma range during movement (Zhou et al., 2019)."

And from Benjamin Griffiths and Ole Jensen (2023)

"That said, in both rodent and human studies, measurements of 'slow' gamma oscillations may be susceptible to distortion by theta harmonics [53], meaning open questions remain about what can be attributed to 'slow' gamma oscillations and what is attributable to theta."

This second statement should be heavily considered as it is from one of the original authors who reported the existence of slow gamma.

Yet another instance from Schomburg, Fernández-Ruiz, Mizuseki, Berényi, Anastassiou, Christof Koch, and Buzsáki (2014):

"Note that modulation from 20-30 Hz may not be related to gamma activity but, instead, reflect timing relationships with non-sinusoidal features of theta waves (Belluscio et al., 2012) and/or the 3rd theta harmonic."

One of this manuscript's authors is Fernández-Ruiz, a contemporary proponent of the multiple gamma theory. Thus, the modulation to slow gamma offered in the present manuscript may actually be related to theta harmonics.

With the above emphasis from proponents of the slow/fast gamma theory on disambiguating harmonics from slow gamma, our first suggestion to the authors is that they A) address these statements (citing the work of these authors in their manuscript) and B) demonstrably quantify theta harmonics in relation to slow gamma prior to making assertions of phase relationships (methodological suggestions below). As the frequency of theta harmonics can extend as high as 56 Hz (PMID: 32297752), overlapping with the slow gamma range defined here (25-45 Hz), it will be important to establish an approach that decouples the two phenomena using an approach other than an arbitrary frequency boundary.

We agree with the reviewer that the theta oscillations harmonics could overlap with higher frequency bands including slow gamma, as the above reviews discussed.  In order to rule out the possibility of theta harmonics effects in this study, we added new analyses in this letter (see below).

(2) Can gammas be segregated into different lamina of the hippocampus? This idea appears to be foundational in the premise of the research but is also undergoing revision.

As discussed by Etter et al. above, the initial theory of gamma routing was launched on coherence values. However, the values reported by Colgin et al. (2009) lean more towards incoherence (a value of 0) rather than coherence (1), suggesting a weak to negligible interaction. Nevertheless, this theory is coupled with the idea that the different gamma frequencies are exclusive to the specific lamina of the hippocampus.

Recently, Deschamps et al. (2024) suggested a broader, more nuanced understanding of gamma oscillations than previously thought, emphasizing their wide range and variability across hippocampal layers. This perspective challenges the traditional dichotomy of gamma sub-bands (e.g., slow vs. medium gamma) and their associated cognitive functions based on a more rigid classification according to frequency and phase relative to the theta rhythm. Moreover, they observed all frequencies across all layers.

Similarly, the current source density plots from Belluscio et al. (2012) suggest that SG and FG can be observed in both the radiatum and lacunosum-moleculare.

Therefore, if the initial coherence values are weak to negligible and both slow and fast gamma are observed in all layers of the hippocampus, can the different gammas be exclusively related to either anatomical inputs or psychological functions (as done in the present manuscript)? Do these observations challenge the authors' premise of their research? At the least, please discuss.

We thank the reviewer for raising this point, which I believe still remains controversial in this field.  We also thank the reviewer for providing detailed proofs of existence forms of gamma rhythms.  The reviewer was considering 2 aspects of gamma: 1) the reasonability of dividing slow and fast gamma by specific frequency bands; 2) the existence of gamma across all hippocampal layers, which challenged the functional significance of different types of gamma rhythms.  Although the results in Douchamps et al., 2024 challenged the idea of rigid gamma sub-bands, we still could see separate slow and fast gamma components exclusively occurred along time course, with central frequency of slow gamma lower than ~60Hz and central frequency of fast gamma higher than ~60Hz (Fig.1b of Douchamps et al., 2024).  This was also seen in the rat dataset of this reference (Fig. S3).  Since their behavioral test required both memory encoding and retrieval processes, it was hard to distinguish the role of different gamma components as they may dynamically coordinate during complex memory process.  Thus, although the behavioral performance can be decoded from broad range of gamma, we still cannot deny the existence of difference gamma rhythms and their functional significance during difference memory phases.

(3) Do place cells, phase precession, and theta sequences require input from afferent regions? It is offered in the introduction that "Fast gamma (~65-100Hz), associated with the input from the medial entorhinal cortex, is thought to rapidly encode ongoing novel information in the context (Fernandez-Ruiz et al., 2021; Kemere, Carr, Karlsson, & Frank, 2013; Zheng et al., 2016)".

CA1 place fields remain fairly intact following MEC inactivation include Ipshita Zutshi, Manuel Valero, Antonio Fernández-Ruiz , and György Buzsáki (2022)- "CA1 place cells and assemblies persist despite combined mEC and CA3 silencing" and from Hadas E Sloin, Lidor Spivak, Amir Levi, Roni Gattegno, Shirly Someck, Eran Stark (2024) - "These findings are incompatible with precession models based on inheritance, dual-input, spreading activation, inhibition-excitation summation, or somato-dendritic competition. Thus, a precession generator resides locally within CA1."

These publications, at the least, challenge the inheritance model by which the afferent input controls CA1 place field spike timing. The research premise offered by the authors is couched in the logic of inheritance, when the effect that the authors are observing could be governed by local intrinsic activity (e.g., phase precession and gamma are locally generated, and the attribution to routed input is perhaps erroneous). Certainly, it is worth discussing these manuscripts in the context of the present manuscript.

We thank the review for this discussion.  The main purpose of our current study is to investigate the mechanism of theta sequence development along with learning, which may or may not dependent on theta phase precession of single place cells as it remains controversial in this field.  Also, there is a limitation in this study that all gamma components were recorded from stratum pyramidale, thus we cannot make any conclusion on the originate of gamma in modulating sequence development.

II. Results

(1) Figure 2-

a. There is a bit of a puzzle here that should be discussed. If slow and fast frequencies modulate 25% of neurons, how can these rhythms serve as mechanisms of communication/support psychological functions? For instance, if fast gamma is engaged in rapid encoding (line 72) and slow gamma is related to the integration processing of learned information (line 84), and these are functions of the hippocampus, then why do these rhythms modulate so few cells? Is this to say 75% of CA1 neurons do not listen to CA3 or MEC input?

The proportion ~25% was the part of place cells phase-locked to either slow or fast gamma.  However, one of the main findings in this study was that most cells were modulated by slow gamma as they fired at precessed slow gamma phase within a theta cycle (Figs 6-8), which would promote information compression for theta sequence development.  Therefore, we didn’t mean that only a small proportion of cells were modulated by gamma rhythms and contributed to this process.

b. Figure 2. It is hard to know if the mean vector lengths presented are large or small. Moreover, one can expect to find significance due to chance. For instance, it is challenging to find a frequency in which modulation strength is zero (please see Figure 4 of PMID: 30428340 or Figure 7 of PMID: 31324673).

i. Please construct the histograms of Mean Vector Length as in the above papers, using 1 Hz filter steps from 1-120Hz and include it as part of Figure 2 (i.e., calculate the mean vector length for the filtered LFP in steps of 1-2 Hz, 2-3 Hz, 3-4 Hz,... etc). This should help the authors portray the amount of modulation these neurons have relative to the theta rhythm and other frequencies. If the theta mean vector length is higher, should it be considered the primary modulatory influence of these neurons (with slow and fast gammas as a minor influence)?

We thank the review for this suggestion.  We measured the mean vector length at 5Hz step (equivalent to 1Hz step), and we found that the FG-cells were phase-locked to fast gamma rhythms even stronger than that to theta (Author response image 2B, mean MVL of theta=0.126±0.007, mean MVL of theta=0.175±0.006, paired t-test, t(112)=-5.9, p=0.01, Cohen's d=0.7).  In addition, in some previous studies with significant fast gamma phase locking, the MVL values were around 0.15 by using broad gamma band (Kitanishi et al., 2015 Neuron, Lasztóczi et al., 2016 Neuron, Tomar et al., 2021 Front Behav Neurosci, and Asiminas et al., 2022 Molecular Autism), which was consistent with the value in this study.  Therefore, we don’t believe that fast gamma was only a minor influence of these neurons.

ii. It is possible to infer a neuron's degree of oscillatory modulation without using the LFP. For instance, one can create an ISI histogram as done in Figure 1 here (https://www.biorxiv.org/content/10.1101/2021.09.20.461152v3.full.pdf+html; "Distinct ground state and activated state modes of firing in forebrain neurons"). The reciprocal of the ISI values would be "instantaneous spike frequency". In favor of the Douchamps et al. (2024) results, the figure of the BioRXiV paper implies that there is a single gamma frequency modulate as there is only a single bump in the ISIs in the 10^-1.5 to 10^-2 range. Therefore, to vet the slow gamma results and the premise of two gammas offered in the introduction, it would be worth including this analysis as part of Figure 2.

By using suggested method, we calculated the ISI distribution on log scale for FG-cells and NFG-cells during behavior (Author response image 5).  We could observe that the ISI distribution of FG-cells had a bump in the 10^-1.5= to 10^-2= range (black bar), in particular in the fast gamma range (10^-2= to 10^-1.8=).

Author response image 5.

c. There are some things generally concerning about Figure 2.

i. First, the raw trace does not seem to have clear theta epochs (it is challenging to ascertain the start and end of a theta cycle). Certainly, it would be worth highlighting the relationship between theta and the gammas and picking a nice theta epoch.

We thank the review for this suggestion.  We've updated this figure with a nice theta epoch in the revised manuscript.

ii. Also, in panel A, there looks to be a declining amplitude relationship between the raw, fast, and slow gamma traces, assuming that the scale bars represent 100uV in all three traces. The raw trace is significantly larger than the fast gamma. However, this relationship does not seem to be the case in panel B (in which both the raw and unfiltered examples of slow and fast gamma appear to be equal; the right panels of B suggest that fast gamma is larger than slow, appearing to contradict the A= 1/f organization of the power spectral density). Please explain as to why this occurs. Including the power spectral density (see below) should resolve some of this.

We thank the review for pointing this out.  The scales of y-axis of LFPs tracs in Fig.2B was not consistent, which mislead the comparison of amplitude between slow and fast gamma.  We have unified y axis scales across different gamma types in the revised manuscript.  Moreover, we also have replaced these examples with more typical ones (also see the response below).

iii. Within the example of spiking to phase in the left side of Panel B (fast gamma example)- the neuron appears to fire near the trough twice, near the peak twice, and somewhere in between once. A similar relationship is observed for the slow gamma epoch. One would conclude from these plots that the interaction of the neuron with the two rhythms is the same. However, the mean vector lengths and histograms below these plots suggest a different story in which the neuron is modulated by FG but not SG. Please reconcile this.

We thank the review for pointing this out.  We found that the fast gamma phase locking was robust across FG-cells with fast gamma peak as the preferred phase.  Therefore, we have replaced these examples with more typical ones, so that the examples were consistent with the group effect.

iv. For calculating the MVL, it seems that the number of spikes that the neuron fires would play a significant role. Working towards our next point, there may be a bias of finding a relationship if there are too few spikes (spurious clustering due to sparse data) and/or higher coupling values for higher firing rate cells (cells with higher firing rates will clearly show a relationship), forming a sort of inverse Yerkes-Dodson curve. Also, without understanding the magnitude of the MVL relative to other frequencies, it may be that these values are indeed larger than zero, but not biologically significant.

- Please provide a scatter plot of Neuron MVL versus the Neuron's Firing Rate for 1) theta (7-9 Hz), 2) slow gamma, and 3) fast gamma, along with their line of best fit.

- Please run a shuffle control where the LFP trace is shifted by random values between 125-1000ms and recalculate the MVL for theta, slow, and fast gamma. Often, these shuffle controls are done between 100-1000 times (see cross-correlation analyses of Fujisawa, Buzsaki et al.).

- To establish that firing rate does not play a role in uncovering modulation, it would be worth conducting a spike number control, reducing the number of spikes per cell so that they are all equal before calculating the phase plots/MVL.

We thank the review for raising this point.  Beside of the MVL value, we also calculated the pairwise phase consistency (PPC) as suggested by Reviewer2, which is not sensitive to the spike counts.  We found that the phase locking strength to either rhythm (theta or gamma) was comparable between MVL and PPC measurements (Author response image 2).  Moreover, we quantified the relationship between MVL and mean firing rate, as suggested.  We found that the MVL value for theta, slow gamma and fast gamma was negatively correlated with mean firing rate (Author response image 6, Pearson correlation, theta: R²= 0.06, Pearson’s r=-0.3, p=1.3×10^-8=; slow gamma: R²= 0.1, Pearson’s r=-0.4, p=2.4×10^-17=; fast gamma: R²= 0.03, Pearson’s r=-0.2, p=4.3×10^-5=).  These results help us rule out the concerns of the effect of spikes counts on the phase modulation measurement.

Author response image 6.

(2) Something that I anticipated to see addressed in the manuscript was the study from Grosmark and Buzsaki (2016): "Cell assembly sequences during learning are "replayed" during hippocampal ripples and contribute to the consolidation of episodic memories. However, neuronal sequences may also reflect preexisting dynamics. We report that sequences of place-cell firing in a novel environment are formed from a combination of the contributions of a rigid, predominantly fast-firing subset of pyramidal neurons with low spatial specificity and limited change across sleep-experience-sleep and a slow-firing plastic subset. Slow-firing cells, rather than fast-firing cells, gained high place specificity during exploration, elevated their association with ripples, and showed increased bursting and temporal coactivation during postexperience sleep. Thus, slow- and fast-firing neurons, although forming a continuous distribution, have different coding and plastic properties."

My concern is that much of the reported results in the present manuscript appear to recapitulate the observations of Grosmark and Buzsaki, but without accounting for differences in firing rate. A parsimonious alternative explanation for what is observed in the present manuscript is that high firing rate neurons, more integrated into the local network and orchestrating local gamma activity (PING), exhibit more coupling to theta and gamma. In this alternative perspective, it's not something special about how the neurons are entrained to the routed fast gamma, but that the higher firing rate neurons are better able to engage and entrain their local interneurons and, thus modulate local gamma. However, this interpretation challenges the discussion around the importance of fast gamma routed from the MEC.

a. Please integrate the Grosmark & Buzsaki paper into the discussion.

b. Also, please provide data that refutes or supports the alternative hypothesis in which the high firing rate cells are just more gamma modulated as they orchestrate local gamma activity through monosynaptic connections with local interneurons (e.g., Marshall et al., 2002, Hippocampal pyramidal cell-interneuron spike transmission is frequency dependent and responsible for place modulation of interneuron discharge). Otherwise, the attribution to a MEC routed fast gamma routing seems tenuous.

c. It is mentioned that fast-spiking interneurons were removed from the analysis. It would be worth including these cells, calculating the MVL in 1 Hz increments as well as the reciprocal of their ISIs (described above).

We thank the review for this suggestion.  Because we found the mean firing rate of FG-cells was higher than that of NFG-cells, it would be possible that the FG-cells are mainly overlapped with fast-firing cells (rigid cells) in Grosmark et al., 2016 Science.  Actually, in this study, we aimed to investigate how fast and slow gamma rhythms modulated neurons dynamically during learning, rather than defining new cell types.  Thus, we don’t think this work was just a replication of the previous publication.  We have added this description in the Discussion part (Lines 439-441).  In addition, we don’t have enough number of interneurons to support the analysis between interneurons and place cells.  Therefore, we couldn’t make any statement about where was the fast gamma originated (CA1 locally or routed from MEC) in this study.

(3) Methods - Spectral decomposition and Theta Harmonics.

a. It is challenging to interpret the exact parameters that the authors used for their multi-taper analysis in the methods (lines 516-526). Tallon-Baudry et al., (1997; Oscillatory γ-Band (30-70 Hz) Activity Induced by a Visual Search Task in Humans) discuss a time-frequency trade-off where frequency resolution changes with different temporal windows of analysis. This trade-off between time and frequency resolution is well known as the uncertainty principle of signal analysis, transcending all decomposition methods. It is not only a function of wavelet or FFT, and multi-tapers do not directly address this. (The multitaper method, by using multiple specially designed tapers -like the Slepian sequences- smooths the spectrum. This smoothing doesn't eliminate leakage but distributes its impact across multiple estimates). Given the brevity of methods and the issues of theta harmonics as offered above, it is worth including some benchmark trace testing for the multi-taper as part of the supplemental figures.

i. Please spectrally decompose an asymmetric 8 Hz sawtooth wave showing the trace and the related power spectral density using the multiple taper method discussed in the methods.

ii. Please also do the same for an elliptical oscillation (perfectly symmetrical waves, but also capable of casting harmonics). Matlab code on how to generate this time series is provided below:

A = 1; % Amplitude

T = 1/8; % Period corresponding to 8 Hz frequency

omega = 2*pi/T; % Angular frequency

C = 1; % Wave speed

m = 0.9; % Modulus for the elliptic function (0<m<1 for cnoidal waves)

x = linspace(0, 2*pi, 1000); % temporal domain

t = 0; % Time instant

% Calculate B based on frequency and speed

B = sqrt(omega/C);

% Cnoidal wave equation using the Jacobi elliptic function

u = A .* ellipj(B.*(x - C*t), m).^2;

% Plotting the cnoidal wave

figure;

plot(x./max(x), u);

title('8 Hz Cnoidal Wave');

xlabel('time (x)');

ylabel('Wave amplitude (u)');

grid on;

The Symbolic Math Toolbox needs to be installed and accessible in your MATLAB environment to use ellipj. Otherwise, I trust that, rather than plotting a periodic orbit around a circle (sin wave) the authors can trace the movement around an ellipse with significant eccentricity (the distance between the two foci should be twice the distance between the co-vertices).

We thank the review for this suggestion.  In the main text of manuscript, we only applied Morlet's wavelet method to calculate the time varying power of rhythms.  Multitaper method was used for the estimation of power spectra across running speeds, which was shown in the manuscript.  Therefore, we removed the description of Multitaper method and updated the Morlet's wavelet power spectral analysis in the Methods (Lines 541-544).

As suggested, we estimated the power spectral densities of 8 Hz sawtooth and elliptical oscillation by using these methods, and compared them with the results from FFT.  We found that both the Multitaper's and Morlet's wavelet methods could well capture the 8Hz oscillatory components (Author response image 7).  However, we could observe harmonic components from FFT spectrum.

Author response image 7.

iii. Line 522: "The power spectra across running speeds and absolute power spectrum (both results were not shown).". Given the potential complications of multi-taper discussed above, and as each convolution further removes one from the raw data, it would be the most transparent, simple, and straightforward to provide power spectra using the simple fft.m code in Matlab (We imagine that the authors will agree that the results should be robust against different spectral decomposition methods. Otherwise, it is concerning that the results depend on the algorithm implemented and should be discussed. If gamma transience is a concern, the authors should trigger to 2-second epochs in which slow/fast gamma exceeds 3-7 std. dev. above the mean, comparing those resulting power spectra to 2-second epochs with ripples - also a transient event). The time series should be at least 2 seconds in length (to avoid spectral leakage issues and the issues discussed in Talon-Baudry et al., 1997 above).

Please show the unmolested power spectra (Y-axis units in mV2/Hz, X-axis units as Hz) as a function of running speed (increments of 5 cm/s) for each animal. I imagine three of these PSDs for 3 of the animals will appear in supplemental methods while one will serve as a nice manuscript figure. With this plot, please highlight the regions that the authors are describing as theta, slow, and fast gamma. Also, any issues should be addressed should there be notable differences in power across animals or tetrodes (issues with locations along proximal-distal CA1 in terms of MEC/LEC input and using a local reference electrode are discussed below).

As suggested, we firstly estimated the power spectra as a function of running speeds in each running lap, and showed them separately for each rat, by using the multitaper spectral analysis (Author response image 8).  In addition, to achieve unmolested power spectra, the short-time Fourier transform (STFT) was used for this analysis at the same frequency resolution (Author response image 9).  We could see that the power spectra were consistent between these two methods.  Notably, there seems no significant theta harmonic component in the slow gamma band range.

The multitaper spectral analysis was performed as follows.  The power spectra were measured across different running speeds as described previously (Ahmed et al., 2012 J Neurosci; Zheng et al., 2015 Hippocampus; Zheng et al., 2016 eNeuro).  Briefly, the absolute power spectrum was calculated for 0.5s moving window and 0.2s step size of the LFPs recordings each lap, using the multitaper spectral analysis in the Chronux toolbox (Mitra and Bokil, 2008, http://chronux.org/) and STFT spectral analysis in Matlab script stft.m.  In the multitaper method, the time-bandwidth product parameter (TW) was set at 3, and the number of tapers (K) was set at 5.  In the STFT method, the FFT length was set at 2048, which was equivalent with the parameters used in multitaper method.  Running speed was calculated (see “Estimation of running speed and head direction” section in the manuscript) and averaged within each 0.5s time window corresponding to the LFP segments.  Then, the absolute power at each frequency was smoothed with a Gaussian kernel centered on given speed bin.  The power spectral as a function of running speed and frequency were plotted in log scale.  Also, the colormap was in log scale, allowing for comparisons across different frequencies that would otherwise be difficult due to the 1/f decay of power in physiological signals.

Author response image 8.

Author response image 9.

iv. Schomberg and colleagues (2014) suggested that the modulation of neurons in the slow gamma range could be related to theta harmonics (see above). Harmonics can often extend in a near infinite as they regress into the 1/f background (contributing to power, but without a peak above the power spectral density slope), making arbitrary frequency limits inappropriate. Therefore, in order to support the analyses and assertions regarding slow gamma, it seems necessary to calculate a "theta harmonic/slow gamma ratio". Aru et al. (2015; Untangling cross-frequency coupling in neuroscience) offer that: " The presence of harmonics in the signal should be tested by a bicoherence analysis and its contribution to CFC should be discussed." Please test both the synthetic signals above and the raw LFP, using temporal windows of greater than 4 seconds (again, the large window optimizes for frequency resolution in the time-frequency trade-off) to calculate the bicoherence. As harmonics are integers of theta coupled to itself and slow gamma is also coupled to theta, a nice illustration and contribution to the field would be a method that uses the bispectrum to isolate and create a "slow gamma/harmonic" ratio.

We thank the reviewer for providing the method regarding on the theta harmonics.  We firstly measured the theta harmonics on the synthesized signal by using the biphasic coherence method, and we could clearly observe the nonlinear coupling between theta rhythm and its harmonics (Author response image 10).

Author response image 10.

In addition, we also measured the bicoherence on raw traces during slow gamma episodes.  We did not see nonlinear coupling between slow gamma and theta bands in this real data (mean bicoherence=0.1±0.0002) compared with that in the synthesized signal (mean bicoherence=0.7 for elliptical waves and 0.5 for sawtooth waves), suggesting that the slow gamma detected in this study was not pure theta harmonic (Author response image 11C, F, I, in red boxes).  Therefore, we believe that the contribution of theta harmonic in slow gamma is not significant.

Author response image 11.

(4) I appreciate the inclusion of the histology for the 4 animals. Knerim and colleagues describe a difference in MEC projection along the proximal-distal axis of the CA1 region (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC3866456/)- "There are also differences in their direct projections along the transverse axis of CA1, as the LEC innervates the region of CA1 closer to the subiculum (distal CA1), whereas the MEC innervates the region of CA1 closer to CA2 and CA3 (proximal CA1)" From the histology, it looks like some of the electrodes are in the part of CA1 that would be dominated by LEC input while a few are closer to where the MEC would project.

a. How do the authors control for these differences in projections? Wouldn't this change whether or not fast gamma is observed in CA1?

b. I am only aware of one manuscript that describes slow gamma in the LEC which appeared in contrast to fast gamma from the MEC (https://www.science.org/doi/10.1126/science.abf3119). One would surmise that the authors in the present manuscript would have varying levels of fast gamma in their CA1 recordings depending on the location of the electrodes in the Proximal-distal axis, to the extent that some of the more medial tetrodes may need to be excluded (as they should not have fast gamma, rather they should be exclusively dominated by slow gamma). Alternatively, the authors may find that there is equal fast gamma power across the entire proximal-distal axis. However, this would pose a significant challenge to the LEC/slow gamma and MEC/fast gamma routing story of Fernandez-Ruiz et al. and require reconciliation/discussion.

c. Is there a difference in neuron modulation to these frequencies based on electrode location in CA1?

We thank the reviewer for this concern, which was also raised by Reviewer2.  We aligned the physical location of LFP channels in the proximal-distal axis based on histology.  In our dataset, only 2 rats were recorded from both distal and proximal hippocampus, so we calculated the gamma power from both sites in these rats.  We found that slow power was higher from proximal tetrodes than that from distal tetrodes (Author response image 12, repeated measure ANOVA, F(1,7)=10.2, p=0.02, partial η ²=0.8).  However, fast gamma power were similar between different recording sites (F(1,7)=0.008, p=0.9, partial η ²=0.001).  These results are partially consistent with the LEC/slow gamma and MEC/fast gamma routing story of Fernandez-Ruiz’s work.  The main reason would be that all LFPs were recorded from tetrodes in stratum pyramidale, deep layer in particular (Author response image 4E), so that it was hard to precisely identify their distance to distal/proximal apical dendrites.

Author response image 12.

In terms of the anatomical location of FG and NFG cells, we identified tetrode traces in slices for each cell.  We found that both FG and NFG cells were recorded from the deep layer of dorsal CA1, with no difference of proportions between cell types (Author response image 4E, Chi-squared test, χ²=0.5, p=0.5, Cramer V=0.05).  The distribution of FG-cells he NFG-cells along the transverse axis was also similar between cell types (Author response image 4F, χ²=0.08, p=0.8, Cramer V=0.02).

(5) Given a comment in the discussion (see below), it will be worth exploring changes in theta, theta harmonic, slow gamma, and fast gamma power with running speed as no changes were observed with theta sequences or lap number versus. Notably, Czurko et al., report an increase in theta and harmonic power with running speed (1999) while Ahmed and Mehta (2012) report a similar effect for gamma.

a. Please determine if the oscillations change in power and frequency of the rhythms discussed above change with running speed using the same parameters applied in the present manuscript. The specific concern is that how the authors calculate running speed is not sensitive enough to evaluate changes.

We thank the reviewer for this suggestion.  The description of running speed quantification has been updated in the Method (see “Estimation of running speed and head direction” section, Lines 501-511).  Overall, the sample frequency of running speed was25Hz which would be sensitive enough to evaluate the behavioral changes.

By measuring the rhythmic power changing as a function of running speed (Author response image 8 and Author response image 9), we could observe that theta power was increased as running speed getting higher.  Consistent with the results in (Ahmed and Mehta, 2012) and our previous study (Zheng et al., 2015), the fast gamma power was increasing and slow gamma power was decreasing when running speed was getting high.

In addition, we also estimated the rhythmic frequency as a function of running speed in the slow and fast episodes respectively.  We found that fast gamma frequency was increased with running speed (Author response image 13, linear regression, R²=0.4, corr=0.6, p=9.9×10^-15), whereas slow gamma frequency was decreased with running speed (R²=0.2, corr=-0.4, p=8.8×10^-6).  Although significant correlation was found between gamma frequency and running speed, consistent with the previous studies, the frequency change (~70-75Hz for fast gamma and ~30-28Hz for slow gamma) was not big enough to affect the sequence findings in this study.  In additiontheta frequency was maintained in either slow episodes (R²=0.02, corr=-0.1, p=0.1) or fast episodes (R²=0.004, corr=0.06, p=0.5), consistent with results in Fig.1G of Kropff et al., 2021 Neuron.

Author response image 13.

b. It is astounding that animals ran as fast as they did in what appears to be the first lap (Figure 3F), especially as rats' natural proclivity is thigmotaxis and inquisitive exploration in novel environments. Can the authors expand on why they believe their rats ran so quickly on the first lap in a novel environment and how to replicate this? Also, please include the individual values for each animal on the same plot.

We thank the reviewer for pointing this out.  The task was not brand new to rats in this dataset, because only days with good enough recording quality for sequence decoding were included in this paper, which were about day2-day10 for each rat.  However, we still observed the process of sequence formation because of the rat’s exploration interest during early laps.  Thus, in terms exploration behaviors, the rats ran at relative high speeds across laps (Author response image 14, each gray line represents the running speed within an individual session).

Author response image 14.

c. Can the authors explain how the statistics on line 169 (F(4,44)) work? Specifically, it is challenging to determine how the degrees of freedom were calculated in this case and throughout if there were only 4 animals (reported in methods) over 5 laps (depicted in Figure 3F. Given line 439, it looks like trials and laps are used synonymously). Four animals over 5 laps should have a DOF of 16.

This statistic result was performed with each session/day as a sample (n=12 sessions/days).  The statistics were generated by repeated measures ANOVA on 5 trials in 12 sessions, with a DOF of 44.

(6) Throughout the manuscript, I am concerned about an inflation of statistical power. For example on line 162, F(2,4844). The large degrees of freedom indicate that the sample size was theta sequences or a number of cells. Since multiple observations were obtained from the same animal, the statistical assumption of independence is violated. Therefore, the stats need to be conducted using a nested model as described in Aarts et al. (2014; https://pubmed.ncbi.nlm.nih.gov/24671065/). A statistical consult may be warranted.

We thank the reviewer for this suggestion.  We have replaced this statistic result by using generalized linear mixed model with ratID being a covariate.  These results have been updated in the revised manuscript (Lines 164-167).

(7) It is stated that one tetrode served as a quiet recording reference. The "quiet" part is an assumption when often, theta and gamma can be volume conducted to the cortex (e.g., Sirota et al., 2008; This is often why laboratories that study hippocampal rhythms use the cerebellum for the differential recording electrode and not an electrode in the corpus callosum). Generally, high frequencies propagate as well as low frequencies in the extracellular milieu (https://www.eneuro.org/content/4/1/ENEURO.0291-16.2016). For transparency, the authors should include a limitation paragraph in their discussion that describes how their local tetrode reference may be inadvertently diminishing and/or distorting the signal that they are trying to isolate. Otherwise, it would be worth hearing an explanation as to how the author's approach avoids this issue.

In terms of the locations of references, we had 2 screws above the cerebellum in the skull connected to the recording drive ground, and 1 tetrode in a quiet area of the cortex serving as the recording reference.  We agree that the theta and gamma can be volume conducted to the cortex which may affect the power of these rhythms in the stratum pyramidale.  However, we didn’t mean to measure or compare the absolute theta or gamma power in this study, as we only cared about the phase modulation of gamma to place cells.  Therefore, we believe the location of recording reference would not make significant effect on our conclusion.

Apologetically, this review is already getting long. Moreover, I have substantial concerns that should be resolved prior to delving into the remainder of the analyses. e.g., the analyses related to Figure 3-5 assert that FG cells are important for sequences. However, the relationship to gamma may be secondary to either their relationship to theta or, based on the Grosmark and Buzsaki paper, it may just be a phenomenon coupled to the fast-firing cells (fast-firing cells showing higher gamma modulation due to a local PING dynamic). Moreover, the observation of slow gamma is being challenged as theta harmonics, even by the major proponents of the slow/fast gamma theory. Therefore, the report of slow gamma precession would come as an unsurprising extension should they be revealed to be theta harmonics (however, no control for harmonics was implemented; suggestions were made above). Following these amendments, I would be grateful for the opportunity to provide further feedback.

III. Discussion.

a. Line 330- it was offered that fast gamma encodes information while slow gamma integrates in the introduction. However, in a task such as circular track running (from the methods, it appears that there is no new information to be acquired within a trial), one would guess that after the first few laps, slow gamma would be the dominant rhythm. Therefore, one must wonder why there are so few neurons modulated by slow gamma (~3.7%).

The proportion of ~3.7% was the part of place cells phase-locked to slow gamma.  However, we aimed to find that the slow gamma phase precession of place cells promoted the theta sequence development.  We would not expect the cells phase-locked to slow gamma if phase precession occurred.

b. Line 375: The authors contend that: "...slow gamma, related to information compression, was also required to modulate fast gamma phase-locked cells during sequence development. We replicated the results of slow gamma phase precession at the ensemble level (Zheng et al., 2016), and furthermore observed it at late development, but not early development, of theta sequences." In relation to the idea that slow gamma may be coupled to - if not a distorted representation of - theta harmonics, it has been observed that there are changes in theta relative to novelty.

i. A. Jeewajee, C. Lever, S. Burton, J. O'Keefe, and N. Burgess (2008) report a decrease in theta frequency in novel circumstances that disappears with increasing familiarity.

ii. One could surmise that this change in frequency is associated with alterations in theta harmonics (observed here as slow gamma), challenging the author's interpretation.

iii. Therefore, the authors have a compelling opportunity to replicate the results of Jeewajee et al., characterizing changes of theta along with the development of slow gamma precession, as the environment becomes familiar. It will become important to demonstrate, using bicoherence as offered by Aru et al., how slow gamma can be disambiguated from theta harmonics. Specifically, we anticipate that the authors will be able to quantify A) theta harmonics (the number, and their respective frequencies and amplitudes), B) the frequency and amplitude of slow gamma, and C) how they can be quantitatively decoupled. Through this, their discussion of oscillatory changes with novelty-familiarity will garner a significant impact.

We think we have demonstrated that the slow gamma observed in this study was not purely theta harmonics.  We didn’t focus on the frequency change of slow gamma or theta rhythms in this study.  Further investigation will be carried out on this topic in the future.

c. Broadly, it is interesting that the authors emphasize the gamma frequency throughout the discussion. Given that the power spectral density of the Local Field Potential (LFP) exhibits a log-log relationship between amplitude and frequency, as described by Buzsáki (2005) in "Rhythms of the Brain," and considering that the LFP is primarily generated through synaptic transmembrane currents (Buzsáki et al., 2012), it seems parsimonious to consider that the bulk of synaptic activity occurs at lower frequencies (e.g., theta). Since synaptic transmission represents the most direct form of inter-regional communication, one might wonder why gamma (characterized by lower amplitude rhythms) is esteemed so highly compared to the higher amplitude theta rhythm. Why isn't the theta rhythm, instead, regarded as the primary mode of communication across brain regions? A discussion exploring this question would be beneficial.

We thank the reviewer for this deep thinking.  When stating the conclusion on gamma rhythms, we didn’t mean to weaken the role of theta rhythm.  Conversely, the fast or slow gamma episodes were detected riding on theta rhythms, and we believe that the information compression should occur at a finer scale within a theta cycle scale.  More investigation will be carried out on this topic in the future.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) It is helpful to clearly define "FG-cell sequences" before the relevant results are described in the Results section. More importantly, the seemingly conflicting results between Figure 3 and Figure 8 may need to be clarified.

The “exFG-sequences and exNFG sequences”, “FG-cell sequences and NFG-cell sequences” have been defined clearly in the revised manuscript.  Moreover, the seemingly conflicting results between Figure 3 and Figure 8 have been interpreted properly.

(2) It is helpful to clearly state the N and what defines a sample whenever a result is described.

In each statistical results, the N and what defines a sample have been clarified in the revised manuscript.

(3) Addressing the questions regarding the methods (#5) would clarify some of the results.

The questions regarding the Methods part has addressed in the revised manuscript.

(4) Line #244: "successful" should be "successive"?

Fixed.

Reviewer #2 (Recommendations For The Authors):

- The writing of the manuscript can be substantially improved.

The manuscript can be substantially revised and updated.

- I noticed that the last author of the manuscript is not the lead or corresponding and has only provided a limited contribution to this work (according to the detailed author contributions). The second to last author seems to be the main senior intellectual contributor and supervisor, together with the third to last author. This speaks of potential bad academic practices where a senior person whose intellectual contribution to the study is relatively minor takes the last author position, against the standard conventions on authorship worldwide. I strongly suggest that this is corrected.

We thank the reviewer for raising this problem.  The last author Dr. Ming was also a senior author and supervised this project with large contribution.  We have fixed his role as a co-corresponding author in the revised manuscript.

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

Qin et al. set out to investigate the role of mechanosensory feedback during swallowing and identify neural circuits that generate ingestion rhythms. They use Drosophila melanogaster swallowing as a model system, focusing their study on the neural mechanisms that control cibarium filling and emptying in vivo. They find that pump frequency is decreased in mutants of three mechanotransduction genes (nompC, piezo, and Tmc), and conclude that mechanosensation mainly contributes to the emptying phase of swallowing. Furthermore, they find that double mutants of nompC and Tmc have more pronounced cibarium pumping defects than either single mutants or Tmc/piezo double mutants. They discover that the expression patterns of nompC and Tmc overlap in two classes of neurons, md-C and md-L neurons. The dendrites of md-C neurons warp the cibarium and project their axons to the subesophageal zone of the brain. Silencing neurons that express both nompC and Tmc leads to severe ingestion defects, with decreased cibarium emptying. Optogenetic activation of the same population of neurons inhibited filling of the cibarium and accelerated cibarium emptying. In the brain, the axons of nompC∩Tmc cell types respond during ingestion of sugar but do not respond when the entire fly head is passively exposed to sucrose. Finally, the authors show that nompC∩Tmc cell types arborize close to the dendrites of motor neurons that are required for swallowing, and that swallowing motor neurons respond to the activation of the entire Tmc-GAL4 pattern.

Strengths:

• The authors rigorously quantify ingestion behavior to convincingly demonstrate the importance of mechanosensory genes in the control of swallowing rhythms and cibarium filling and emptying

• The authors demonstrate that a small population of neurons that express both nompC and Tmc oppositely regulate cibarium emptying and filling when inhibited or activated, respectively

• They provide evidence that the action of multiple mechanotransduction genes may converge in common cell types

Thank you for your insightful and detailed assessment of our work. Your constructive feedback will help to improve our manuscript.

Weaknesses:

• A major weakness of the paper is that the authors use reagents that are expressed in both md-C and md-L but describe the results as though only md-C is manipulated-Severing the labellum will not prevent optogenetic activation of md-L from triggering neural responses downstream of md-L. Optogenetic activation is strong enough to trigger action potentials in the remaining axons. Therefore, Qin et al. do not present convincing evidence that the defects they see in pumping can be specifically attributed to md-C.

Thank you for your comments. This is important point that we did not adequately address in the original preprint. We have obtained imaging and behavioral results that strongly suggest md-C, rather than md-L, are essential for swallowing behavior.

36 hours after the ablation of the labellum, the signals of md-L were hardly observable when GFP expression was driven by the intersection between Tmc-GAL4 & nompC-QF (see F Figure 3—figure supplement 1A). This observation indicates that the axons of md-L likely degenerated after 36 hours, and were unlikely to influence swallowing. Moreover, the projecting pattern of Tmc-GAL4 & nompC-QF>>GFP exhibited no significant changes in the brain post labellum ablation.

Furthermore, even after labellum ablation for 36 hours, flies exhibited responses to light stimulation (see Figure 3—figure supplement 1B-C, Video 5) when ReaChR was expressed in md-C. We thus reasoned that md-C but not md-L, plays a crucial role in the swallowing process.

• GRASP is known to be non-specific and prone to false positives when neurons are in close proximity but not synaptically connected. A positive GRASP signal supports but does not confirm direct synaptic connectivity between md-C/md-L axons and MN11/MN12.

In this study, we employed the nSyb-GRASP, wherein the GRASP is expressed at the presynaptic terminals by fusion with the synaptic marker nSyb. This method demonstrates an enhanced specificity compared to the original GRASP approach.

Additionally, we utilized +/ UAS-nSyb-spGFP1-10, lexAop-CD4-spGFP11 ; + / MN-LexA fruit flies as a negative control to mitigate potential false signals originating from the tool itself (Author response image 1, scale bar = 50μm). Beside the genotype Tmc-Gal4, Tub(FRT. Gal80) / UAS-nSyb-spGFP1-10, lexAop-CD4-spGFP11 ; nompC-QF, QUAS-FLP / MN-LexA fruit flies discussed in this manuscript, we also incorporated genotype Tmc-Gal4, Tub(FRT. Gal80) / lexAop-nSyb-spGFP1-10, UAS-CD4-spGFP11 ; nompC-QF, QUAS-FLP / MN-LexA fruit flies as a reverse control (Author response image 2). Unexpectedly, similar positive signals were observed, indicating that, positive signals may emerge due to close proximity between neurons even with nSyb-GRASP.

Author response image 1.

It should be noted that the existence of synaptic projections from motor neurons (MN) to md-C cannot be definitively confirmed at this juncture. At present, we can only posit the potential for synaptic connections between md-C and motor neurons. A more conclusive conclusion may be attainable with the utilization of comprehensive whole-brain connectome data in future studies.

Author response image 2.

• As seen in Figure 2—figure supplement 1, the expression pattern of Tmc-GAL4 is broader than md-C alone. Therefore, the functional connectivity the authors observe between Tmc expressing neurons and MN11 and 12 cannot be traced to md-C alone

It is true that the expression pattern of Tmc-GAL4 is broader than that of md-C alone. Our experiments, including those flies expressing TNT in Tmc+ neurons, demonstrated difficulties in emptying (Figure 2A, 2D). Notably, we encountered challenges in finding fly stocks bearing UAS>FRT-STOP-P2X2. Consequently, we opted to utilize Tmc-GAL4 to drive UAS-P2X2 instead. We believe that the results further support our hypothesis on the role of md-C in the observed behavioral change in emptying.

Overall, this work convincingly shows that swallowing and swallowing rhythms are dependent on several mechanosensory genes. Qin et al. also characterize a candidate neuron, md-C, that is likely to provide mechanosensory feedback to pumping motor neurons, but the results they present here are not sufficient to assign this function to md-C alone. This work will have a positive impact on the field by demonstrating the importance of mechanosensory feedback to swallowing rhythms and providing a potential entry point for future investigation of the identity and mechanisms of swallowing central pattern generators.

Reviewer #2 (Public Review):

In this manuscript, the authors describe the role of cibarial mechanosensory neurons in fly ingestion. They demonstrate that pumping of the cibarium is subtly disrupted in mutants for piezo, TMC, and nomp-C. Evidence is presented that these three genes are co-expressed in a set of cibarial mechanosensory neurons named md-C. Silencing of md-C neurons results in disrupted cibarial emptying, while activation promotes faster pumping and/or difficulty filling. GRASP and chemogenetic activation of the md-C neurons is used to argue that they may be directly connected to motor neurons that control cibarial emptying.

The manuscript makes several convincing and useful contributions. First, identifying the md-C neurons and demonstrating their essential role for cibarium emptying provides reagents for further studying this circuit and also demonstrates the important of mechanosensation in driving pumping rhythms in the pharynx. Second, the suggestion that these mechanosensory neurons are directly connected to motor neurons controlling pumping stands in contrast to other sensory circuits identified in fly feeding and is an interesting idea that can be more rigorously tested in the future.

At the same time, there are several shortcomings that limit the scope of the paper and the confidence in some claims. These include:

a) the MN-LexA lines used for GRASP experiments are not characterized in any other way to demonstrate specificity. These were generated for this study using Phack methods, and their expression should be shown to be specific for MN11 and MN12 in order to interpret the GRASP experiments.

Thanks for the suggestion. We have checked the expression pattern of MN-LexA, which is similar to MN-GAL4 used in previous work (Manzo et al., PNAS., 2012, PMID:22474379) . Here is the expression pattern:

Author response image 3.

b) There is also insufficient detail for the P2X2 experiment to evaluate its results. Is this an in vivo or ex vivo prep? Is ATP added to the brain, or ingested? If it is ingested, how is ATP coming into contact with md-C neuron if it is not a chemosensory neuron and therefore not exposed to the contents of the cibarium?

The P2X2 experimental preparation was done ex vivo. We immersed the fly in the imaging buffer, as described in the Methods section under Functional Imaging. Following dissection and identification of the subesophageal zone (SEZ) area under fluorescent microscopy, we introduced ATP slowly into the buffer, positioned at a distance from the brain

c) In Figure 3C, the authors claim that ablating the labellum will remove the optogenetic stimulation of the md-L neuron (mechanosensory neuron of the labellum), but this manipulation would presumably leave an intact md-L axon that would still be capable of being optogenetically activated by Chrimson.

Please refer to the corresponding answers for reviewer 1 and Figure 3—figure supplement 1.

d) Average GCaMP traces are not shown for md-C during ingestion, and therefore it is impossible to gauge the dynamics of md-C neuron activation during swallowing. Seeing activation with a similar frequency to pumping would support the suggested role for these neurons, although GCaMP6s may be too slow for these purposes.

Profiling the dynamics of md-C neuron activation during swallowing is crucial for unraveling the operational model of md-C and validating our proposed hypothesis. Unfortunately, our assay faces challenges in detecting probable 6Hz fluorescent changes with GCaMP6s.

In general, we observed an increase of fluorescent signals during swallowing, but movement of alive flies during swallowing influenced the imaging recording, so we could not depict a decent tracing for calcium imaging for md-C neurons. To enhance the robustness of our findings, patching the md-C neurons would be a more convincing approach. As illustrated in Figure 2, the somata of md-C neurons are situated in the cibarium rather than the brain. patching of the md-C neuron somata in flies during ingestion is difficult.

e) The negative result in Figure 4K that is meant to rule out taste stimulation of md-C is not useful without a positive control for pharyngeal taste neuron activation in this same preparation.

We followed methods used in the previous work (Chen et al., Cell Rep., 2019, PMID:31644916), which we believe could confirm that md-C do not respond to sugars.

In addition to the experimental limitations described above, the manuscript could be organized in a way that is easier to read (for example, not jumping back and forth in figure order).

Thanks for your suggestion and the manuscript has been reorganized.

Reviewer #3 (Public Review):

Swallowing is an essential daily activity for survival, and pharyngo-laryngeal sensory function is critical for safe swallowing. In Drosophila, it has been reported that the mechanical property of food (e.g. Viscosity) can modulate swallowing. However, how mechanical expansion of the pharynx or fluid content sense and control swallowing was elusive. Qin et al. showed that a group of pharyngeal mechanosensory neurons, as well as mechanosensory channels (nompC, Tmc, and Piezo), respond to these mechanical forces for regulation of swallowing in Drosophila melanogaster.

Strengths:

There are many reports on the effect of chemical properties of foods on feeding in fruit flies, but only limited studies reported how physical properties of food affect feeding especially pharyngeal mechanosensory neurons. First, they found that mechanosensory mutants, including nompC, Tmc, and Piezo, showed impaired swallowing, mainly the emptying process. Next, they identified cibarium multidendritic mechanosensory neurons (md-C) are responsible for controlling swallowing by regulating motor neuron (MN) 12 and 11, which control filling and emptying, respectively.

Weaknesses:

While the involvement of md-C and mechanosensory channels in controlling swallowing is convincing, it is not yet clear which stimuli activate md-C. Can it be an expansion of cibarium or food viscosity, or both? In addition, if rhythmic and coordinated contraction of muscles 11 and 12 is essential for swallowing, how can simultaneous activation of MN 11 and 12 by md-C achieve this? Finally, previous reports showed that food viscosity mainly affects the filling rather than the emptying process, which seems different from their finding.

We have confirmed that swallowing sucrose water solution activated md-C neurons, while sucrose water solution alone could not (Figure 4J-K). We hypothesized that the viscosity of the food might influence this expansion process.

While we were unable to delineate the activation dynamics of md-C neurons, our proposal posits that these neurons could be activated in a single pump cycle, sequentially stimulating MN12 and MN11. Another possibility is that the activation of md-C neurons acts as a switch, altering the oscillation pattern of the swallowing central pattern generator (CPG) from a resting state to a working state.

In the experiments with w1118 flies fed with MC (methylcellulose) water, we observed that viscosity predominantly affects the filling process rather than the emptying process, consistent with previous findings. This raises an intriguing question. Our investigation into the mutation of mechanosensitive ion channels revealed a significant impact on the emptying process. We believe this is due to the loss of mechanosensation affecting the vibration of swallowing circuits, thereby influencing both the emptying and filling processes. In contrast, viscosity appears to make it more challenging for the fly to fill the cibarium with food, primarily attributable to the inherent properties of the food itself.

Reviewer #4 (Public Review):

A combination of optogenetic behavioral experiments and functional imaging are employed to identify the role of mechanosensory neurons in food swallowing in adult Drosophila. While some of the findings are intriguing and the overall goal of mapping a sensory to motor circuit for this rhythmic movement are admirable, the data presented could be improved.

The circuit proposed (and supported by GRASP contact data) shows these multi-dendritic neurons connecting to pharyngeal motor neurons. This is pretty direct - there is no evidence that they affect the hypothetical central pattern generator - just the execution of its rhythm. The optogenetic activation and inhibition experiments are constitutive, not patterned light, and they seem to disrupt the timing of pumping, not impose a new one. A slight slowing of the rhythm is not consistent with the proposed function.

Motor neurons implicated in patterned motions can be considered effectors of Central Pattern Generators (CPGs)(Marder et al., Curr Biol., 2001, PMID: 11728329; Hurkey et al., Nature., 2023, PMID:37225999). Given our observation of the connection between md-C neurons and motor neurons, it is reasonable to speculate that md-C neurons influence CPGs. Compared to the patterned light (0.1s light on and 0.1s light off) used in our optogenetic experiments, we noted no significant changes in their responses to continuous light stimulation. We think that optogenetic methods may lead to overstimulation of md-C neurons, failing to accurately mimic the expansion of the cibarium during feeding.

Dysfunction in mechanosensitive ion channels or mechanosensory neurons not only disrupts the timing of pumping but also results in decreased intake efficiency (Figure 1E). The water-swallowing rhythm is generally stable in flies, and swallowing is a vital process that may involve redundant ion channels to ensure its stability.

The mechanosensory channel mutants nompC, piezo, and TMC have a range of defects. The role of these channels in swallowing may not be sufficiently specific to support the interpretation presented. Their other defects are not described here and their overall locomotor function is not measured. If the flies have trouble consuming sufficient food throughout their development, how healthy are they at the time of assay? The level of starvation or water deprivation can affect different properties of feeding - meal size and frequency. There is no description of how starvation state was standardized or measured in these experiments.

Defects in mechanosensory channel mutants nompC, piezo, and TMC, have been extensively investigated (Hehlert et al., Trends Neurosci., 2021, PMID:332570000). Mutations in these channels exhibit multifaceted effects, as illustrated in our RNAi experiments (see Figure 2E). Deprivation of water and food was performed in empty fly vials. It's important to note that the duration of starvation determines the fly's willingness to feed but not the pump frequency (Manzo et al., PNAS., 2012, PMID:22474379).

In most cases, female flies were deprived water and food in empty vials for 24 hours because after that most flies would be willing to drink water. The deprivation time is 12 hours for flies with nompC and Tmc mutated or flies with Kir2.1 expressed in md-C neurons, as some of these flies cannot survive 24h deprivation.

The brain is likely to move considerably during swallow, so the GCaMP signal change may be a motion artifact. Sometimes this can be calculated by comparing GCaMP signal to that of a co-expressed fluorescent protein, but there is no mention that this is done here. Therefore, the GCaMP data cannot be interpreted.

We did not co-express a fluorescent protein with GCaMP for md-C. The head of the fly was mounted onto a glass slide, and we did not observe significant signal changes before feeding.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

.>Abstract: I disagree that swallow is the first step of ingestion. The first paragraph also mentions the final checkpoint before food ingestion. Perhaps sufficient to say that swallow is a critical step of ingestion.

Indeed, it is not rigorous enough to say “first step”. This has been replaced by “early step”.

Introduction:

Line 59: "Silence" should be "Silencing"

This has been replaced.

Results:

Lines 91-92: I am not clear about what this means. 20% of nompC and 20% of wild-type flies exhibit incomplete filling? So nompC is not different from wild-type?

Sorry for the mistake. Viscous foods led to incomplete emptying (not incomplete filling), as displayed in Video 4. The swallowing behavior differs between nompC mutants and wild-type flies, as illustrated in Figure 1C, Figure 1—figure supplement 1A-C and video 1&5.

When fed with 1% MC water solution (Figure 1—figure supplement 1E-H). We found that when fed with 1% MC watere solution, Tmc or piezo mutants displayed incomplete emptying, which could constitute a long time proportion of swallowing behavior; while only 20% of nompC flies and 20% of wild-type flies sporadically exhibit incomplete emptying, which is significantly different. Though the percent of flies displaying incomplete pump is similar between nompC mutant and wild-type files, you can find it quite different in video 1 and 5.

Line 94: Should read: “while for foods with certain viscosity, the pump of Tmc or piezo mutants might"

What evidence is there for weakened muscle motion? The phenotypes of all three mutants is quite similar, so concluding that they have roles in initiation versus swallowing strength is not well supported -this would be better moved to the discussion since it is speculative.

Muscles are responsible for pumping the bolus from the mouth to the crop. In the case of Tmc or piezo mutants, as evidenced by incomplete filling for viscous foods (see Video 4), we speculate that the loss of sensory stimuli leads to inadequate muscle contraction. The phenotypes observed in Tmc and piezo mutants are similar yet distinct from those of the wild-type or nompC mutant, as shown in Video 1 and 4. The phrase "due to weakened muscle motion" has been removed for clarity.

Line 146: If md-L neurons are also labeled by this intersection, then you are not able to know whether the axons seen in the brain are from md-L or md-C neurons. Line 148: cutting the labellum is not sufficient to ablate md-L neurons. The projections will still enter the brain and can be activated with optogenetics, even after severing the processes that reside in the labellum.

Please refer to the responses for reviewer #1 (Public Review):” A major weakness of the paper…” and Figure 4.

Line 162: If the fly head alone is in saline, do you know that the sucrose enters the esophagus? The more relevant question here is whether the md-C neurons respond to mechanical force. If you could artificially inflate the cibarium with air and see the md-C neurons respond that would be a more convincing result. So far you only know that these are activated during ingestion, but have not shown that they are activated specifically by filling or emptying. In addition, you are not only imaging md-C (md-L is also labeled). This caveat should be mentioned.

We followed the methods outlined in the previous work (Chen et al., Cell Rep., 2019, PMID:31644916), which suggested that md-C neurons do not respond to sugars. While we aimed to mechanically stimulate md-C neurons, detecting signal changes during different steps of swallowing is challenging. This aspect could be further investigated in subsequent research with the application of adequate patch recording or two-photon microscopy (TPM).

Figure 3: It is not clear what the pie charts in Figure 3 A refer to. What are the three different rows, and what does blue versus red indicate?

Figure 3A illustrates three distinct states driven by CsChrimson light stimulation of md-C neurons, with the proportions of flies exhibiting each state. During light activation, flies may display difficulty in filling, incomplete filling, or a normal range of pumping. The blue and red bars represent the proportions of flies showing the corresponding state, as indicated by the black line.

Figure 4: Where are the example traces for J? The comparison in K should be average dF/F before ingestion compared with average dF/F during ingestion. Comparing the in vitro response to sucrose to the in vivo response during ingestion is not a useful comparison.

Please refer to the answers for reviewer #2 question d).

Reviewer #2 (Recommendations For The Authors):

Suggested experiments that would address some of my concerns listed in the public review include:

a) high resolution SEZ images of MN-LexA lines crossed to LexAop-GFP to demonstrate their specificity

b) more detail on the P2X2 experiment. It is hard to make suggestions beyond that without first seeing the details.

c) presenting average GCaMP traces for all calcium imaging results

d) to rule out taste stimulation of md-C (Figure 4K) I would suggest performing more extensive calcium imaging experiments with different stimuli. For example, sugar, water, and increasing concentrations of a neutral osmolyte (e.g. PEG) to suppress the water response. I think that this is more feasible than trying to get an in vitro taste prep to be convincing.

Please refer to the responses for public review of reviewer #2.

Reviewer #3 (Recommendations For The Authors):

Below I list my suggestions as well as criticisms.

(1) It would be excellent if the authors could demonstrate whether varying levels of food viscosity affect md-C activation.

That is a good point, and could be studied in future work.

(2) It is not clear whether an intersectional approach using TMC-GAL4 and nompC-QF abolishes labelling of the labellar multidendritic neurons. If this is the case, please show labellar multidendritic neurons in TMC-GAL4 only flies and flies using the intersectional approach. Along with this question, I am concerned that labellum-removed flies could be used for feeding assay.

Intersectional labelling using TMC-GAL4 and nompC-QF could not abolish labelling of the labellar multidendritic neurons (Author response image 4). Labellum-removed flies could be used for feeding assay (Figure 3—figure supplement 1B-C, video 5), but once LSO or cibarium of fly was damaged, swallowing behavior would be affected. Removing labellum should be very careful.

Author response image 4.

(3) Please provide the detailed methods for GRASP and include proper control.

Please refer to the responses for public review of reviewer #1.

(4) The authors hypothesized that md-C sequentially activates MN11 and 12. Is the time gap between applying ATP on md-C and activation of MN11 or MN12 different? Please refer to the responses for public review of reviewer #3. The time gap between applying ATP on md-C and activation of MN11 or MN12 didn’t show significant differences, and we think the reason is that the ex vivo conditions could not completely mimic in vivo process.

I found the manuscript includes many errors, which need to be corrected.

(1) The reference formatting needs to be rechecked, for example, lines 37, 42, and 43.

(2) Line 44-46: There is some misunderstanding. The role of pharyngeal mechanosensory neurons is not known compared with chemosensory neurons.

(3) Line 49: Please specify which type of quality of food. Chemical or physical?

(4) Line 80 and Figure 1B-D Authors need to put filling and emptying time data in the main figure rather than in the supplementary figure. Otherwise, please cite the relevant figures in the text(S1A-C).

(5) Line 84-85; Is "the mutant animals" indicating only nompC? Please specify it.

(6) Figure 1a: It is hard to determine the difference between the series of images. And also label filling and emptying under the time.

(7) S1E-H: It is unclear what "Time proportion of incomplete pump" means. Please define it.

(8) Please reorganize the figures to follow the order of the text, for example, figures 2 and 4

(9) Figure 4A. There is mislabelling in Figure 4A. It is supposed to be phalloidin not nc82.

(10) Figure 4K: It does not match the figure legend and main text.

(11) Figure 4D and G: Please indicate ATP application time point.

Thanks for your correction and all the points mentioned were revised.

Reviewer #4 (Recommendations For The Authors):

The figures need improvement. 1A has tiny circles showing pharynx and any differences are unclear.

The expression pattern of some of these drivers (Supplement) seems quite broad. The tmc nompC intersection image in Figure 1F is nice but the cibarium images are hard to interpret: does this one show muscle expression? What are "brain" motor neurons? Where are the labellar multi-dendritic neurons?

Tmc nompC intersection image show no expression in muscles. Somata of motor neurons 12 or 11 situated at SEZ area of brain, while somata of md-C neurons are in the cibarium. Image of md-L neurons was posted in response for reviewer #3 (Recommendations For The Authors):

Why do the assays alternate between swallowing food and swallowing water?

Thank for your suggestion, figure 1A has been zoomed-in. The Tmc nompC intersection image in Figure 2F displayed the position of md-C neurons in a ventral perspective, and muscles were not labelled. We stained muscles in cibarium by phalloidin and the image is illustrated in Figure 4A, while we didn’t find overlap between md-C neurons and muscles. Image of md-L neurons were posted as Author response image 4.

In the majority of our experiments, we employed water to test swallowing behavior, while we used methylcellulose water solution to test swallowing behavior of mechanoreceptor mutants, and sucrose solution for flies with md-C neurons expressing GCaMP since they hardly drank water when their head capsules were open.

How starved or water-deprived were the flies?

One day prior to the behavioral assays, flies were transferred to empty vials (without water or food) for 24 hours for water deprivation. Flies who could not survive 24h deprivation would be deprived for 12h.

How exactly was the pumping frequency (shown in Fig 1B) measured? There is no description in the methods at all. If the pump frequency is scored by changes in blue food intensity (arbitrary units?), this seems very subjective and maybe image angle dependent. What was camera frame rate? Can it capture this pumping speed adequately? Given the wealth of more quantitative methods for measuring food intake (eg. CAFE, flyPAD), it seems that better data could be obtained.

How was the total volume of the cibarium measured? What do the pie charts in Figure 3A represent?

The pump frequency was computed as the number of pumps divided by the time scale, following the methodology outlined in Manzo et al., 2012. Swallowing curves were plotted using the inverse of the blue food intensity in the cibarium. In this representation, ascending lines signify filling, while descending lines indicate emptying (see Figure 2D, 3B). We maintain objectivity in our approach since, during the recording of swallowing behavior, the fly was fixed, and we exclusively used data for analysis when the Region of Interest (ROI) was in the cibarium. This ensures that the intensity values accurately reflect the filling and emptying processes. Furthermore, we conducted manual frame-by-frame checks of pump frequency, and the results align with those generated by the time series analyzer V3 of ImageJ.

For the assessment of total volume of ingestion, we referred the methods of CAFE, utilizing a measurable glass capillary. We then calculated the ingestion rate (nL/s) by dividing the total volume of ingestion by the feeding time.

The changes seem small, in spite of the claim of statistical significance.

The observed stability in pump frequency within a given genotype underscores the significance of even seemingly small changes, which is statistically significant. We speculate that the stability in swallowing frequency suggests the existence of a redundant mechanism to ensure the robustness of the process. Disruption of one channel might potentially be partially compensated for by others, highlighting the vital nature of the swallowing mechanism.

How is this change in pump frequency consistent with defects in one aspect of the cycle - either ingestion (activation) or expulsion (inhibition)?

Please refer to Figure 2, 3. Both filling and emptying process were affects, while inhibition mainly influences emptying time (Figure 1—figure supplement 1).

for the authors:

Line 48: extensively

Line 62 - undiscovered.

Line 107, 463: multi

Line 124: What is "dysphagia?" This is an unusual word and should be defined.

Line 446: severe

Line 466: in the cibarium or not?

Thanks for your correction and all the places mentioned were revised.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:  

Reviewer #1 (Public review):  

Summary:  

This work examines the binding of several phosphonate compounds to a membrane-bound pyrophosphatase using several different approaches, including crystallography, electron paramagnetic resonance spectroscopy, and functional measurements of ion pumping and pyrophosphatase activity. The work attempts to synthesize these different approaches into a model of inhibition by phosphonates in which the two subunits of the functional dimer interact differently with the phosphonate.  

Strengths:  

This study integrates a variety of approaches, including structural biology, spectroscopic measurements of protein dynamics, and functional measurements. Overall, data analysis was thoughtful, with careful analysis of the substrate binding sites (for example calculation of POLDOR omit maps).  

Weaknesses:  

Unfortunately, the protein did not crystallize with the more potent phosphonate inhibitors. Instead, structures were solved with two compounds with weak inhibitory constants >200 micromolar, which limits the molecular insight into compounds that could possibly be developed into small molecule inhibitors. Likewise, the authors choose to focus the spectroscopy experiments on these weaker binders, missing an opportunity to provide insight into the interaction between more potent binders and the protein. 

We acknowledge the reviewer concern regarding the choice of weaker inhibitors. We attempted cocrystallization with all available inhibitors, including those with higher potency. However, despite numerous efforts, these potent inhibitors yielded low-resolution crystals, making them unsuitable for detailed structural analysis. Therefore, we chose to focus on the weaker binders, as we were able to obtain high-quality crystal structures for these compounds. This allowed us to perform DEER spectroscopy and monitor conformational TmPPase state ensembles in solution with the added advantage of accurately analysing the data against structural models derived from X-ray crystallography. Using these weaker inhibitors enabled a more precise interpretation of the DEER data, thus providing reliable insights into the conformational dynamics and inhibition mechanism. As suggested by the reviewer, in the revised version, we add new DEER experiments, conditions and analysis on two of the more potent inhibitors (alendronate and pamidronate) to provide additional insight into their interactions. Furthermore, we also implemented additional DEER data on the cytoplasmic side of TmPPase; at a new site we identified (with the advantage of being an endogenous cysteine residue) and spin labelled (C599R1), given the DEER data for the previous T211R1cytoplasmic site were difficult to interpret owing to the highly dynamic nature of this region. The new pair C599R1 yielded high-quality DEER traces and indicated more clearly than T211R1, distance distributions consistent with asymmetry across the sampled conditions.  Again, as suggested by the reviewer, alendronate and pamidronate DEER measurements were also recorded for this site (cytoplasmic side; C599R1) as well as the periplasmic side (525R1).

In general, the manuscript falls short of providing any major new insight into membrane-bound pyrophosphatases, which are a very well-studied system. Subtle changes in the structures and ensemble distance distributions suggest that the molecular conformations might change a little bit under different conditions, but this isn't a very surprising outcome. It's not clear whether these changes are functionally important, or just part of the normal experimental/protein ensemble variation. 

We respectfully disagree with the reviewer. The scale of motions particularly seen in solution (and now on a new reliable spin pair (C599R1) located on the cytoplasmic side) correspond to those seen in the full panoply of crystal structures of mPPases. Some proteins undergo very large conformational changes during catalysis – such as the rotary ATPase. This one does not, meaning that the precise motions we describe here are relevant and observed in solution for the first time. Conformational changes in the ensemble, whether large or small, represent essential protein motions which underlie key mPPase catalytic function. These dynamic transitions are extremely challenging to monitor, especially in so many conditions and our DEER spectroscopy data demonstrate the sensitivity and resolution necessary to monitor these subtle changes in equilibria, even if these are only a few Angstroms. For several of the conditions we investigated by DEER in solution, corresponding X-ray structures have been solved, with the derived distances agreeing well with the DEER distributions. This further validates the biological relevance of the structures, and reveals the complete conformational ensemble, intractable using other current approaches. Indeed, some conformational states were previously seen using serial time-resolved X-ray static structures and were consistent with asymmetry.

The ZLD-bound crystal structure doesn't predict the DEER distances, and the conformation of Na+ binding site sidechains in the ZLD structure doesn't predict whether sodium currents occur. This might suggest that the ZLD structure captures a conformation that does not recapitulate what is happening in solution/ a membrane. 

We agree with the reviewer that the ZLD-bound crystal structure does not predict the DEER distances. However, we believe this discrepancy arises from the steric bulkiness of ZLD inhibitor, which prevents the closure of the hydrolytic centre. Additionally, the absence of Na+ at the ion gate in the ZLD-bound structure suggests that Na+ transport does not occur, a conclusion further supported by our electrometric measurements. We agree with the reviewer; distances observed in the DEER experiments might represent a potential new conformation in solution, not captured by the static X-ray structure, thereby offering new insights into the dynamic nature of the protein under physiological conditions. This serves to emphasize the complementarity of the DEER approach to Xray crystallography and redoubles the importance of using both techniques. Finally, the static X-ray structures have not captured the asymmetric conformations that must exist to explain half-of-thesites reactivity, where DEER yields distance distributions, across all 16 cases tested here (two mutants with eight conditions each), that are consistent with asymmetry.

Reviewer #2 (Public review):  

Summary:  

Crystallographic analysis revealed the asymmetric conformation of the dimer in the inhibitor-bound state. Based on this result, which is consistent with previous time-resolved analysis, authors verified the dynamics and distance between spin introduced label by DEER spectroscopy in solution and predicted possible patterns of asymmetric dimer.  

Strengths:  

Crystal structures with inhibitor bound provide detailed coordination in the binding pocket thus useful information for the mPPase field and maybe for drug development.  

Weaknesses:  

The distance information measured by DEER is advantageous for verifying the dynamics and structure of membrane protein in solution. However, regarding T211 data, which, as the authors themselves stated, lacks measurement precision, it is unclear for readers how confident one can judge the conclusion leading from these data for the cytoplasmic side. 

We thank the reviewer for acknowledging the advantageous use of the DEER methodology for identifying dynamic states of membrane proteins in solution. In our original manuscript, we used two sites in our analysis: S525 (periplasm) and T211 (cytoplasm), in which S525R1 yielded highquality DEER data, while T211R1 yielded weak (or no) visual oscillations, leading to broad distributions for the several conditions tested. In the revised manuscript, we now added a third site at the cytoplasmic side (C599R1 located at TMH14), which yielded high-quality DEER data and comparable to S525R1. Both C599R1 and C525R1 spin pairs generated distance distributions for all 16 conditions (two mutants of eight conditions each) that were described well by the solution-state ensemble adopting a predominantly asymmetric conformation.  

Furthermore, we have tailored our interpretation of the T211R1 DEER data, and refrain from using the data to draw conclusions about the TmPPase conformational ensemble in the presence of different inhibitors. However, we still opted to include the T211R1 data in the SI because they confirm an important structural feature of mPPase in solution conditions; the intrinsically dynamic behaviour of the loop5-6 where T211 is located. This observation in solution is also consistent with our previous (Kellosalo et al., Science, 2012; Li et al., Nat. Commun, 2016; Vidilaseris et al., Sci. Adv., 2019; Strauss et al., EMBO Rep., 2024) and current X-ray crystallography data. To reiterate, we excluded T211R1 from any analysis relating to mPPase asymmetry and our conclusions were entirely based on the S525R1 and new C599R1 DEER data, which allowed us to monitor both sides on the membrane.  

The distance information for the luminal site, which the authors claim is more accurate, does not indicate either the possibility or the basis for why it is the ensemble of two components and not simply a structure with a shorter distance than the crystal structure.  

We thank the reviewer for pointing out this possibility and alternative interpretation of our DEER data. We now provide further analysis to show that our DEER data from both membrane sides reporters are highly consistent with (although they cannot completely exclude) asymmetry and rephrase to be inclusive of other possibilities. Importantly, this additional possibility does not affect the current interpretation of the data in our manuscript. Furthermore, we have removed Fig. 6 from the manuscript, and we now include a direct comparison of the in silico predicted distribution coming from the asymmetric hybrid structure with the 8 conditions tested, for both mutants (i.e. S525R1 and C599R1).

Reviewer #3 (Public review):  

Summary:  

Membrane-bound pyrophosphatases (mPPases) are homodimeric proteins that hydrolyze pyrophosphate and pump H+/Na+ across membranes. They are attractive drug targets against protist pathogens. Non-hydrolysable PPi analogue bisphosphonates such as risedronate (RSD) and pamidronate (PMD) serve as primary drugs currently used. Bisphosphonates have a P-C-P bond, with its central carbon can accommodate up to two substituents, allowing a large compound variability. Here the authors solved two TmPPase structures in complex with the bisphosphonates etidronate (ETD) and zoledronate (ZLD) and monitored their conformational ensemble using DEER spectroscopy in solution. These results reveal the inhibition mechanism of these compounds, which is crucial for developing future small molecule inhibitors.  

Strengths:  

The authors show that seven different bisphosphonates can inhibit TmPPase with IC50 values in the micromolar range. Branched aliphatic and aromatic modifications showed weaker inhibition.  

High-resolution structures for TmPPase with ETD (3.2 Å) and ZLD (3.3 Å) are determined. These structures reveal the binding mode and shed light on the inhibition mechanism. The nature of modification on the bisphosphonate alters the conformation of the binding pocket.  

The conformational heterogeneity is further investigated using DEER spectroscopy under several conditions.  

Weaknesses:  

The authors observed asymmetry in the TmPPase-ELD structure above the hydrolytic center. The structural asymmetry arises due to differences in the orientation of ETD within each monomer at the active site. As a result, loop5-6 of the two monomers is oriented differently, resulting in the observed asymmetry. The authors attempt to further establish this asymmetry using DEER spectroscopy experiments. However, the (over)interpretation of these data leads to more confusion than any further understanding. DEER data suggest that the asymmetry observed in the TmPPase-ELD structure in this region might be funneled from the broad conformational space under the crystallization conditions. 

We respectfully disagree with the reviewer. The asymmetry was previously established using serial time crystallography (Strauss et al., EMBO Rep, 2024) and biochemical assays (e.g. Malinen et al., Prot. Sci., 2022; Artukka et al., Biochem J, 2018; Luoto et al., PNAS, 2013) and partially seen in one static structure (Vidilaseris et al., Sci Adv 2019). DEER data here also show that the previously proposed asymmetry is also present (and this presence of asymmetry is consistent across all DEER data) within the TmPPase conformational ensemble in solution conditions. Although we cannot rule out the possibility that the TmPPase monomers adopt a metastable intermediate state, in such a case we would expect the distance changes reported by DEER to be symmetric across both membrane sides. However, we observe a symmetry breaking between the cytoplasmic and periplasmic TmPPase sites. Indeed, DEER data yield distance distributions similar to that of the hybrid asymmetric structure under all: apo, +Ca, +Ca/ETD, +ETD, +ZLD, +IDP, +PAM, +ALE conditions.

DEER data for position T211R1 at the enzyme entrance reveal a highly flexible conformation of loop56 (and do not provide any direct evidence for asymmetry, Figure EV8).

Please see relevant response above. We acknowledge that T211 is indeed situated on a highly dynamic loop, which is important for gating and our DEER data confirm the high flexibility of this protein region. Given we have not observed dipolar oscillations, leading to broad distributions, we have stated in the original manuscript that we will not establish the presence of any asymmetry in solution on the basis of T211, rather relying on the S525R1 and the new C599R1 sites, for which we have acquired high-quality DEER data, as was also pointed out and has been commented on by all reviewers. We have provided data at the C599R1 position (same cytoplasmic side as 211 for which we have now limited our analysis to a minimum) which further provides evidence for asymmetry, including two new conditions.

Similarly, data for position S521R1 near the exit channel do not directly support the proposed asymmetry for ETD.  

The reviewer appears to suggest that we hold the S525R1 DEER data as direct proof of asymmetry; this is combative on the grounds that to directly prove asymmetry would require time-resolved DEER measurements, far beyond the scope of this work. Rather, we have applied DEER measurements to explore whether asymmetry (observed previously via time-resolved X-ray crystallography) is also present (or indeed a possibility) in solution. All our S525R1 and C599R1 DEER data (recorded for eight conditions) are consistent with asymmetry (see also detailed response above).

Despite the high quality of the data, they reveal a very similar distance distribution. The reported changes in distances are very small (+/- 0.3 nm), which can be accommodated by a change of spin label rotamer distribution alone. Further, these spin labels are located on a flexible loop, thereby making it difficult to directly relate any distance changes to the global conformation

We thank the reviewer for recognising the high quality of our DEER data for the S525R1 site which we now complement with a new pair on the cytoplasmic facing membrane side (C599R1) with DEER data of comparable quality as for S525R1, where visual oscillations in the raw traces for both spin pairs, as in our case, reportedly lead to highly accurate and reliable distributions, able to separate (in fortuitous cases) helical movements of only a few Angstroms (Peter et al., Nature Comms 13:4396, 2022; Klose et al., Biophys J 120:4842-4858, 2021). The ability of DEER/PELDOR offering near Angstrom resolution was also previously demonstrated by the acquisition and solution of highresolution multi-subunit spin-labelled membrane protein structures (Pliotas at al., PNAS, 2012; Pliotas et al., Nat Struct Mol Biol, 2015; Pliotas, Methods Enzymol, 2017) as well as its ability in detecting small (and of similar to mPPase magnitude) conformational changes in different integral membrane protein systems (Kapsalis et al., Nature Comms, 2019; Kubatova et al., PNAS, 2023; Schmidt et al., JACS, 2024; Lane et al., Structure, 2024; Hett et al., JACS, 2021; Zhao et al., Nature, 2024), occurring under different conditions and/or stimuli in solution and/or lipid environment. The changes here are not below the detection sensitivity of DEER (e.g. ~ 7 Angstroms between the two modal distance extremes (+Ca vs +IDP for S525R1), and with all other conditions showing intermediate changes.  

We agree with the reviewer that these changes are relatively small, but they are expected for membrane ion pumps. Indeed, none of the mPPase structures show helical movements of greater than half a turn, and that only in helices 6 and 12. There appear to be larger-scale loop closing motions of the 5-6 loop that includes T211, due to the presence of E217 which binds to one of the Mg²⁺ ions that coordinate the leaving group phosphate. This is, inter alia, the reason that this loop is so flexible: it cannot order before substrate is bound.  

The reviewer suggests that the subtle distance shifts detected arise only from changes of label rotamer distribution. However, the concerted nature of the modal distance shifts with respect to multiple different conditions at a single labelling site strongly suggests that preferential rotamer orientations are not the cause. Indeed, for so many spin labels to undergo an arbitrary shift that the modal distance of the entire distribution changes – and in the absence of any conformational change – appears improbable. Here we have the resolution to detect such subtle differences by DEER, given there are unambiguous shifts in our time domain data (i.e. the position of the minimum of the first dipolar oscillation) (Fig 4) and these are reflected in the modal distances in the distributions. We also refrain from performing any quantitative analysis and use qualitative trends in modal distance shifts only; all which support our proposed model of a symmetry breaking across the membrane face. To further belabour this point, we do not quantify the DEER data (for instance through parametric fitting) to extract populations of different conformational states and we appreciate that to do so would be highly prone to error; however we do (and can, we feel without over-interpretation) assert that the modal distances shift.  

The interpretations listed below are not supported by the data presented:  

(1) 'In the presence of Ca2+, the distance distribution shifts towards shorter distances, suggesting that the two monomers come closer at the periplasmic side, and consistent with the predicted distances derived from the TmPPase:Ca structure.'

Problem: This is a far-stretched interpretation of a tiny change, which is not reliable for the reasons described in the paragraph above. 

While the authors overall agree with the reviewer assessment that ±0.3 nm is a small (not a minor) change, there are literature examples quantifying (or using for quantification) distribution peaks separated by similar Δr. (Kubatova et al., PNAS, 2023; Schmidt et al., JACS, 2024; Hett et al., JACS, 2021; Zhao et al., Nature, 2024). However, the time-domain data clearly indicate the position of the first minimum of the dipolar oscillation shifts to shorter dipolar evolution time. The sensitivity of the time-domain data to subtle changes in dipolar coupling frequency is significantly improved compared to the distance distributions.

Importantly, we have fitted Gaussians to the experimental distance distributions of 525R1 output by the Comparative Deer Analyzer 2.0 and observed a change in the distribution width in presence of Ca2+, implying the rotameric freedom of the spin label is restricted. However, the CW-EPR for 525R1 indicate that the rotational correlation time of the spin label is highly consistent between conditions (the spectra are almost identical); this cannot be explained simply by rotameric preference of the spin label (as asserted by the reviewer 3), as there is no (further) immobilisation observed from the CW-EPR of apo-state (Figure EV9) to that in presence of Ca2+. Furthermore, in the absence of conformational changes, it is reasonable to assume (and demonstrable from the CW-EPR data) that the rotamer cloud should not significantly change between conditions. However, Gaussian fits of the two extreme cases yielding the longest (i.e., in presence of IDP) and shortest (in presence of ZLD) modal distances for the 525R1 DEER data indicated significant (i.e., above the noise floor after Tikhonov validation) probability density for the IDP condition at 50 Å (P(r) = 0.18). This occurs at four standard deviations above the mean of the Guassian fit to the +ZLD condition, which by random chance should occur with <0.007% probability.  

As in previous response, the method can detect changes of such magnitude which are not small, but physiologically relevant and expected for integral membrane proteins, such as mPPases. Indeed, even in equal (or more) complex systems such as heptameric mechanosensitive channel proteins DEER provided sub-Angstrom accuracy, when a spin labelled high resolution XRC structure was solved (Pliotas et al., PNAS, 2012; Pliotas et al., Nat Struct Mol Biol, 2015). Despite this being an ideal case where DEER accuracy was experimentally validated another high-resolution structural method on modified membrane protein and is not very common it demonstrates the power of the method, especially when strong oscillations are present in the raw DEER data (as here for mPPase S525R1, and C599R1), even when multiple distances are present, Angstrom resolution is achievable in such challenging protein classes.

(2) 'Based on the DEER data on the IDP-bound TmPPase, we observed significant deviations between the experimental and the in silico distances derived from the TmPPase:IDP X-ray structure for both cytoplasmic- (T211R1) and periplasmic-end (S525R1) sites (Figure 4D and Figure EV8D). This deviation could be explained by the dimer adopting an asymmetric conformation under the physiological conditions used for DEER, with one monomer in a closed state and the other in an open state.'  

Problem: The authors are trying to establish asymmetry using the DEER data. Unfortunately, no significant difference is observed (between simulation and experiment) for position 525 as the authors claim (Figure 4D bottom panel). The observed difference for position 112 must be accounted for by the flexibility and the data provide no direct evidence for any asymmetry.  

Reviewer 3 is incorrect in suggesting that we are trying to prove asymmetry through the DEER data. That is a well-known fact in the literature (e.g. Vidilaseris et al, Sci Adv 2019) where we show (1) that the exit channel inhibitor ATC (i.e. close to S525R1) binds better in solution to the TmPPase:PPi complex than the TmPPase:PPi₂ complex, and (2) that ATC binds in an asymmetric fashion to the TmPPase:IDP₂ complex with just one ATC dimer on one of the exit channels. We merely use the DEER data to support this well-established fact.  

However, because we agree that the DEER data in presence of IDP does not provide direct proof for asymmetry; particularly for the cytoplasmic facing mutant T211R1, we have refrained from interpreting T211R1 data beyond being a highly dynamic loop region (as evidenced by the broad distributions). As pointed out by the reviewer, the differences in distance distributions between conditions observed for T211R1 likely arise from conformational heterogeneity in solution. Furthermore, we now report DEER data on another new site (C599R1), which is also on the cytoplasmic side and yields high quality DEER data comparable to the S525R1 data (commended for their quality by both the reviewers). The C599R1 measurements show that in all conditions tested, highly similar distributions are observed, inconsistent with the in silico predicted distance distributions from the symmetric X-ray structures, but consistent with an asymmetric hybrid structure (i.e. open-closed) in solution. Importantly, the difference between the fully open (6.8 nm modal distance) and fully closed (4.8 nm modal distance) states of the C599R1 dimer is larger than for the S525R1 dimer pair. Thus, delineating the asymmetric hybrid conformation from the symmetric conformations is more robust.

(3) 'Our new structures, together with DEER distance measurements that monitor the conformational ensemble equilibrium of TmPPase in solution, provide further solid experimental evidence of asymmetry in gating and transitional changes upon substrate/inhibitor binding.'  

Problem: See above. The DEER data do not support any asymmetry. 

We feel that the reviewer comments here are somewhat unfounded. All the DEER data (for 525R1 periplasmic and C599R1 cytoplasmic sites are described, most parsimoniously, using an asymmetric hybrid structure. In particular, the new C599R1 distance distributions are poorly described by the symmetric X-ray crystal structures, with a conserved modal distance of approx. 5.8 nm throughout the tested conditions that aligns nicely with the in silico predictions from the asymmetric hybrid structure. Additionally, all S525R1 and C599R1 data well exceed the relevant criteria of the recent white paper (Schiemann et al., 2021, JACS) from the EPR community to be considered reliably interpretable (strong visual oscillations in the raw traces; signal-to-noise ratio .r.t modulation depth of > 20 in all cases; replicates have been performed and added into the maintext or supplementary; near quantitative labelling efficiency (evidenced by lack of free spin label signal in the CW-EPR spectra); analysed using the CDA (now Figure EV10) to avoid confirmation bias).

While the DEER data do not prove asymmetry, we do not claim proof of asymmetry in the above sentence. We concede to rephrase the offending sentence above as: “Our new structures, together with DEER distance measurements that monitor the conformational ensemble of TmPPase in solution, do not exclude asymmetry in gating and transitional changes upon substrate/inhibitor binding and are consistent with our proposed model.” We feel that this reframed conjecture of asymmetry is well founded; indeed, comparing all the 16 experimentally derived DEER distance distributions for the 525R1 and 599R1 sites with in-silico modelling performed on the hybridised asymmetric structure (i.e., comprised of one monomer bound to Ca2+ and another bound to IDP) yields overlap coefficients (Islam and Roux, JPC B, 2015) of >0.85. This implies the envelope of the modelled distance distribution is quantitatively inside the envelope of the experimental distance distributions. Thus, the DEER data support asymmetry (previously observed by time-resolved XRC) in solution, and while we appreciate that ideally one would measure time-resolved DEER to directly correlate kinetics of conformational changes within the ensemble to the catalytic cycle of mPPase, (and this is something we aim to do in the future), it is far beyond the scope of this study.

Indeed, half-of-the-sites reactivity has been demonstrated in at least the following papers

(Vidilaseris et al, Sci Acv. ,2019, Strauss et al, EMBO Rep. 2024, Malinen et al Prot Sci, 2022, Artukka et al Biochem J, 2018; Luoto et al, PNAS, 2013). Half-of-the sites activity requires asymmetry in the mechanism, and therefore asymmetric motions in the active site (viz 211) and exit channel (viz 525). As mentioned above, we have demonstrated this for other inhibitors (Vidilaseris et al 2019) and as part of a time-resolved experiment (Strauss et al 2024). In fact, given the wealth of evidence showing that the symmetrical crystal structures sample a non- or less-productive conformation of the protein, it would be quixotic to propose the DEER experiments - in solution - do not generate asymmetric conformations. It certainly doesn’t obey Occam’s razor of choosing the simplest possible explanation that covers the data.

(4) Based on these observations, and the DEER data for +IDP, which is consistent with an asymmetric conformation of TmPPase being present in solution, we propose five distinct models of TmPPase (Figure 7).  

Problem: Again, the DEER data do not support any asymmetry and the authors may revisit the proposed models. 

We have redressed the proposed models and limited them to four asymmetric models to clearly illustrate the apo/+Ca/+Ca:ETD-state (model 1) and highlight the distinct binding patterns of various inhibitors (ETD, ZLD and IDP; model 2-4), which result in a variety of closed/open-open states. In this version, we clarify that the proposed models are not solely based on the DEER data but all DEER data recorded for multiple conditions, inhibitors and for two opposite membrane side facing reporters are highly consistent, and are grounded in both current and previously solved structures, with the DEER data providing additional consistency with these models.

(5) 'In model 2 (Figure 7), one active site is semi-closed, while the other remains open. This is supported by the distance distributions for S525R1 and T211R1 for +Ca/ETD informed by DEER, which agrees with the in silico distance predictions generated by the asymmetric TmPPase:ETD X-ray structure'  

Problem: Neither convincing nor supported by the data 

We respectfully disagree with the reviewer. However, owing to the conformational heterogeneity of T211R1, we now exclude T211R1 data from quantitative interpretation of changes to the conformational ensemble. Instead, we include new DEER data from site C599R1, which provides high-quality and convincing data that is consistent with asymmetry at the cytoplasmic face, and inconsistent with in silico distance distributions derived from symmetric X-ray crystal structures. Furthermore, the S525R1 distance distributions for the +ETD (corresponding to +Ca/ETD) and +ZLD conditions were directly compared with both the apo-state distance distribution (corresponding to a fully open, symmetric conformation) and the in silico predicted distributions of the asymmetric hybrid structure (corresponding to an open-closed conformation). Overlap coefficients were calculated (given in the main text) that indicated the +ETD (corresponding to +Ca/ETD) and +ZLD S525R1 distributions were more consistent with the apo-state distance distribution. This suggests that while on the cytosolic face of the membrane, an open-closed conformation is favoured, on the periplasmic face, a symmetric open-open conformation is favoured.

Recommendations for the authors:  

Reviewer #1 (Recommendations for the authors):   

(1) The DEER experiments were performed with the two crystallized inhibitors, ETD and ZLD, along with previously characterized IDP. It would increase the impact of a tighter-binding phosphonate was examined since the inhibitory mechanism of these molecules is of greater interest. 

We acknowledge the reviewer concern regarding the choice of weaker inhibitors. We chose to focus on the weaker binders, as we were able to obtain high-quality crystal structures for these compounds. This allowed us to perform DEER spectroscopy with the added advantage of accurately analysing the data against structural models derived from X-ray crystallography. In the revised version, we also include results from alendronate and pamidronate, two of the tighter inhibitors, which show similar and consistent results to the others.

(2) I'm not able to find the concentrations of ETD and ZLD used for the DEER experiments. This information should be added to the Methods section on sample prep for EPR. 

The information is already mentioned in the Method section on sample preparation for EPR spectroscopy (page 24), where we indicated that the protein aliquots were incubated with a final concentration of 2 mM inhibitors or 10 mM CaCl2 (30 min, RT). However, we recognise that this may not have been sufficiently clear. To clarify, we now explicitly state that the concentration of ETD and ZLD (amongst other inhibitors) used for the DEER experiments is 2 mM.  

(3) There should be additional detail about the electrometry replicates. Does "triplicate" mean three measurements on the same sensor, three different sensors, and different protein preparations? At a minimum, data should be collected from three different sensors to ensure that the negative results (lack of current) for ETD and ZLD are not due to a failed sensor prep. In addition, Data from the other replicates should be shown in a supplementary figure, either the traces, or in a summary figure. Are the traces shown collected on the same sensor? They could be, in principle, since the inhibitor is washed away after each perfusion. 

Yes, by 'triplicate', we mean three measurements taken on the same sensor. All traces shown were collected from a single sensor. Thank you for your advice; we now show here additional data from other sensors that display the same pattern. As for the possibility of a failed sensor preparation, this is unlikely since we always ensure the sensor quality with the substrate (PPi) as a positive control after each measurement.

Author response image 1.

(4) I'm confused by the NEM modification assay, and I don't think there is enough information in this manuscript for a reader to figure out what is happening. Why is the protein active if an inhibitor is present? I understand that there is a conformational change in the presence of the inhibitor that buries a cysteine, but the inhibitor itself should diminish function, correct? Is the inhibitor removed before testing the function? In addition, it would be clearer if the cysteines that are modified are indicated in the main text. I don't understand what is being shown in Figure Ev2. Shouldn't the accessible cysteines in the apo form be shown? Finally, the sentence "IDP has been reported to prevent the NEM modification..." does not make sense to me. Should the word "by" be removed from this sentence? 

We apologize for the confusion. Yes, the inhibitors were removed before testing the protein function. In Figure EV2, the accessible cysteines are shown for both the apo and IDP-bound states. As seen, the accessible cysteines in the IDP-bound states are fewer than those in the apo state, meaning fewer cysteines are available for modification. Consequently, more activity is retained when IDP binds due to the reduction in accessible cysteines. We have addressed this in the manuscript (see the method section on the NEM modification assay).

(5) Why does the model in Figure 7 show the small molecules bound to only one subunit, when they are crystallized in both subunits? 

We propose that the small molecules bound to the two subunits in the crystal structure is likely a result of substrate inhibition, given the excess inhibitor used during crystallisation (e.g. Artukka, et al., Biochemical Journal, 2018; Vidilaseris, et al., Science Advances, 2022). Our PELDOR data indicate that in solution, the small molecules bound to TmPPase are in an intermediate state between both subunits being closed and both being open, most likely with at least one subunit in an open state. This is also consistent with previous kinetic studies (Anashkin, V. A., et al., International Journal of Molecular Sciences, 22, 2021), which showed that the binding constant of IDP to the second subunit is around 120 times higher than that of the first subunit.

(6) The authors argue that the two ETDs bound in the two protomers adopt distinct conformations. Can this be further supported, for example, by swapping the position of the two ETDs between the two protomers and calculating a difference map (there should be corresponding negative/positive density if the modelling of the two different conformations is robust)? 

As per the reviewer suggestion, we swapped the positions of the two ETDs between the protomers and calculated the difference electron density map. This analysis, presented in Figure EV3, reveals corresponding negative and positive electron density peaks, indicating that the ETDs indeed adopt distinct conformations in each protomer, supporting the accuracy of our modeling.

(7) Are the changes in loop conformation possibly due to crystal packing differences for the two protomers? 

We examined the crystal packing of the two protomers and found no interactions at the loop regions (red coloured in Author response image 2 below) that could be attributed to crystal packing differences. Therefore, we rule out this possibility.

Author response image 2.

(8) Typos:  

Legend for Figure EV2 cystine - cysteine  

Page 14, last sentence of the first paragraph: further - further  

Figure 6 legend: there is no reference to panel B.  

Thanks for pointing out the typos, now they are fixed.

Reviewer #2 (Recommendations for the authors):  

(1) T211 is located on the same loop where ligand/inhibitor-coordinating side chains (E217, D218) are located. It has not been tested whether spin labeling here would affect inhibitor binding. 

We test all the mutant(s) activity before spin labelling, but not the activity of the spin-labelled mutants. MTSSL spin labels are typically not structurally perturbing. In particular, the T211R1 site that the reviewer is referring to is now not included in our interpretation of conformational changes occurring during mPPase’s functional cycle.

(2) Why should the spin label be introduced to T211, which is recognized as a flexible region in the crystal structure? Authors should search for suitable residues except for T211 and other residues in this loop to evaluate the cytoplasmic distance. 

We acknowledge the reviewer’s concern regarding the flexibility of the T211 region for spin labelling. Given the challenges associated with TmPPase, including reduced protein expression, loss of function, or inaccessibility upon spin labelling at certain sites, we have explored alternative residues. After extensive testing, we identified C599 as a suitable site for spin labelling resulting in high-quality DEER data. The results from spin labelling at C599 have been incorporated into the revised manuscript.

(3) On the other hand, DEER data for S525 is solid, as the authors stated. This residue is located on the luminal side of the enzyme. However, the description of the luminal side structure and the comparison of symmetric/asymmetric dimer in this par are missing in the paper. 

We thank the viewer for their positive assessment of the S525R1 DEER data. The data for 525 and now also for 599 spin pairs are indeed solid given the strong visual oscillation we observed particularly in such a challenging system.   

We presented the periplasmic sites in the crystal structure dimer (Figure 4A), highlighting both the symmetrical region and the asymmetric model in Figure 4. In the revised version, we include additional details about this region and our rationale for labeling at position S525.

(4) The conclusion models (Figure 7) are misleading. In the crystal structure, the 5-6Loop distance between each monomer should be close given the location of the dimer interface, and the actual distance between T211 in the structure (for example, in 5lzq) is about 10A. Nevertheless, the model depicts this distance longer than S525 (40.7A in 5LZQ), which would give a false impression. 

We would like to apologize for the misleading model. We have now corrected the models to ensure they are consistent with their respective regions in the crystal structures.

(5) P8 last paragraph  

It is hard to imagine that in a crystal lattice, the straight inhibitor always binds to monomer A, and the neighboring monomer is always attached to a slightly tilted inhibitor, which causes asymmetry. For example, wouldn't it mean that it would first bind to one of them, which would then affect the neighboring monomer via 5-6 Loop, which would then affect its binding pose? So in this case, the inhibitor did not ARAISE asymmetry, and this is where it is misleading for readers. 

We apologize for the confusion. What we intended to convey is that the first inhibitor binds to one protomer, which then affects the conformation of the neighbouring monomer, ultimately influencing its binding pose. This is required for half-of-the-sites reactivity, which is well-established in this system. This is reflected in our crystal structure, where we observed asymmetry in the loop 5-6 region and the ETD orientation between the two protomers. We have addressed this in the manuscript accordingly.

(6) P11 L4 EV10 instead of EV8? 

Thanks for pointing out. We have corrected it accordingly.

(7) P11 L5 It is difficult to determine whether the peak is broad or sharp. Should be evaluated quantitatively by showing the half-value width of the peak. This may also be helpful to judge whether the peak is a mixture of two components or a single one. 

We have taken this analysis out and rephrased the offending sentence. We have also added the FWHM values as the Reviewer suggested, and corresponding standard deviations for the distance distributions (under approximation as Gaussian distribution).   

(8) Throughout the paper, the topology of the enzyme may be difficult to follow for readers who are not experts in this field. Please indicate the membrane plane's location or a figure's viewpoint in the caption. 

We acknowledge the importance of making our figures accessible to all readers. In the revised manuscript, we have enhanced the clarity of our figures by explicitly indicating the membrane plane’s location and specifying the viewpoint in each figure caption. For example, we have added annotations such as “Top view of the superposition of chain A (cyan) and chain B (wheat), showing the relative movements (black arrow) of helices. The membrane plane is indicated by dashed lines.”

(9) Figure 2B Check the color of the helix.  

IDP and ETD are almost the same color, so it is difficult to see the superposition. It would be easier to understand the reading by, for example, using a lighter or transparent color set only for IDPs.  

We acknowledge the reviewer concern regarding the colour similarity between the IDP and ETD in Figure 2B, which hinders clear differentiation. To enhance visual distinction, we have adjusted the colour scheme by changing the TmPPase:IDP structure colour to light blue. This modification improves the clarity of the superposition, making the structural differences more discernible.

(10) Figure 2C Check the coordination state (dotted line), there appears to be coordination between E217Cg and Mg. Also, water that is located near N492 appears to be a bit distant from Mg, why does this act as a ligand? Stereo view or view from different angles, and distance information would help the reader understand the bonding state in more detail.  

Yes, we confirm that Mg²⁺ is coordinated by the oxygen atoms from both the side chain and main chain of residue E217. The water molecule near N492 is not directly coordinated with Mg²⁺ but interacts with the O5 atom of one of the phosphate groups in ETD. To enhance clarity, we have updated Figure 2C (and other related figures) to include stereo views.  

(11) Figure 5A: in the Bottom view (lower left), the symmetric dimer does not look symmetric. Better to view from a 2-fold axis exactly.  

We have taken this figure out entirely and instead add a direct comparison to the in silico predicted distribution from the asymmetric hybrid structure to all 16 experimental DEER distributions. We have added the symmetric and asymmetric structures to Fig. 4A and view the symmetric structure along the 2-fold axis, as suggested.   

(12) Figure 5B: Indicate which data is plotted in the caption.  

As mentioned above, we have taken this figure out, as we felt quantifying two overlapping populations from a single Gaussian was over-interpretation of the data, and at the suggestion of reviewer 3, we have tailored our interpretation here.  

(13) Figure EV8:  

Because the authors discuss a lot about their conclusive model based on this data, Figure EV8 should be treated as a main figure, not a supplement. However, this reviewer has serious concerns about the measurement in this figure. Because DEER for T211 is too noisy, I don't see the point in discussing this in detail. For example, in the Ca/ETD data, there is a peak near 50A, but it would be difficult for TM5 to move away from this distance unless the protein unfolds. I do not find it meaningful to discuss using measurement results in which such an impossible distance is detected as a peak.  

A: Show top view as in Figure 5  

D: 2nd row dotted line. Regarding the in silico model that is used as a reference to compare the distance information, the distance of 40-50 A for T211 in the Ca-bound form is hard to imagine. PDB 4av6 model shows that T211 is disordered and not visible, but given the position of the TM5 helix, it does not appear to be that different from the IDR binding structure (5LZQ, 10A between two T211). The structures of in silico models are not shown in the figure, as it is only mentioned as modeled in Rossetafold. Please indicate their structures, especially focused on the relative orientation of T211 and S525 in the dimer, which would allow readers to determine the distances.  

We acknowledge the reviewer’s concerns regarding Figure EV8 and the DEER data for T211R1. Upon re-evaluation, we recognize that the non-oscillating nature of the DEER data for T211R1 leads to broad distributions, indicating increased conformational dynamics, which is expected for a highly dynamic loop. Consequently, we have limited the discussion and interpretation of T211R1 in the revised manuscript and focused more on C599R1.

Reviewer #3 (Recommendations for the authors):  

A careful interpretation of the data in view of these limitations and without directly linking to asymmetry could solve the problem of the over-interpretation of the DEER data.  

We respectfully disagree with the reviewer. Please see our detailed response above.  

Additional comments:  

(1) Did the authors use a Cys-less construct for spin labeling and DEER experiments?  

We utilized a nearly Cys-less construct in which all native cysteines were mutated to serine, except for Cys183, which was retained due to its buried location and functional importance. We then introduced single cysteine mutations for spin labelling. For C599, Ser599 was reverted to cysteine.

(2) The time data for position T211R1 is too short for most cases (Figure EV8D) for a reliable distance determination. No confidence interval is given for the '+Ca' sample distance distributions.  

We recorded longer time traces for two of the conditions to better assign the background. We did not use the 211R1 data to reach any conclusions regarding asymmetry, which were based on the 525R1 and the 599R1 data. We now simply include T211R1 data to indicate the high mobility observed at loop5-6. We have added the confidence interval for the +Ca condition.  

(3) It is recommended to mention the 2+1 artefact obvious at the end of the DEER data. 

In the methods section, we have mentioned that the “2+1” artefact present at the end of the S525R1, and T211R1 DEER data likely arises from using a 65 MHz offset, rather than an 80 MHz offset (as for the C599R1 data), which avoids significant overlap of the pump and detection pulses. We also mention in the methods section that owing to the intense “2+1” artefact, the decision was made to truncate the artefact away, to minimise the impact on data treatment. As for motivation to use the lower offset of 65 MHz, we did so to maximise the achievable signal-to-noise ratio (SNR), as particularly for the T211R1 data, the detected echo was quite weak. This was further exacerbated by the poor transverse relaxation time observed at that site.  

(4) Please check the number of significant digits for all the reported values. 

We have addressed the number of significant digits as requested.

(5) Please report the mean distances from DEER experiments with the standard deviation or FWHM.

We have addressed this in the revised manuscript, we report modal distances rather than the mean distances and provide the FWHM and standard deviation.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1:

Weaknesses:

(1) Only Experiment 1 of Rademaker et al (2019) is reanalyzed. The previous study included another experiment (Expt 2) using different types of distractors which did result in distractor-related costs to neural and behavioral measures of working memory. The Rademaker et al (2019) study uses these two results to conclude that neural WM representations are protected from distraction when distraction does not impact behavior, but conditions that do impact behavior also impact neural WM representations. Considering this previous result is critical for relating the present manuscript's results to the previous findings, it seems necessary to address Experiment 2's data in the present work

We thank the reviewer for the proposal to analyze Experiment 2 where subjects completed the same type of visual working memory task, but instead had either a flashing orientation distractor or a naturalistic (gazebo or face) distractor present during two-thirds of the trials. As the reviewer points out, unlike Experiment 1, these two conditions in Experiment 2 had a behavioral impact on recall accuracy, when compared to the blank delay. We have now run the temporal cross-decoding analysis, temporally-stable neural subspace analysis, and condition cross-decoding analysis in Experiment 2. The results from the stable subspace analysis are present in Figure 3, while the results from the temporal cross-decoding analysis and condition cross-decoding analysis are present in the Supplementary Data.

First, we are unable to draw strong conclusions from the temporal cross-decoding analysis, as the decoding accuracies across time in Experiment 2 are much lower compared to Experiment 1. In some ROIs of the naturalistic distractor condition we see that some diagonal elements are not part of the above-chance decoding cluster, making it difficult to draw any conclusions regarding dynamic clusters. We do see some dynamic coding in the naturalistic condition in V3 where the off-diagonals do not show above-chance decoding. Since the temporal cross-decoding provides low accuracies, we do not examine the dynamics of neural subspaces across time.

We do, however, run the stable subspace analysis on the flashing orientation distractor condition. Just like in Experiment 1, we examine temporally stable target and distractor subspaces. When projecting the distractor onto the working memory target subspace, we see a higher overlap between the two as compared to Experiment 1. A similar pattern is seen also when projecting the target onto the distractor subspace. We still see an above-chance principal angle between the target and distractor; however, this angle is qualitatively smaller compared to Experiment 1. This shows that the degree of separation between the two neural subspaces is impacted by behavioral performance during recall.

(2) Primary evidence for 'dynamic coding', especially in the early visual cortex, appears to be related to the transition between encoding/maintenance and maintenance/recall, but the delay period representations seem overall stable, consistent with previous findings

We agree with the reviewer that we primarily see dynamic coding between the encoding/maintenance and at the end of the maintenance periods, implying the WM representations are stable in most ROIs. The only place where we argue that we might see more dynamic coding during the delay itself is in V1 during the noise distractor trials in Experiment 1.

(3) Dynamicism index used in Figure 1f quantifies the proportion of off-diagonal cells with significant differences in decoding performance from the diagonal cell. It's unclear why the proportion of time points is the best metric, rather than something like a change in decoding accuracy. This is addressed in the subsequent analysis considering coding subspaces, but the utility of the Figure 1f analysis remains weakly justified.

We agree that other metrics can also provide a summary of dynamics; here, the dynamicism index just acts as a summary visualizing the dynamic elements. It offers an intuitive way to visualize peaks and troughs of the dynamic code across the extent of the trial.

(4) There is no report of how much total variance is explained by the two PCs defining the subspaces of interest in each condition, and timepoint. It could be the case that the first two principal components in one condition (e.g., sensory distractor) explain less variance than the first two principal components of another condition.

We thank the reviewer for this comment. We have now included the percent variance explained for the two PCs in both the temporally-stable target and distractor subspace and the dynamic subspace analysis. The percent-explained is comparable across analyses; the first PC ranges from 43-50% and the second ranges from 28-37%. The PCs within each analysis (dynamic no-distractor, orientation and noise distractor; temporally-stable target and distractor) are even closer in range (Figure 2c and 3d).

(5) Converting a continuous decoding metric (angular error) to "% decoding accuracy" serves to obfuscate the units of the actual results. Decoding precision (e.g., sd of decoding error histogram) would be more interpretable and better related to both the previous study and behavioral measures of WM performance.

We thank the reviewer for the comments. FCA is a linear function of the angular error that uses the following equation:

We think that the FCA does not obfuscate the results, but instead provides an intuitive scale where 0% accuracy corresponds to a 180° error, 50% to a 90° error and so on. This also makes it easy to reverse-calculate the absolute error if need be. Our lab has previously used this method in other neuroimaging papers with continuous variables (Barbieri et al. 2023, Weber et al. 2024).

We do, however, agree that “% decoding accuracy” does not provide an accurate reflection of the metric used. We have thus now changed “% decoding accuracy” to “Accuracy (% FCA)”.

(6) This report does not make use of behavioral performance data in the Rademaker et al (2019) dataset.

We have now analyzed Experiment 2 which, as previously mentioned by the reviewer and unlike Experiment 1, showed a decrease in recall accuracy during the two distractor conditions. We address the results from Experiment 2 in a previous response (please see Weaknesses 1).

We do not, however, relate single subject behavioral performance to neural measurements, as we do not think there is enough power to do so with a small number of subjects in both Experiment 1 and 2. 

(7) Given there were observed differences between individual retinotopic ROIs in the temporal cross-decoding analyses shown in Figure 1, the lack of data presented for the subspace analyses for the corresponding individual ROIs is a weakness

We have now included an additional supplementary figure that shows individual plots of each ROI for the temporally stable subspace analysis for both Experiment 1 and Experiment 2 (Supplementary Figure 5). 

Reviewer #1 (Recommendations For The Authors):

(1) Is there any relationship between stable/dynamic coding properties and aspects of behavioral performance? This seems like a major missed opportunity to better understand the behavioral relevance or importance of the proposed dynamic and orthogonal coding schemes. For example, is it the case that participants who have more orthogonal coding subspaces between orientation distractor and remembered orientation show less of a behavioral consequence to distracting orientations? Less induced bias? I know these differences weren't significant at the group level in the original study, but maybe individual variability in the metrics of this study can explain differences in performance between participants in the reported dataset

As mentioned in the previous response, we do not run individual correlations between dynamic or orthogonal coding metrics and behavioral performance, because of the small number of subjects in both experiments. We believe that for a brain-behavior correlation between average behavioral error of subjects and an average brain measure, we would need a larger sample size.  

(2) The voxel selection procedure differs from the original study. The authors should add additional detail about the number of voxels included in their analyses, and how this number of voxels compares to that used in the original study.

We have now added a figure summarizing the number of voxels selected across participants. We do select fewer voxels compared to Rademaker et al. 2019 (see their Supplementary Tables 9 and 10 and our Supplementary Figure 8). For example we have ~500 voxels on average in V1 in Experiment 1, while the original study had ~1000. As mentioned in the methods, we aimed to select voxels that reliably responded to both the perception localizer conditions and the working memory trials.

(3) Lines 428-436 specify details about how data is rescaled prior to decoding. The procedure seems to estimate rescaling factors according to some aspect of the training data, and then apply this rescaling to the training and testing data. Is there a possibility of leakage here? That is - do aspects of the training data impact aspects of the testing data, and could a decoder pick up on such leakage to change decoding? It seems this is performed for each training/testing timepoint pair, and so the temporal unfolding of results may depend on this analysis choice.

Thank you for the suggestion. To prevent data leakage, the mean and standard deviation are computed exclusively from the training set. These scaling parameters are then applied to the test set, ensuring that no information from the test set influences the training process. This transformation simply adjusts the test set to the same scale as the training data, without exposing the model to unseen test data during training.

(4) Figure 1d, V1: it looks like the 'dynamics' are a bit non-symmetric - perhaps the authors could comment on this detail of the results? Why would we expect there would be a dynamic cluster on one side of the diagonal, but not the other? Given that this region, condition is the primary evidence for a dynamic code that's not related to the beginning/end of delay (see other comments), figuring this out is of particular importance.

We thank the reviewer for this question. We think that this is just due to small numerical differences in the upper and lower triangles of the matrix, rather than a neuroscientifically interesting effect. However, this is only a speculative observation.

(5) I think it's important to address the issue I raised in "weaknesses" about variance explained by the top N principal components in each condition. What are we supposed to learn from data projected into subspaces fit to different conditions if the subspaces themselves are differently useful?

Thank you, this has now been addressed in a previous comment (please see Weakness 4). 

Reviewer #2:

Weaknesses:

(1) An alternative interpretation of the temporal dynamic pattern is that working memory representations become less reliable over time. As shown by the authors in Figure 1c and Figure 4a, the on-diagonal decoding accuracy generally decreased over time. This implies that the signal-to-noise ratio was decreasing over time. Classifiers trained with data of relatively higher SNR and lower SNR may rely on different features, leading to poor generalization performance. This issue should be addressed in the paper.

We thank the reviewer for raising this issue and we have now run three simulations that aim to address whether a changing SNR across time might create dynamic clusters. 

In the first simulation we created a dataset of 200 voxels that have a sine or cosine response function to orientations between 1° to 180°, the same orientations as the remembered target. A circular shift is applied to each voxel to vary preferred (or maximal) responses of each simulated voxel. We then assess the decoding performance under different SNR conditions during training and testing. For each of the seven iterations we selected 108 responses (out of 180) to train on and 108 to test on. To increase variability the selected trials differed in each iteration. Random white noise was applied to the data and thus the SNR was independently scaled according to the specified levels for train and test data. We then use the same pSVR decoder as in the temporal cross decoding analysis to train and test. 

The second and third simulations more directly address whether increased noise levels  would induce the decoder to rely on different features of the no-distractor and noise distractor data. We use empirical data from the primary visual cortex (V1; where dynamic coding was seen in the noise distractor trials) under the no-distractor and noise distractor conditions for the second and third simulations, respectively. Data from time points 5.6–8.8 seconds after stimulus onset are averaged across five TRs. As in the first simulation, SNR is systematically manipulated by adding white noise. Additionally, to see whether the initial decrease in SNR and subsequent increase would result in dynamic coding clusters, we initially increased and subsequently decreased the amplitude of added noise. The same pSVR decoder was used to train and test on the data with different levels of added noise.

We see an absence of dynamic elements in the SNR cross-decoding matrices, as the decoding accuracy primarily depends on the training data rather than test data. This results in some off-diagonal values in the decoding matrix that are higher, rather than smaller, than corresponding on-diagonal elements.

We have now added a Methods section explaining the simulations in more detail and Supplementary Figure 9 showing the SNR cross-decoding matrices. 

(2) The paper tests against a strong version of stable coding, where neural spaces representing WM contents must remain identical over time. In this version, any changes in the neural space will be evidence of dynamic coding. As the paper acknowledges, there is already ample evidence arguing against this possibility. However, the evidence provided here (dynamic coding cluster, angle between coding spaces) is not as strong as what prior studies have shown for meaningful transformations in neural coding. For instance, the principal angle between coding spaces over time was smaller than 8 degrees, and around 7 degrees between sensory distractors and WM contents. This suggests that the coding space for WM was largely overlapping across time and with that for sensory distractors. Therefore, the major conclusion that working memory contents are dynamically coded is not well-supported by the presented results.

We thank the reviewer for this comment. The principal angles we calculate are above-baseline, meaning that we subtract the within-subspace principal angles from the between-subspace principal angles and take the average. Thus a 7 degree difference does not imply that there are only 7 degrees separating e.g. the sensory distractor from the target; it just indicates that the separation is 7 degrees above chance. 

(3) Relatedly, the main conclusions, such as "VWM code in several visual regions did not generalize well between different time points" and "VWM and feature-matching sensory distractors are encoded in separable coding spaces" are somewhat subjective given that cross-condition generalization analyses consistently showed above chance-level performance. These results could be interpreted as evidence of stable coding. The authors should use more objective descriptions, such as 'temporal generalization decoding showed reduced decoding accuracy in off-diagonals compared to on-diagonals.

Thank you, we agree that our previous claims might have been too strong. We have now toned down our statements in the Abstract and use “did not fully generalize” and “VWM and feature-matching sensory distractors are encoded in coding spaces that do not fully overlap.”

Reviewer #2 (Recommendations For The Authors):

Weakness 1 can potentially be addressed with data simulations that fix the signal pattern, vary the noise pattern, and perform the same temporal generalization analysis to test whether changes in SNR can lead to seemingly dynamic coding formats.

Thank you for the great suggestion. We have now run the suggested simulations. Please see above (response to Weakness 1).

There are mismatches in the statistical symbols shown in Figure 4 and Supplementary Table 2. It seems that there was a swap between the symbols for the noise between-condition and noise within-condition.

Thank you, this has now been fixed.

Author response:

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

Public Reviews: 

Reviewer #1 (Public Review):

This manuscript presents a pipeline incorporating a deep generative model and peptide property predictors for the de novo design of peptide sequences with dual antimicrobial/antiviral functions. The authors synthesized and experimentally validated three peptides designed by the pipeline, demonstrating antimicrobial and antiviral activities, with one leading peptide exhibiting antimicrobial efficacy in animal models. However, the manuscript as it stands, has several major limitations on the computational side.

Thanks for your comments. 

Major issues:

(1) The choice of GAN as the generative model. There are multiple deep generative frameworks (e.g., language models, VAEs, and diffusion models), and GANs are known for their training difficulty and mode collapse. Could the authors elaborate on the specific rationale behind choosing GANs for this task?

We thank the reviewer for his/her concern on GAN models. We agree that there are some limitations of GAN itself such as its training difficulty, but we cannot deny its potential in generating biological sequences, especially in AMP generation. GAN and VAE are the two most commonly used generative models in the field of AMP design (Curr Opin Struct Biol 2023, 83:102733). AMPGAN (J Chem Inf Model, 2021, 61, 2198-2207.), Multi-CGAN (J Chem Inf Model 2024, 64, 1, 316–326), PepGAN (ACS Omega, 2020, 5, 22847-22851) and others have verified its application ability on peptide design. Moreover, PandoraGAN (Sn Comput Sci 2023, 4, 607) is one of the few works on AVP generation which is also based on GAN architecture. GAN updates the generator weights on the backpropagation from the discriminator directly rather than manually defined complicated loss function, which alleviates the reliance on input data. Our current results demonstrated that the trained GAN generator could produce novel sequences that featured high antimicrobial activity, both validated in silico and in vitro. 

(2) The pipeline is supposed to generate peptides showing dual properties. Why were antiviral peptides not used to train the GAN? Would adding antiviral peptides into the training lead to a higher chance of getting antiviral generations?

A major mechanism of antimicrobial peptides is to disrupt cell membranes. Thus, some antimicrobial peptides are reported with broad-spectrum antibacterial and antiviral activities, since the virus shares a membrane structure with bacteria, especially the enveloped viruses. In APD3 database, 244 of 3940 AMPs are labeled with antiviral activities. In constrast, most reported antiviral peptides inhibit the viruses by binding to specific targets (proteins and nucleic acids) related to viral proliferation so that they may not have antibacterial effects. Therefore, we trained the GAN with the AMP dataset. We chose this AMP dataset mainly for AMPredictor (with detailed logMIC label against E.coli) and then used the same dataset to train a GAN for simplification. 

In the revised manuscript, we also tested adding available antiviral peptides from AVPdb to train the GAN model. The number of AVPs is 1,788 after removing overlaps with used AMP dataset. The GAN architecture and hyperparameters remain the same. After generating a batch of sequences with this trained generator, we scored them by AMPredictor and filtered them with five AVP classifiers. As expected, the predicted MIC values shifted to higher performance with 17 sequences < 5 μM and 39 sequences < 10 uM, and previous numbers are 26 and 42 in the manuscript. Among 39 sequences < 10 μM, 13 passed all five AVP classifiers and 17 passed four (33.3% and 43.6%, respectively). Previous ratios are 40.5% and 35.7% (17 and 15 out of 42). Two generators perform roughly the same for generating AVPs (76.9% vs. 76.1%) as evaluated by our rules (4 or more positives), but the generator trained solely with AMPs provided more AVPs with higher possibility (5 positives).

We also experimentally tested dozens of generated peptides from two versions of generators (v1 for training solely on AMPs, v2 for training with AVPs, Figure 2 in revised manuscript). The ‘antiviral’ feature of a peptide was checked when significant inhibition was observed in immunofluorescence assays against HSV-1 at the concentration of 10 µM. Six and seven antiviral peptides were found out of 12 tested peptides from generators v1 and v2, respectively. Therefore, the success rates for two versions of generators are about 60% (including three reported peptides in the original manuscript) and show no significant difference.

(3) For the antimicrobial peptide predictor, where were the contact maps of peptides sourced from?

The contact maps of AMPs were predicted from ESM, which were obtained at the same time when obtaining the ESM embeddings (Methods section, Page 24, Line 538: Pretrained language model esm1b_t33_650M_UR50S was used to provide the embeddings and the contact maps.)

(4) Morgan fingerprint can be used to generate amino acid features. Would it be better to concatenate ESM features with amino acid-level fingerprints and use them as node features of GNN?

We thank the reviewer for this suggestion. We test using ESM and fingerprint (FP) features on graph nodes and the result is shown in Author response table 1. AMPredictor (ESM on nodes, FP after GNN) still performed slightly better than concatenating FP on node features on four regression metrics. 

Author response table 1.

Results of AMPredictor with fingerprint on nodes 

(5) Although the number of labeled antiviral peptides may be limited, the input features (ESM embeddings) should be predictive enough when coupled with shallow neural networks. Have the authors tried simple GNNs on antiviral prediction and compared the prediction performance to those of existing tools?

We thank the reviewer for his/her suggestion on AVP predictions. We haven’t tried it. An important reason is that we focused on developing regressors instead of binary classifiers. Currently available AVP data with numerical labels did not support training a reliable regressor, for their limited amount as well as heterogenous virus target and experimental assay. Therefore, we decided to use reported AVP classifiers as an additional filter following AMPredictor. Since only using one classifier may lead to bias, we chose five AVP classifiers as ensemble votes. 

(6) Instead of using global alignment to get match scores, the authors should use local alignment.

We calculated the match scores by global alignment methods referred to AMPGAN v2 (J Chem Inf Model 2021, 61, 2198−2207), CLaSS (Nat Biomed Eng 2021 5, 613–623), and AMPTrans-lstm (Comput Struct Biotechnol J 2022, 21, 463-471), to check the similarity between the generated sequences and any sequences in the training set. In addition, we also used local alignment to check the novelty of peptides (regarding the next question). 

(7) How novel are the validated peptides? The authors should run a sequence alignment to get the most similar known AMP for each validated peptide, and analyze whether they are similar.

We have listed the most similar AMP segments to our generated peptides from the training set and DRAMP database (28,233 sequences after filtering out those containing irregular characters). BLAST parameters were set as CLaSS (Nat Biomed Eng 2021 5, 613–623) for short peptides. The lowest Evalue of P001 aligned with the training set is 1.2, and no hits were found for P001 with DRAMP. Two E-values of P002 are 1.4 and 0.46. P076 had no hits in the training set and got a high E-value of 7.0 with DRAMP. Detailed alignments are shown below. This result indicates that our three validated AMPs are novel. 

Since we generated more sequences using two versions of generator for validation, we also checked the BLAST E-value of these validated peptides. The results are listed in Table S3. All sequences obtained E-values > 0.1 and some of them had no hits when aligned with the training set or the DRAMP database. 

Author response image 1.

Alignments of three validated peptides.

(8) Only three peptides were synthesized and experimentally validated. This is too few and unacceptable in this field currently. The standard is to synthesize and characterize several dozens of peptides at the very least to have a robust study.

We thank the reviewer for the suggestion and promoted our models to generate >10 times more peptides in the revised manuscript. We have synthesized and tested more peptides in vitro and added these results in the revised manuscript (Figure 2). From two versions of generators (trained with or without AVPs), we selected 24 peptides in total for antibacterial and antiviral validations. All 24 peptides showed antibacterial activity towards at least bacterial strain, and 13 peptides were screened out through the quick antiviral test. This result indicates the capability of our design method for bifunctional AMPs with a notable success rate (60%).

Reviewer #2 (Public Review):

Summary:

This study marks a noteworthy advance in the targeted design of AMPs, leveraging a pioneering deeplearning framework to generate potent bifunctional peptides with specificity against both bacteria and viruses. The introduction of a GAN for generation and a GCN-based AMPredictor for MIC predictions is methodologically robust and a major stride in computational biology. Experimental validation in vitro and in animal models, notably with the highly potent P076 against a multidrug-resistant bacterium and P002's broad-spectrum viral inhibition, underpins the strength of their evidence. The findings are significant, showcasing not just promising therapeutic candidates, but also demonstrating a replicable means to rapidly develop new antimicrobials against the threat of drug-resistant pathogens.

Strengths:

The de novo AMP design framework combines a generative adversarial network (GAN) with an AMP predictor (AMPredictor), which is a novel approach in the field. The integration of deep generative models and graph-encoding activity regressors for discovering bifunctional AMPs is cutting-edge and addresses the need for new antimicrobial agents against drug-resistant pathogens. The in vitro and in vivo experimental validations of the AMPs provide strong evidence to support the computational predictions. The successful inhibition of a spectrum of pathogens in vitro and in animal models gives credibility to the claims. The discovery of effective peptides, such as P076, which demonstrates potent bactericidal activity against multidrug-resistant A. baumannii with low cytotoxicity, is noteworthy. This could have far-reaching implications for addressing antibiotic resistance. The demonstrated activity of the peptides against both bacterial and viral pathogens suggests that the discovered AMPs have a wide therapeutic potential and could be effective against a range of pathogens.

We thank the reviewer for the comments.

Reviewer #3 (Public Review):

Summary:

Dong et al. described a deep learning-based framework of antimicrobial (AMP) generator and regressor to design and rank de novo antimicrobial peptides (AMPs). For generated AMPs, they predicted their minimum inhibitory concentration (MIC) using a model that combines the Morgan fingerprint, contact map, and ESM language model. For their selected AMPs based on predicted MIC, they also use a combination of antiviral peptide (AVP) prediction models to select AMPs with potential antiviral activity. They experimentally validated 3 candidates for antimicrobial activity against S. aureus, A. baumannii, E. coli, and P. aeruginosa, and their toxicity on mouse blood and three human cell lines. The authors select their most promising AMP (P076) for in vivo experiments in A. baumannii-infected mice. They finally test the antiviral activity of their 3 AMPs against viruses.

Strengths:

-The development of de novo antimicrobial peptides (AMPs) with the novelty of being bifunctional (antimicrobial and antiviral activity).

-Novel, combined approach to AMP activity prediction from their amino acid sequence.

Weaknesses:

(1) I missed justification on why training AMPs without information of their antiviral activity would generate AMPs that could also have antiviral activity with such high frequency (32 out of 104).

Thanks for your inquiry. A major mechanism of antimicrobial peptides is to disrupt cell membranes. Thus, some antimicrobial peptides are reported with broad-spectrum antibacterial and antiviral activities, since the virus shares a membrane structure with bacteria, especially the enveloped viruses. In APD3 database, 244 of 3940 AMPs are labeled with antiviral activities. However, several reported antiviral peptides inhibit the viruses by binding to specific targets (proteins and nucleic acids) related to viral proliferation so that they may not have antibacterial effects. Therefore, we trained the GAN with the AMP dataset. We chose this AMP dataset mainly for AMPredictor (with detailed logMIC label against E.coli) and then used the same dataset to train a GAN for simplification. In addition, it’s not 32 antiviral candidates out of 104 but 32 out of 42 peptides with predicted MIC < 10 µM because we did the filtering process stepwise. 

In revision, we also tested adding available antiviral peptides from AVPdb to train the GAN model (generator v2). The number of AVPs is 1,788 after removing overlaps with used AMP dataset. The GAN architecture and hyperparameters remain the same. We used generator v2 to obtain a batch of sequences and screened out bifunctional candidates following the same procedure. 30 out of 39 peptides with predicted MIC < 10 µM passed four or five AVP predictors. Therefore, two generators perform roughly the same for generating AVP candidates (76.9% vs. 76.1%). 

(2) The justification for AMP predictor advantages over previous tools lacks rationale, comparison with previous tools (e.g., with the very successful AMP prediction approach described by Ma et al. 10.1038/s41587-022-01226-0), and proper referencing.

Thanks for your suggestion. Ma et al. proposed ensemble binary classification models to mine AMPs from metagenomes successfully. However, we concentrated on the development of regression models. As a regressor, AMPredictor predicts the specific logMIC value of the input sequences instead of giving a yes/no answer. Since the training settings and evaluation metrics are different for the classification and regression tasks, we could not compare AMPredictor with Ma et al. directly. Instead, we compared the performance of AMPredictor with some regression baseline models (Figure S2a) and our model outperformed them. 

(3) Experimental validation of three de novo AMPs is a very low number compared to recent similar studies.

Thanks for pointing out this shortcoming. We have synthesized and tested more peptides in vitro and added these results in the revised manuscript (Figure 2). From two versions of generators (trained with or without AVPs), we selected 24 peptides in total for antibacterial and antiviral validations. All 24 peptides showed antibacterial activity towards at least bacterial strain, and 13 peptides were screened out through the quick antiviral test. This result indicates the capability of our design method for bifunctional AMPs with a notable success rate (60%).

(4) I have concerns regarding the in vivo experiments including i) the short period of reported survival compared to recent studies (0.1038/s41587-022-01226-0, 10.1016/j.chom.2023.07.001, 0.1038/s41551-022-00991-2) and ii) although in Figure 2 f and g statistics have been provided, log scale y-axis would provide a better comparative representation of different conditions.

Thank you for your suggestions. 

i) In current study, we monitored the survival of mice with peritoneal bacterial infection for 48 h.

Because abdominal bacterial infection can induce severe sepsis and cause mouse death within 40 h (Sci Adv 2019, 5(7), eaax1946), the 48 h is sufficient to evaluate the therapeutic efficacy of antimicrobial peptides (Nat Biotechnol 2019, 37(10), 1186-1197).

ii) In Figure 2f and 2g (3f and 3g in the revised manuscript), the y-axis has already been in log-scale and tick labels are marked in scientific notation.

(5) I had difficulty reading the story because of the use of acronyms without referring to their full name for the first time, and incomplete annotation in figures and captions.

Thank you for pointing this. We have checked the manuscript carefully and modified the figure captions during revision. 

Reviewer #2 (Recommendations For The Authors):

(1) To validate the generalizability of the model, it would be prudent to include data on AMPs targeting a broader range of bacteria and viruses. This could help ensure that the peptides designed are not narrowly focused on E. coli but are effective against a more extensive set of pathogens. 

Thanks for your suggestions. We just incorporated AMPs with E. coli activity labels since it is the most common strain among available AMP databases. As for a regressive model (AMPredictor), the fitting object should be defined concisely, which means limited targeting bacteria. Some other articles also focused on E. coli labels as well (Nat Commun 2023, 14, 7197; mSystems 2023, 8, e0034523). 

We used the same processed dataset to train the GAN generator for simplification. Most reported AMPs have the potential to target various microbes. We have counted the antimicrobial labels of these peptides in our dataset, shown in Figure S1b. In addition to E. coli, some of the peptides target Grampositive S. aureus, fungus C. albicans, and other bacterial species as well. Our experimental validation also reveals the wide spectrum of designed peptides inhibiting Gram-negative, Gram-positive, drugresistant bacteria, and enveloped viruses. With the expansion of well-curated AMP databases, we expect to update the model with larger scale datasets in the near future. 

(2) Conduct sensitivity analyses to understand how minor changes in the peptide sequences impact the model’s predictions. This will reduce the chances of overlooking potential AMP candidates due to the model’s inability to capture subtle changes.

Thank you for this valuable suggestion. We kept similar known peptide sequences in the training sets regarding that a single mutation may have an impact on their antimicrobial performances. We took P001 as an example to perform the sensitivity analysis by site saturation mutagenesis in silico. Author response image 2 represents the change of antimicrobial activity scores as predicted by AMPredictor. Since the predicted MIC of P001 is 0.949 µM (experimentally measured value is 0.80 µM), most single mutations lead to higher scores (i.e., worse performance), especially Asp (D) and Glu (E) residues with negative charges. The largest change value of single amino acid replacement is 25.51 (W6D). Although this value may not reflect the actual changes, it is enough to be distinguished when screening and ranking candidate sequences.

Author response image 2.

Site saturated mutagenesis of P001. Color shows the change of predicted MIC against E. coli as predicted by AMPredictor (lower score is better).

(3) Given the relatively short length of the peptides, typically ranging from 10 to 20 residues, the authors might consider employing a fully-connected graph in the peptide’s graphical representation. This approach could potentially simplify the model without sacrificing the descriptive power due to the limited size of the peptides.

Thanks for your suggestions. We tested fully-connected graph edge encodings and the results on the test set were shown in Author response table 2 below. We found that AMPredictor with peptide contact map still performed better on Pearson correlation coefficient and CI, while using fully-connected graphs reached a slightly improved RMSE and MSE. Nonetheless, using fully-connected graph demands about 10time memory and more computational costs when processing more complicated message-passing. Therefore, the involvement of structural information is still a preferred choice.

Author response table 2.

Results of AMPredictor with different graph edge encodings

(4) Upon reviewing Table S1, it is apparent that the application of ESM embeddings alone achieves commendable prediction accuracy. It would be intriguing to investigate whether the adoption of the more recent ESM models-specifically the second-generation ESM2 t36_3B, t48_15B, and t33_650Mcould enhance model performance beyond that observed using the esm1b_t33_650M_UR50S model described in the manuscript. 

Thanks for your suggestions. Here, we included various ESM2 models’ outputs as our node features and presented the results in Author response table 3. Notably, the dimensions of esm2_t36_3B and esm2_t48_15B are 2560 and 5120, respectively, while both esm2_t33_650M and esm1b_t33_650M are 1280 dimensions. 

Interestingly, we found that larger models don’t lead to improved performance. ESM-1b version still holds the best metrics in RMSE, MSE, and Pearson correlation coefficient. This indicates that the choice of pretrained model versions depended on specific downstream tasks. 

Author response table 3.

Results of AMPredictor with different ESM versions

(5) It may be pertinent to reevaluate the use of the MM-PBSA approach within the scope of this study. Typically, MM-PBSA is utilized to estimate the free energy differences between the bound and unbound states of solvated molecules. The application of MM-PBSA is to calculate binding energies between proteins and membranes is unconventional and infrequently documented in the literature. Therefore, it is recommended that the authors consider omitting this portion of the manuscript, or provide a robust justification for its inclusion and application in this context.

Thanks for your comments on MM/PBSA methods. There have been several literatures using this approach to calculate peptide-membrane binding free energy (Langmuir 2016, 32, 1782-1790; J Cell Biochem 2018, 119, 9205-9216; J Chem Inf Model 2019, 59, 3262-3276; Molecular Therapy Oncolytics 2019, 16, 7-19; Microbiology Spectrum 2023, 11, e0320622; J Chem Inf Model 2023, 63, 5823-5833) and we referred to their settings, such as the dielectric constant. All of these works built similar all-atom systems including cationic antimicrobial peptides and membrane bilayers, and utilized MM/PBSA method to describe the absorption process of the peptide from an unbound initial state. The order of magnitude of our calculation results is consistent with other reported works. Additionally, computational results may provide supporting evidence and we discussed that this quantitative energy calculation should be considered along with other observed metrics. 

Reviewer #3 (Recommendations For The Authors):

The weaknesses I mentioned in the Public Review may be addressed by improving the writing and presentation and corrections to the text and figures.

Thanks for your suggestion. We have carefully checked and improved the presentation of text and figures in the revised manuscript.

Author Response

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

REVIEWER 1

The claim that olivooid-type feeding was most likely a prerequisite transitional form to jet-propelled swimming needs much more support or needs to be tailored to olivooids. This suggests that such behavior is absent (or must be convergent) before olivooids, which is at odds with the increasing quantities of pelagic life (whose modes of swimming are admittedly unconstrained) documented from Cambrian and Neoproterozoic deposits. Even among just medusozoans, ancestral state reconstruction suggests that they would have been swimming during the Neoproterozoic (Kayal et al., 2018; BMC Evolutionary Biology) with no knowledge of the mechanics due to absent preservation.

Thanks for your suggestions. Yes, we agree with you that the ancestral swimming medusae may appear before the early Cambrian, even at the Neoproterozoic deposits. However, discussions on the affinities of Ediacaran cnidarians are severely limited because of the lack of information concerning their soft anatomy. So, it is hard to detect the mechanics due to absent preservation. Olivooids found from the basal Cambrian Kuanchuanpu Formation can be reasonably considered as cnidarians based on their radial symmetry, external features, and especially the internal anatomies (Bengtson and Yue 1997; Dong et al. 2013; 2016; Han et al. 2013; 2016; Liu et al. 2014; Wang et al. 2017; 2020; 2022). The valid simulation experiment here was based on the soft tissue preserved in olivooids.

While the lack of ambient flow made these simulations computationally easier, these organisms likely did not live in stagnant waters even within the benthic boundary layer. The absence of ambient unidirectional laminar current or oscillating current (such as would be found naturally) biases the results.

Many thanks for your suggestion concerning the lack of ambient flow in the simulations. We revised the section “Perspectives for future work and improvements” (lines 381-392 in our revised version of manuscript). Conducting the simulations without ambient flow can reduce the computational cost and, of course, making the simulation easier, while adding ambient flow can lead to poorer convergency and more technical issues. Meanwhile, we strongly agreed that these (benthic) organisms did not live in stagnant waters, as discussed in Liu et al. 2022. However, reducing computational complexity is not the main reason that the ambient flow was not incorporated in the simulations. As we discussed in section “Perspectives for future work and improvements”, our work focuses on the theoretical effect caused by the dynamics (based on fossil observation and hypothesis) of polyp on ambient environment (i.e., how fast the organism inhales water from ambient environment) rather than effect caused by ambient flow on organism (e.g., drag forces), which was what previous palaeontological CFD simulations mainly focused based on fossil morphology and hydrodynamics. To this end, we mainly concern the flow velocity above or near peridermal aperture (and vorticity computed in this paper) generated only by polyp’s dynamics itself without the interference of ambient flow (as many CFD simulations for modern jellyfish, i.e., McHenry & Jed 2003; Gemmell et al. 2013; Sahin et al. 2009. All those simulations were conducted under hydrostatic conditions). Adding ambient flow to our simulations “biases” the flow velocity profiles we expect to obtain in this case.

Nevertheless, we do agree that the ambient unidirectional laminar current or oscillating current plays an important role in feeding and respiration behavior of Quadrapyrgites. Further investigations need to be realized by designing a set of new insightful simulations and is beyond the scope of this work. We conducted CFD simulations incorporated with a randomly generated surface that imitated uneven seabed, where unidirectional laminar current and oscillating current (or vortex) were formed and exerted on Quadrapyrgites located in different places on the surface (Zhang et al. 2022). We assumed that combining the method we used in Zhang et al. 2022 and the velocity profiles collected in this work to conduct new simulations may be a promising way to further investigate the effect of the ambient current on organisms’ active feeding behavior.

There is no explanation for how this work could be a breakthrough in simulation gregarious feeding as is stated in the manuscript.

Thanks for your suggestion. We revised the section “Perspectives for future work and improvements” (lines 396-404 in our revised version of manuscript).

Conducting simulations of gregarious active feeding behavior generally need to model multi (or clustered) organisms, which is beyond the present computational capability. However, exploiting the simulation result and thus building a simplified model can be possible to realize that, as we may apply an inlet or outlet boundary condition to the peridermal aperture of Quadrapyrgites with corresponding exhale or inhale flow velocity profiles collected in this work. By doing this we can obtain a simplified version of an active feeding Quadrapyrgites model without using computational expensive moving mesh feature. Such a model can be used solely or in cluster to investigate gregarious feeding behavior incorporated with ambient current. Those above are explicit explanations for how this work could be a “breakthrough” in simulation gregarious feeding. However, we modified the corresponding description in section “Perspectives for future work and improvements” to make it more appropriate.

Throughout the manuscript there are portions that are difficult to digest due to grammar, which I suspect is due to being written in a second language. This is particularly problematic when the reader is attempting to understand if the authors are stating an idea is well documented versus throwing out hypotheses/interpretations.

Thanks. Our manuscript was checked and corrected by a native speaker of English again.

Line-by-line:

L023: "Although fossil evidence suggests..."

L026: "demonstrated" instead of "proven"

We corrected them accordingly.

L030: "The hydrostatic simulations show that the..." Maybe I'm confused by the wording, but shouldn't this be the case since it's a set part of the model?

As is demonstrated in our manuscript, all the simulations were conducted under “hydrostatic” environment. We originally intend to use the description “hydrostatic” here to emphasize the simulation condition we set in our work. However, it can literally lead to misunderstanding that some of the simulations we conducted are “hydrostatic” while the others are not. To this end, deleting the word “hydrostatic” here (line 30) may be appropriate to eliminate confusion.

L058: "lacking soft tissue" Haootia preservation suggests it is soft tissue (Liu et al., 2014), unless the preceding sentence is not including Haootia, in which case this section is confusingly worded

Thank you. We deleted the sentence “However, their affinities are not without controversy as the lacking soft tissue.”

L085: change "proxy"

Yes, we changed to “Considering their polypoid shape and cubomedusa-type anatomy, the hatched olivooids appear to a type of periderm-bearing polyp-shaped medusa (Wang et al. 2020) (lines 86-88).”

L092: "assist in feeding" has this been stated before? Citation needed, else this interpretation should primarily be in the discussion

Yes, you are right. We cited the reference at the end of the mentioned sentence (lines 91-94).

L095: Remove "It is suggested that"

Thanks for your suggestions. We corrected it.

L100: "Probably the..." here to the end belongs in the discussion and not introduction.

Thanks for your suggestions. We corrected the sentences.

L108: "an abapical"

Thanks for your suggestions. We revised it in line 107.

L112: "for some distance" be specific or remove

Yes, we deleted “for some distance” in line 111.

L133: I can't find a corresponding article to Zhang et al., 2022. Is this the correct reference?

The article Zhang et al. 2022 (entitled “Effect of boundary layer on simulation of microbenthic fossils in coastal and shallow seas”.) was in press at the time when we first submitted this manuscript. We complemented the corresponding term in References with the doi (10.13745/j.esf.sf.2023.5.32), which may help readers to locate this article easier.

L138: You can't be positive that your simulations "provide a good reproduction of the movement." You have attempted to reconstruct said movement, but the language here is overly firm - as is "pave a new way"

Thanks for your suggestions. We corrected the corresponding description (lines 138-140) to make it more rigorous.

L149: "No significant change" implies statistics were computed that are not presented here.

The statistics were computed by using built-in function of Excel and presented in Table supplement 2 (deposited in figshare, https://doi.org/10.6084/m9.figshare.23282627.v2) rather than in manuscript. To be specific, the error computations are followed by the formula of relative error, which is defined by:

where u_z denotes the velocity profile collected on each cut point z with the current mesh parameters, u_z^* denotes the velocity profile collected on each cut point z with the next finer mesh parameters, i denotes each time step (from 0.01 to 4.0). In this case, the total average error was computed by averaging the sum of each 〖error〗_i on corresponding time step. The results are red marked in Table supplement 2. We revised the corresponding description in lines 140-146

L152: "line graphs" >> "profiles"

Thanks for your suggestions. We corrected it in line 144.

L159: remove "significant" unless statistics are being reported, in which case those need to be explained in detail.

Thanks for your suggestions. We removed "significant" and corrected the corresponding sentences in lines 150-153 to make them more rigorous.

L159: I would recommend including a supplemental somewhere that shows how tall the modeled Quadrapyrgites is and where the cut lines exist above it.

Many thanks for your suggestions. Corresponding complementation was made in the last paragraph of section “Computational fluid dynamics” (line 455 and line 535). We agree that it is appropriate to elucidate the height of modeled Quadrapyrgites and the position of each cut point. Hence, we add a supplementary figure (entitled Figure supplement 1) to illustrate those above.

L183: "The maximum vorticity magnitude was set..." I do not follow what this threshold is based on the current phrasing.

The vorticity magnitude mentioned here is the visualisation range of the color scalebar, which can be set manually set in the software. The positive number represent the vortex rotated counterclockwise, while the negative number represent that rotated clockwise on the cut plane. In this case, the visualisation range is [-0.001,0.001] (i.e., the absolute value of 0.001 is the threshold), as the color scalebar in Figure 7. Decreasing the threshold, for example, setting the visualisation range to [-0.0001,0.0001], can capture smaller vorticity on the cut plane, as the figure below on the left. Otherwise, setting the range to [-0.01,0.01] will focus on bigger vorticity, as the figure below on the right. We found [-0.001,0.001] could be an appropriate parameter to visualize the vortex near periderm based on our trial. To be more rigorous and to avoid confusion, we modified the description in the corresponding place of the manuscript (lines 172-174).

Author response image 1.

L201: "3.9-4 s"

Thanks, we corrected it in line 191.

L269: "Sahin et al.,..." add to the next paragraph

Yes, we rearranged the corresponding two paragraphs (lines 258-289).

L344: "Higher expansion-contraction..." this needs references and/or more justification.

Thanks. We deleted the sentence.

L446: two layers of hexahedral elements is a very low number for meshing boundary layer flow

Many thanks for your question. We agree that an appropriate hexahedral elements mesh for boundary layer is essential to recover boundary flow, especially in cases where turbulence model incorporated with wall function is adopted such as the standard k-epsilon model. In this case, the boundary flow is not the main point since the velocity profile was collected above periderm aperture rather than near no-slip wall region. What else, we do not need drag (related to sheer stress and pressure difference) computations in this case, which requires a more accurate flow velocity reconstruction near no-slip walls as what previous palaeontological CFD simulations have done. Thus, we think two layers of hexahedral elements are enough. What else, hexahedral elements added to periderm aperture domain, as illustrated in figure below, can let the velocity near wall vary smoothly and thus can benefit the convergency of simulations.

Author response image 2.

L449: similar to comments regarding lines 146-148, key information is missing here. Figure 3C appears to be COMSOL's default meshing routine. While it is true that the domain is discretized in a non-uniform manner, no information is provided as to what mesh parameters were "tuned" to determine "optimal settings" or what those settings are (or how they are optimal).

Many thanks for your question. Specific mesh parameters were listed in Table supplement 3 and corresponding descriptions and modifications were made both in lines 475-479 and lines 542-549. In most CFD cases, the mesh parameters need to be tuned to ensure a balance between computational cost and accuracy. If the difference of the result obtained from present mesh and that obtained from the next finer mesh ranges from 5% -10%, the present mesh is expected to be “optimal”. To achieve this, we prescribed several sets of different mesh (mainly concerning maximum and minimum element size) to each subdomain (domain of the inner cavity, domain of the peridermal aperture and domain outside of fossil model) of the whole computational domain in the test model. Subsequently, we refined the mesh step by step as much as possible and adjust the element size of subdomains to find suitable mesh parameters, that is how the mesh parameters were "tuned". We agree that we should explicit what mesh parameters were tuned and what those settings are.

Figure 7 should have the timesteps included and the scaling of the arrows should be explicit in the caption

Many thanks for your suggestions. We intended to use the white arrows to represent the velocity orientation rather than true velocity scale in Figure 7 (Instead, the white arrows in Animation supplement 1 represent a normalized velocity profile). To avoid confusion, we revised Figure 7 with timesteps and arrows represent a normalized velocity profile, making it consistent with Animation supplement 1. Corresponding modification is also made in the caption of Figure 7.

The COMSOL simulation files (raw data) are missing from the supplemental data. These should be posted to Dryad or here.

We uploaded the files to Dryad (https://datadryad.org/stash/share/QGDSqLh8HOll7ofl6JWVrqM57Rp62ZPjvZU0AQQHwTY), and added the corresponding link to section “Data Availability Statement”.

REVIEWER 2

Lines 319-334: The omission in this paragraph of Paraconularia ediacara Leme, Van Iten and Simoes (2022) from the terminal Ediacaran of Brazil is a serious matter, as (1) the medusozoan affinities of this fossil are every bit as well established as those of anabaritids, Sphenothallus, Cambrorhytium and Byronia, and (2) P. ediacara was a large (centimetric) polyp, the presence of which in Precambrian times is thus a problem for the simple evolutionary scenario (very small polyps followed later in evolutionary history by large polyps) outlined in the paragraph. Thus, Paraconularia ediacara must be mentioned in this paper, both in connection with the early evolution of size in cnidarian polyps and in other places where the early evolution of cnidarians is discussed.

Thanks for your important suggestions. We added some sentences in lines 323-326 as following: “Significantly, the large-bodied, skeletonized conulariids-like Paraconularia found from the terminal Ediacaran Tamengo Formation of Brazil confirmed their ancient predators like the extant medusozoans and suggested the origin of cnidarians even farther into the deep evolutionary scenario (Leme et al. 2022).”

Line 23. Delete the word, been.

Line 25. Replace conjecture with conjectural.

Line 26. Delete the word, the before calyx-like.

Line 32. Replace consisting with consistent.

Thanks for your suggestions. We all corrected them.

Author response:

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

eLife assessment

This is a valuable study in which the authors provide an expression profile of the human blood fluke, Schistosoma mansoni. A strength of this solid study is in its inclusion of in situ hybridisation to validate the predictions of the transcript analysis.

We thank the reviewers and the editor for their effort and expertise in reviewing our manuscript. We have made changes based on the reviews and believe this has greatly strengthened our manuscript. We appreciate their insightful comments and suggestions.

Public Reviews:

Reviewer #1 (Public Review):

In this work, the authors provide a valuable transcriptomic resource for the intermediate free-living transmission stage (miracidium larva) of the blood fluke. The single-cell transcriptome inventory is beautifully supplemented with in situ hybridization, providing spatial information and absolute cell numbers for many of the recovered transcriptomic states. The identification of sex-specific transcriptomic states within the populations of stem cells was particularly unexpected. The work comprises a rich resource to complement the biology of this complex system, however falls short in some technical aspects of the bioinformatic analyses of the generated sequence data.

(1) Four sequencing libraries were generated and then merged for analysis, however, the authors fail to document any parameters that would indicate that the clustering does not suffer from any batch effects.

We thank the reviewer for this comment which has given us the opportunity to elaborate on this interesting point. Consequently, we have added evidence to show that the data do not suffer from batch effects between samples (e.g. between sorted samples 1 and 4, and unsorted samples 2 and 3). We now show that there are contributions to all clusters from sorted and unsorted samples and highlight the benefits to using both conditions in a cell atlas with unknown cell types.

Accordingly, we have now added the following paragraph to line 153:

There were contributions from sorted and unsorted samples in almost all clusters (except ciliary plates). We found that some cell/tissue types had similar recovery from both methods (e.g. Stem A, Muscle 2, and Tegument), others were preferentially recovered by sorting (e.g Neuron 1, Neuron 4, and Stem E), and some were depleted by sorting (e.g. Parenchyma 1, Protonephridia, and Ciliary plates) (Supplementary Figure 1) , Supplementary Table 4). This variation in recovery, therefore, enabled us to maximise the discovery and inclusion of different cell types in the atlas.

We have now added a Supplementary Figure 1 showing the contribution of sorted and unsorted cells to the Seurat clusters. We have also included a Supplementary Table 4 detailing the cell number contribution for both conditions and the percentages in order to easily compare differential recovery between cell types.

These are added to the manuscript.

(2) Additionally, the authors switch between analysis platforms without a clear motivation or explanation of what the fundamental differences between these platforms are. While in theory, any biologically robust observation should be recoverable from any permutation of analysis parameters, it has been recently documented that the two popular analysis platforms (Seurat - R and scanPy python) indeed do things slightly differently and can give different results (https://www.biorxiv.org/content/10.1101/2024.04.04.588111v1). For this reason, I don't think that one can claim that Seurat fails to find clusters resolved by SAM without running a similar pipeline on the cluster alone as was done with SAM/scanPy here. The manuscript itself needs to be checked carefully for misleading statements in this regard.

We thank the reviewer for this comment and agree that it’s important to increase the clarity on this matter. We have added additional detail to explain that results of subclustering Neuron 1 using Seurat and SAM/ScanPy were broadly similar, but that we presented the results from the SAM/ScanPy analysis due to the strengths of SAM in detecting small differences in gene expression (Tarashanky et al., 2019 PMID: 31524596). We have included here the UMAP showing subclustering of Neuron 1 in Seurat for comparison.

Author response image 1.

UMAP showing subclustering of Neuron 1 cluster in Seurat (SCT normalisation, PC = 19, resolution = 0.3).

We’ve added this additional text to the ‘Neuron abundance and diversity’ section on line 220:

We explored whether Neuron 1 could be further subdivided into transcriptionally distinct cells by subclustering (Supplementary Figure 2; Supplementary Table 6) using the self-assembling manifold (SAM) algorithm (Tarashansky et al., 2019) with ScanPy (Wolf et al., 2018), given its reported strength in discerning subtle variation in gene expression (Tarashansky et al., 2019), although a similar topology was subsequently found using Seurat.

(3) Similarly, the manuscript contains many statements regarding clusters being 'connected to', or forming a 'bridge' on the UMAP projection. One must be very careful about these types of statements, as the relative position of cells on a reduced-dimension cell map can be misleading (see Chari and Pachter 2023). To support these types of interpretations, the authors should provide evidence of gene expression transitions that support connectivity as well as stability estimates of such connections under different parameter conditions. Otherwise, these descriptors hold little value and should be dropped and the transcriptomic states simply defined as clusters with no reference to their positions on the UMAP.

We thank the reviewer for this thoughtful comment. We agree and have rephrased those statements accordingly e.g. line numbers 218, 439, 543, and 557.

(4) The underlying support for the clusters as transcriptomically unique identities is not well supported by the dot plots provided. The authors used very permissive parameters to generate marker lists, which hampers the identification of highly specific marker genes. This permissive approach can allow for extensive lists of upregulated genes for input into STRING/GO analyses, this is less useful for evaluating the robustness of the cluster states. Running the Seurat::FindAllMarkers with more stringent parameters would give a more selective set of genes to display and thereby increase the confidence in the reader as to the validity of profiles selected as being transcriptomically unique.

The Reviewer is correct in noting that we used a permissive approach to enable a better understanding of the biology of each cluster, based on analysing enriched functions. However, we disagree about the suitability of the approach for finding markers. First, the permissive approach produced longer candidate lists, but those with the best AUC scores for each cluster are at the top of the list for each cluster. Second, some of the markers with lower expression also revealed interesting biology (e.g. Notum in the muscles). Furthermore, we used filtering on the marker genes lists to increase the minimum marker gene scores for analyses such as the GO analyses (details in the GO section of the methods). It’s important to stress that our approach also utilised validation by FISH for top marker genes, as well as biologically informative genes that were lower down the marker gene list.

(5) Figure 5B shows a UMAP representation of cell positions with a statement that the clustering disappears. As a visual representation of this phenomenon, the UMAP is a very good tool, however, to make this statement you need to re-cluster your data after the removal of this gene set and demonstrate that the data no longer clusters into A/B and C/D.

We’ve added Supplementary Figure 13 to show that after removing WSR and ZSR genes and reclustering, the data no longer clusters in A/B and C/D, even at a higher resolution where clusters appear oversplit.

Also, as a reader, these data beg the question: which genes are removed here? Is there an over-representation of any specific 'types' of genes that could lead to any hypotheses of the function? Perhaps the STRING/GO analyses of this gene set could be informative.

We have performed GO-enrichment analyses on W-specific genes, Z-specific genes and both together compared to the rest of the genome, but we did not find very informative results (see Supplementary Table 13 that we have now added, line 464). This may be due to the large difference in size. There are approx 900 Z-specific genes (males two copy, females one copy), while approx 30 W-specific genes many of which have homologs in the Z-specific region of the genome. Instead we suggest that tissue-specific regulation of gene dosage compensation is the more likely explanation as reported for other species (Valsecchi et al. 2018).

(6) How do the proportions of cell types characterized via in situ here compare to the relative proportions of clusters obtained? It does not correspond to the percentages of the clusters captured (although this should be quantified in a similar manner in order to make this comparison direct: 10,686/20,478 = ~50% vs. 7%), how do you interpret this discrepancy? While this is mentioned in the discussion, there is no sufficient postulation as to why you have an overabundance of the stem cells compared to their presence in the tissue. While it is true that you could have a negative selection of some cell types, for example as stated the size of the penetration glands exceeds both that of the 10x capabilities (40uM), and the 30uM filters used in the protocol, this does not really address why over half of the captured cells represent 'stem cells'. A more realistic interpretation would be biological rather than merely technical. For example, while the composition of the muscle cells and the number of muscle transcriptomes captured are quite congruent at ~20%, the organism is composed of more than 50% of neurons, but only 15% of the transcriptomic states are assigned to neuronal. Could it be that a large fraction of the stem cells are actually neural progenitors? Are there other large inconsistencies between the cluster sizes and the fraction of expected cells? Could you look specifically at early transcription factors that are found in the neurons (or other cell types) within the various stem cell populations to help further refine the precursor/cell type relationships?

Yes, it is really interesting that more than 50% of cells in the animal are neurons whereas more than 50% of cells in scRNAseq data are stem cells. This dataset provides a unique opportunity to compare tissue composition in the whole animal to the corresponding single cell RNAseq dataset.

The table (in Supplementary Table 17) shows the percentage of cells from each tissue type in the miracidium (identified via in situ hybridisation of tissue-type marker genes) and in the scRNAseq to understand this phenomenon.

This table shows that the single cell protocol used in this study negatively selected for nerves and tegument, and positively selected for stem and parenchyma. The composition of the muscle and protonephridia cells and the number of muscle and protonephridia transcriptomes captured are quite congruent.

This technical finding is also biologically consistent. For instance, the tegument cells span the body wall muscles, with the cell bodies below and a syncytial layer above. It is not known how the tegument fragments during the dissociation process, and which parts of the cells get packaged by the 10X GEMs. Because of tegumental structure, the cells are likely prone to damage, and therefore we speculate that is why the tegument cells are under-represented in our 10X data. Unusually shaped fragments may not have been captured in 10X GEMs and of those that were, damaged or distressed tegument cells/fragments may have been excluded post-sequencing, by QC filters including cell calling, mitochondrial percentage and low transcript count (e.g. if there there was a tegumental fragment with 100 transcripts it would have not passed QC). Stem cells are spherical with a large nucleus:cytoplasm ratio, likely making them more robust during dissociation and more likely to be captured in 10X GEMs.

We don’t think that a large fraction of the stem cells are actually neural progenitors because:

(1) we used previously reported marker genes of different tissue types to identify the single cell RNAseq clusters, e.g. Ago2-1 for stem cells, which has been used in multiple life stages.

(2) The stem cell transcriptomes express many previously reported stem cell marker genes.

(3) We found that the stem cells from the single cell data generally had higher numbers of transcripts than the other cell types which is consistent with the Wang et al. 2013 observation that RNA marker POPO-1 could distinguish germinal (stem) cells from other cell types as they are RNA rich.

(4) We also found higher numbers of ribosomal related transcripts in our stem cell transcriptomes, which is consistent with Pan’s observation that part of the distinct morphology of stem cells is densely packed ribosomes in the cytoplasm.

In order to elaborate on this discussion we have generated new visualisations:

(1) A UMAP of the stem cell marker ago2-1 (Supplementary figure 10), to further illustrate our evidence in classifying the stem cell clusters

(2) A co-expression plot of the stem cell marker ago2-1 with neural marker complexin to confirm that there is little coexpression (the most coexpression being in Neuron 1 and Stem F). We identified that 15.56% of cells in the Stem F cluster show some expression of complexin (neural marker), suggesting that a small fraction of Stem F may be early/precursor neurons, but the gene expression indicates that the majority of cells in Stem F are more likely to be stem cells than any other tissue type. There is little to no complexin expression in the other stem clusters.

(3) Expression plots of the 5 neurogenins (TFs involved in neuronal differentiation) we could identify using WormBase ParaSite in these data. Four of the five showed very little expression, and not in specific clusters. The fifth (Smp_072470) showed slightly more expression, though still sparse, mostly across the stem and neural clusters not enough to indicate that any of the stem clusters are neural progenitors.

Author response image 2.

Coexpression UMAP showing the expression of stem cell marker Ago2-1 and neural marker complexin.

Author response image 3.

UMAPs showing the expression five putative neurogenins of S.mansoni.

Reviewer #2 (Public Review):

Summary:

In this manuscript the authors have generated a single-cell atlas of the miracidium, the first free-living stage of an important human parasite, Schistosoma mansoni. Miracidia develop from eggs produced in the mammalian (human) host and are released into freshwater, where they can infect the parasite's intermediate snail host to continue the life cycle. This study adds to the growing single-cell resources that have already been generated for other life-cycle stages and, thus, provides a useful resource for the field.

Strengths:

Beyond generating lists of genes that are differentially expressed in different cell types, the authors validated many of the cluster-defining genes using in situ hybridization chain reaction. In addition to providing the field with markers for many of the cell types in the parasite at this stage, the authors use these markers to count the total number of various cell types in the organism. Because the authors realized that their cell isolation protocols were biasing the cell types they were sequencing, they applied a second method to help them recover additional cell types.

Schistosomes have ZW sex chromosomes and the authors make the interesting observation that the stem cells at this stage are already expressing sex (i.e. W)-specific genes.

Weaknesses:

The sample sizes upon which the in situ hybridization results and cell counts are based are either not stated (in most cases) or are very small (n=3). This lack of clarity about biological replicates and sample sizes makes it difficult for the reader to assess the robustness of the results and the extremely small sample sizes (when provided) are a missed opportunity to explore the variability of the system, or lack thereof.

We have now added more details about the methods we used for validating cell type marker genes by in situ hybridisation. We have added to the methods that ‘We carried out at least three in situ hybridisation experiments for each marker gene we validated (each experiment was a biological replicate). From each experiment we imaged (by confocal microscopy) at least 10 miracidia (technical replicates) per marker gene experiment.’ on line 1036.

In the figure legends we have added the number of miracidia that were screened, and documented the percentage of the screened larvae that showed the in situ gene expression pattern that is seen in the images in the figures, and that we described in the text.

We manually segmented the nuclei of pan tissue marker genes, and we did this for one miracidium in the case of all tissues, except stem cells where we segmented stem cells in five larvae. Manual segmentation of gene expression in a confocal z-stack is very time consuming. We consider that the variability of different cell and tissue types (stereotypy) between miracidia is beyond the scope of this paper and can be investigated in future work.

Although assigning transcripts to a given cell type is usually straightforward via in situ experiments, the authors fail to consider the potential difficulty of assigning the appropriate nuclei to cells with long cytoplasmic extensions, like neurons. In the absence of multiple markers and a better understanding of the nervous system, it seems likely that the authors have overestimated the number of neurons and misassigned other cell types based on their proximity to neural projections.

This is a valid point, and we acknowledge the difficulties of assigning a nucleus to a cell using mRNA expression only and in the absence of a cell membrane marker. We tried to address this issue by labelling the cell membranes using an antibody against beta catenin after the HCR in situ protocol. This method has been used successfully on sections on slides (Schulte et al., 2024), but we failed to get usable results in our miracidia whole-mounts. The beta catenin localisation marked the membranes of the gland cells but didn’t do the same for the neurons or other cell types (see image below).

Author response image 4.

Image showing a maximum intensity projection of a subvolume of a confocal z-stack of a miracidia wholemount in situ hybridisation (by HCR) for paramyosin counterstained with a beta catenin antibody (1:600 concentration of Sigma C2206). The cell membrane of a lateral gland is clearly labelled, but those of the neurons of the brain and the paramyosin+ muscle cells are not.

Our observation that 57% of the cells in a miracidium are nerves is high compared to the C.elegans hermaphrodite adult in which 302 out of 959 cells are neurons (Hobert et al., 2016), few studies have equivalent data with which to make comparisons. Despite this, and the limitation described above, we believe that we have not overestimated the number of neural cells. During the process of validating the marker genes and closely examining gene expression in hundreds of miracidia, we noted that the nuclei of different tissue types are distinct and recognisable (see figure below). The nuclei of stem, tegument and parenchymal cells are comparatively large and spherical with obvious nucleoli (i). The four nuclei of the apical gland cell are angular, pentagonal in shape and sit adjoining each other (inside red dashed circle, i-iii), those of the two lateral glands are bilaterally symmetrical and surrounded by flask shaped cytoplasm (arrows, iv). The nuclei of the body wall muscle cells are peripheral and flattened on the outer edge (iii). The notum+ muscle cell nuclei are anterior of the apical gland (manuscript Figure 2E). The only other two tissue types are the nerves and protonephridia, and their nuclei are smaller and more compact/condensed. In situ expression of the protonephridia marker suggests that 6 cells make up the protonephridial system (manuscript Figure 4 B&E). Therefore, by process of elimination, the remaining nuclei should belong to neurons. The complexin expression pattern supports this and we counted 209 nuclei that were surrounded by cpx transcript expression. To help the reader interpret this for themselves we have added confocal z-stacks of miracidia where tissue level markers have been multiplexed (supplementary videos 18-20). We counted all tissue type cells individually and the tissue type cell numbers added up to the overall cell count.

Author response image 5.

Image showing the diversity of nucleus morphology between tissue types in the miracidium.

Biologically, it is not surprising that this larva is dominated by neural cells. It must navigate a complex aquatic environment and identify a suitable mollusc host in less than 12 hours. It is a non-feeding vehicle that must deliver the stem cells to a suitable environment where they can develop into the subsequent life cycle stage. Accordingly, the cell type composition reflects this challenge.

The conclusion that germline genes are expressed in the miracidia stem cells seems greatly overstated in the absence of any follow-up validation. The expression scales for genes like eled and boule are more than 3 orders of magnitude smaller than those used for any of the robustly expressed genes presented throughout the paper. These scales are undefined, so it isn't entirely clear what they represent, but neither of these genes is detected at levels remotely high (or statistically significant) enough to survive filters for cluster-defining genes.

Given that germ cells often develop early in embryogenesis and arrest the cell cycle until later in development, and that these transcripts reveal no unspliced forms, it seems plausible that the authors are detecting some maternally supplied transcripts that have yet to be completely degraded.

We agree that the expression of genes such as eled and boule are low. We made this clear in the figure legends and text, and have now added scale information to the figure legends. We did not explore these genes as cluster-defining genes, partly due to their comparatively low levels of expression, but as genes already reported to be important in germ line specification. We found the expression of these genes to be consistent with our hypothesis that the Kappa stem cells may include germ line segregated cells, but our hypothesis does not rest on these lower-expressed genes.

It is certainly possible that we have detected some maternally supplied transcripts in the miracidia stem cells. However experiments to distinguish between zygotic and maternal transcripts using metabolic labelling of zygotic transcripts (e.g. Fishman et al. 2023) would be hard in this species due to the hard egg capsule and its ectolethical embryogenesis. Therefore this is out of scope for this work, but this would be a very interesting topic to follow up on and develop tools for.

We have added these sentences to the Discussion ln 746 ‘Intriguingly, the presence of spliced-only copies of the germline defining genes eled and boule could suggest that they are maternal transcripts that have been restricted to the primordial germ cells during embryogenesis, as is the case in Zebrafish embryos (Fishman et al., 2023). An alternative explanation is that unspliced transcripts exist for these lowly expressed genes but their abundance was below our threshold for detection.’

Reviewer #1 (Recommendations For The Authors):

Ln 138: specify the version of Seurat used, and reference the primary papers for this software. Also, from the dot plot shown here, these do not all appear to be supported by unique gene sets. How was the final clustering determined? This information is in the methods section, but a summary here could make it more robust for the readership.

In addition to the details in the methods section, we have added the version and referenced the version-specific primary paper for Seurat when it is first mentioned. We have also summarised the methods used to select the final clustering when we first present the results to aid in clarity.

We added to line 140 ‘Using Seurat (version 4.3.0) (Hao et al., 2021), 19 distinct clusters of cells were identified, along with putative marker genes best able to discriminate between the populations (Figure 1C & D and Supplementary Table 2 and 3). We used Seurat’s JackStraw and ElbowPlot, along with molecular cross-validation to select the number of principal components, and Seurat’s clustree to select a resolution where clusters were stable (Hao et al., 2021).’

Ln 147: isn't seven stem cell clusters a lot? See comment in public review.

We did not have preconceived expectations of the number of stem cell clusters, and were guided by the data and gene expression. In doing so we also discovered that four of those clusters were likely only two ‘biologically or functionally distinct’ clusters, but these split into four clusters based on the expression of genes on the sex-specific regions of the chromosomes, which was both unexpected and interesting.

Figure 1D: gene model names are un-informative for the general reader. Can you provide any putative gene identities here to render this plot interpretable? For example in the main text you state that Smp-085540 is paramyosin; please use this annotation in all your visual material (as is used in Figure 2A).

We have added gene names to the dotplots in all figures with the locus identifier (minus the ‘Smp’ prefix) in brackets after the gene name.

Ln 191:196 Identification of the two muscle clusters as circular and longitudinal muscles is very well supported. However, it would be interesting to look specifically at the genes that are different here. Did the authors attempt to specifically pull out genes differentially expressed between these two groups, or only examine the output of FindAllMarkers at this point?

We did indeed look specifically for genes differentially expressed between the muscle clusters, the results of which can be found in Supplementary Table 5 (Line 206). This analysis revealed “Wnt-11-1 (circular) and MyoD (longitudinal) were among the most differentially expressed genes”, which were important findings in our understanding of the muscle cells in the miracidium.

Ln 207: "connected to stem F" - does this refer specifically to their relative positions on the UMAP in Figure 1C? One must be very careful about these types of statements, as the relative position of cells on a reduced-dimension cell map can be misleading (public review).

We agree, and have rephrased accordingly.

Ln 209:211: Here the authors switch from Seurat (R) as an analysis package, to SAM (python) for subset analysis of one large neural cluster. The results indicate that there may be small populations of transcriptomically distinct neural subtypes also within the neural1 cluster, but that the vast majority of these cells do not express unique transcriptomic profiles. Also in the supplementary material for this (SF1) there is a question of whether or not there is any clustering according to batch effects.

In general, I find the neuronal section a little difficult to follow and it is unclear how many unique profiles are present and which are documented with in situ. I would recommend re-running the analysis on the entire neural subset (n1:5: complexin positive) and generating an inventory of putatively unique neural states with the associated in situ validation altogether in a main figure.

In response to comments above we have both clarified our reasoning for using SAM analysis, and presented more details on possible batch effects. We have gone through the neural system results in order to make it clearer for the reader to follow.

Ln 236: here the authors introduce a STRING analysis for the first time. Also, this method requires some introduction for the general audience in terms of its goals and general functionality and output.

We used STRING analysis on some well defined clusters to provide additional clues about function. At the first mention of STRING (neuron 3 results) we have added the following statement to give more introduction to the reader: “STRING analysis of the top 100 markers of Neuron 3 predicted two protein interaction networks with functional enrichment: ….”

Ln. 280:281. It is unclear why Steger et al is referenced here. In what way does a description of neural and glandular cell transcriptomic similarity in a Cnidarian inform your data on a member of the playhelmenthes? (which should also be referenced in the introduction: to which phylogenetic lineage does Schistosoma belong).

We have now added that the Schistosoma belong to the Platyhelminths on the first line of the introduction.

Ln 295 we have added ‘We expected to find a discrete cluster(s) for the penetration glands, and that it would show similarities to the neural clusters (as glandular cells arise from neuroglandular precursor cells in other animals, such as the sea anemone, Nematostella vectensis, Steger et al., 2022).’

Ln 339: explain the motivation for generating a further plate-based scRNA of the ciliary plates.

We wished to include the ciliary plates alongside the gland cells for plate based RNAseq as they are unique to the miracidium stage and wanted to make sure we had captured them in this study.

Ln 345: Define the tegumental cells for the general reader.

We have added further description on tegument cells in the introduction and tegument results section, e.g. on line 61, 366).

Ln 365: "this cluster" is imprecise. Which cluster are we looking at here?' Also: were flame cells already described morphologically at this stage, or is this the first description of the protonephridial system for this stage of the life cycle?

We have now clarified which cluster we are talking about in the text. The flame cells have been described using TEM before (Pan, 1980).

Stem Cells: also here you refer to cells as 'bridge' which refers to the configuration of the UMAP. While this is likely a biological representation of a different differentiation state, the nomination of this based solely on the UMAP representation should be avoided.

We have rephrased this.

Figure 5B: What is neuron 6? This was Neuron 3 in Figure 1.

Thank you for spotting these mistakes in the labelling, we have corrected them now.

Ln 421:438 - Here you represent a UMAP representation of the cell positions, but state that the clustering disappears. See comment in Public Review.

Modified accordingly, see response in public review.

Ln 472 "Cells in stem E, F, and G in silico clusters might be stressed/damaged/dying cells or cells in transcriptionally transitional states." Is there any evidence supporting either of these conclusions?

We found that 15.56% of the cells in Stem F expressed the neural marker complexin, leading us to consider the possibility that a fraction of these cells may be neural precursors. Stem F also had some cells with a mitochondrial % near the maximum threshold we set, suggesting they could be experiencing some stress. Since we could not identify clear markers for these clusters, their function and a more specific identity, beyond ‘stem’, is not yet known.

That the two stem cell populations contribute to different parts of the next life cycle stage is interesting. The combined analysis suffers from the same issues as the previous analysis in terms of sample distribution; are the 'grey' sporocyst cells also contributing to the stem A/B (kappa) C/D (delta/phi) clusters? This is not possible to tell from the plot as the miracidia may simply be plotted on the top. A different representation of sample contribution to clusters is warranted.

We have made an alternative visualisation here to demonstrate that the miracidia cells are not plotted on top of the sporocyst stem cells. Unfortunately this visual is hampered as there is not a straightforward way to split the panels. In the figure below, the left pane shows the miracidia cells, and the right pane shows the sporocyst cells. Below that, we have included the original figure for comparison. It can be clearly seen that there are three miracidia tegument cells in the sporocyst tegument cluster, and one sporocyst cell in the miracidia stem cells (Stem E), but the miracidia A/B and C/D stem cells are not plotted on top of any sporocyst cells.

Author response image 6.

Methods: Why is the multiplet rate estimate at >50% for the unsorted sample?

We have added more detail on this: “The estimated doublet rate was calculated based on 10X loading guidelines and adjusted for our sample concentrations”.

Reviewer #2 (Recommendations For The Authors):

(1) The manuscript would benefit from a more careful consideration of what was already known based on previous literature, which would help the authors to better put their results in context. For example, previous work suggested that one of the sporocyst stem cell populations (phi) gives rise to tegument and other temporary larval structures; this appears not to be mentioned here. The model in Figure 7 suggests that two of the stem cell populations are gone at day 15 post-infection; the literature shows that those cells can still be detected at this stage (there are just far fewer of them).

We have added the definition of Kappa, Delta and Phi as per Wang et al (2018) in the stem cell results p13 ln 428.

We have amended Figure 7 to include further elements from the Wang et al (2018) paper that show that mother sporocyst stem cells classified as delta and phi are still detectable on day 15 post-infection in mother sporocysts.

We intentionally didn’t put too much emphasis on fitting our data to the model of Wang et al (2018), because a) it’s a different life cycle stage and b) the single cell data the model was based on was from 35 stem cells and gathered using a different method, c) more recent data (Diaz, Attenborough et al. 2024) with 119 stem cells from sporocysts did not recover the same populations of stem cells. We therefore linked our data to previous literature where it was relevant but focused on being led by the data we gathered (>10,000 stem cells).

(2) To add some detail to the public comment about the lack of clarity about sample sizes and biological replicates, and how this leads to questions about the robustness of the results, Figures 4 B and F show the expression pattern for the same parenchyma marker (Smp_318890) in two different samples. The patterns appear quite distinctive. In B, the cell bodies are so clearly labeled that the signal appears oversaturated. In F the cell bodies are barely apparent. Based on the single-cell clustering, it should be possible to distinguish between Parenchyma clusters 1 and 2 based on the levels of this transcript. Careful quantification of signal intensity from multiple samples across multiple experiments might enable the authors to detect such differences.

The reason the expression patterns look different between panels 4Bii and 4F is that in 4Bii we have manually segmented the nuclei of the parenchymal cells in order to count them, whereas in the images in 4F there is no segmentation. We have made this more clear in this legend now, and also in the legends of Figures 2,3, and 5. If there was any signal intensity difference between parenchyma 1 and 2 cells based on expression of the marker gene, Smp_318890, it was not obvious. We carried out 6 experiments for parenchyma markers, multiplexing the pan-parenchyma marker, Smp_318890, with markers for parenchyma 2 but we were unable to distinguish between the two populations.

(3) The authors find that the "somatic" stem cells in miracidia seem to combine attributes of the previously defined delta and phi stem cells from sporocysts. Because the 3 classes of sporocyst stem cells were defined by expression of nanos-2 and fgfrA, using those probes in in-situ experiments could have helped them resolve whether or not the miracidial cells represent precursors that can adopt either fate or if the heterogeneity is already present in miracidia.

In silico expression of the marker genes for the 3 classes of sporocyst stem cells didn’t support those three classes in the miracidia stem cells (See supplementary table 10). We further subclustered the delta/phi cells to see if we could recover separate delta and phi populations but we were unable to do so. We therefore did not pursue in situ experiments of these genes. We instead prioritised cluster-defining genes in the miracidia stem cell populations rather than cluster defining genes in the sporocyst (defined by Wang et al., 2018), but we still explored these in silico. For example, instead of using klf to define Kappa (Wang et al 2018), we used UPPA to validate the Kappa population as it showed similar expression to klf but higher expression levels and was specific to that population. However, like Wang et al 2018, we did use p53, which is a cluster marker of delta and phi in sporocysts, as it showed clear and high expression in our miracidia delta/phi population. We were guided by our data and our knowledge of the literature. More in depth single cell RNAseq is needed from the mother and daughter sporocyst stages to understand the heterogeneity and fates of these stem populations.

(4) Scale bars should be included throughout the figures and the scale should be defined either on the figure or in the legend. Similarly, all the scales used for velocity and expression analysis should be defined.

We have added scale bars to all figures and legends.

The statements “Gene expression has been log-normalised and scaled using Seurat(v. 4.3.0)”, “Gene expression has been normalised (CPM) and log-transformed using scvelo(v. 0.2.4)”, or “Library size was normalised and gene expression values were log-normalised using SAM (v1.0.1) and Scanpy (v1.8.2)” has been added to all figures as appropriate.

(5) The table entitled In situ hybridization probes (Supplementary Table 15) contains no probe sequences, so any interested reader wishing to use these probes would have to design their own. To ensure the reproducibility of the results presented here, the authors should provide the probe sequences they used.

In Supplementary Table 15 we have added the Molecular Instruments Lot number of all the probes used. Anyone wanting to repeat the experiment can order the same probes from the company.

(6) It is unclear how useful the supplemental figures showing the STRING enrichment analyses will be for readers. Unannotated Smp gene identifiers provide no way to help readers digest the information in these hairballs. It would probably be best to replace the Smp names with useful annotations based on their orthologs; if not, these figures could probably be dropped entirely. (Also, the bottom panel of Supplementary Figure 7 has the word "Lorem" embedded on one of the connecting nodes.)

“Lorem” has been removed.

Many of the genes in these analyses do not have short descriptions, therefore we have used Smp gene identifiers in the STRING analysis supplementary figures. These ‘Smp_’ numbers can be used to search WormBase Parasite, where a description can be found and the history of the gene ID traced. This latter function facilitates searching for these genes in the literature and consistency between versions as gene models are updated.

Minor edits

(1) Figures 4A-D aren't cited in the text until after 4E-F are. It seems like moving the section on protonephridial cells (line 364) before the section on tegumental cells (line 345) better reflects the order of the figures.

Thank you for flagging this, we have updated the in-text citations of Figure 4.

(2) In-text references to Sarfati et al, 2021 should be to Nanes Sarfati, as listed in the references. Poteaux et al 2023 is cited in the text, but not in the reference list.

Both of these have been fixed.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The study introduces and validates the Cyclic Homogeneous Oscillation (CHO) detection method to precisely determine the duration, location, and fundamental frequency of non-sinusoidal neural oscillations. Traditional spectral analysis methods face challenges in distinguishing the fundamental frequency of non-sinusoidal oscillations from their harmonics, leading to potential inaccuracies. The authors implement an underexplored approach, using the auto-correlation structure to identify the characteristic frequency of an oscillation. By combining this strategy with existing time-frequency tools to identify when oscillations occur, the authors strive to solve outstanding challenges involving spurious harmonic peaks detected in time-frequency representations. Empirical tests using electrocorticographic (ECoG) and electroencephalographic (EEG) signals further support the efficacy of CHO in detecting neural oscillations.

Response:  We thank the reviewer for recognizing the strengths of our method in this encouraging review and for the opportunity to further improve and finalize our manuscript.

Strengths:

(1) The paper puts an important emphasis on the 'identity' question of oscillatory identification. The field primarily identifies oscillations through frequency, space (brain region), and time (length, and relative to task or rest). However, more tools that claim to further characterize oscillations by their defining/identifying traits are needed, in addition to data-driven studies about what the identifiable traits of neural oscillations are beyond frequency, location, and time. Such tools are useful for potentially distinguishing between circuit mechanistic generators underlying signals that may not otherwise be distinguished. This paper states this problem well and puts forth a new type of objective for neural signal processing methods.

Response:  We sincerely appreciate this encouraging summary of the objective of our manuscript.

(2) The paper uses synthetic data and multimodal recordings at multiple scales to validate the tool, suggesting CHO's robustness and applicability in various real-data scenarios. The figures illustratively demonstrate how CHO works on such synthetic and real examples, depicting in both time and frequency domains. The synthetic data are well-designed, and capable of producing transient oscillatory bursts with non-sinusoidal characteristics within 1/f noise. Using both non-invasive and invasive signals exposes CHO to conditions which may differ in extent and quality of the harmonic signal structure. An interesting followup question is whether the utility demonstrated here holds for MEG signals, as well as source-reconstructed signals from non-invasive recordings.

Response:  We thank the reviewer for this excellent suggestion.  Indeed, our next paper will focus on applying our CHO method to signals that were source-reconstructed from non-invasive recordings (e.g., MEG and EEG) to extract their periodic activity.

(3) This study is accompanied by open-source code and data for use by the community.

Response:  We thank the reviewer for recognizing our effort to widely disseminate our method to the broader community.

Weaknesses:

(1) Due to the proliferation of neural signal processing techniques that have been designed to tackle issues such as harmonic activity, transient and event-like oscillations, and non-sinusoidal waveforms, it is naturally difficult for every introduction of a new tool to include exhaustive comparisons of all others. Here, some additional comparisons may be considered for the sake of context, a selection of which follows, biased by the previous exposure of this reviewer. One emerging approach that may be considered is known as state-space models with oscillatory and autoregressive components (Matsuda 2017, Beck 2022). State-space models such as autoregressive models have long been used to estimate the auto-correlation structure of a signal. State-space oscillators have recently been applied to transient oscillations such as sleep spindles (He 2023). Therefore, state-space oscillators extended with auto-regressive components may be able to perform the functions of the present tool through different means by circumventing the need to identify them in time-frequency. Another tool that should be mentioned is called PAPTO (Brady 2022). Although PAPTO does not address harmonics, it detects oscillatory events in the presence of 1/f background activity. Lastly, empirical mode decomposition (EMD) approaches have been studied in the context of neural harmonics and nonsinusoidal activity (Quinn 2021, Fabus 2022). EMD has an intrinsic relationship with extrema finding, in contrast with the present technique. In summary, the existence of methods such as PAPTO shows that researchers are converging on similar approaches to tackle similar problems. The existence of time-domain approaches such as state-space oscillators and EMD indicates that the field of timeseries analysis may yield even more approaches that are conceptually distinct and may theoretically circumvent the methodology of this tool.

Response:  We thank the reviewer for this valuable insight.  In our manuscript, we acknowledge emerging approaches that employ state-space models or EMD for time-frequency analysis.  However, it's crucial to clarify that the primary focus in our study is on the detection and identification of the fundamental frequency, as well as the onset/offset of non-sinusoidal neural oscillations.  Thus, our emphasis lies specifically on these aspects.  We hope that future studies will use our methods as the basis to develop better methods for time-frequency analysis that will lead to a deeper understanding of harmonic structures.  

Our Limitation section is addressing this issue.  Specifically, we recognize that a more sophisticated time-frequency analysis could contribute to improved sensitivity and that the core claim of our study is centered around the concept of increasing specificity in the detection of non-sinusoidal oscillations.  We hope that future studies will use this as a basis for improving time-frequency analysis in general.  Notably, our open-source code will greatly enable these future studies in this endeavor.  Specifically, in the first step of our algorithm, the timefrequency estimation can be replaced with any other preferred time-frequency analysis, such as state-space models, EMD, Wavelet transform, Gabor transform, and Matching Pursuit. 

For our own follow-up study, we plan to conduct a thorough review and comparison of emerging approaches employing state-space models or EMD for time-frequency analysis.  In this study, we aim to identify which approach, including the six methods mentioned by the reviewer (Matsuda 2017, Beck 2022, He 2023, Brady 2022, Quinn 2021, and Fabus 2022), can maximize the estimation of the fundamental frequency of non-sinusoidal neural oscillations using CHO.  The insights provided by the reviewer are appreciated, and we will carefully consider these aspects in our follow-up study.  

In the revision of this manuscript, we are setting the stage for these future studies.  Specifically, we added a discussion paragraph within the Limitation section about the state-space model, and EMD approaches:

“However, because our CHO method is modular, the FFT-based time-frequency analysis can be replaced with more sophisticated time-frequency estimation methods to improve the sensitivity of neural oscillation detection.  Specifically, a state-space model (Matsuda 2017, Beck 2022, He 2023, Brady 2022) or empirical mode decomposition (EMD, Quinn 2021, Fabus 2022) may improve the estimation of the auto-correlation of the harmonic structure underlying nonsinusoidal oscillations.  Furthermore, a Gabor transform or matching pursuit-based approach may improve the onset/offset detection of short burst-like neural oscillations (Kus 2013 and Morales 2022).”

(2) The criteria that the authors use for neural oscillations embody some operating assumptions underlying their characteristics, perhaps informed by immediate use cases intended by the authors (e.g., hippocampal bursts). The extent to which these assumptions hold in all circumstances should be investigated. For instance, the notion of consistent auto-correlation breaks down in scenarios where instantaneous frequency fluctuates significantly at the scale of a few cycles. Imagine an alpha-beta complex without harmonics (Jones 2009). If oscillations change phase position within a timeframe of a few cycles, it would be difficult for a single peak in the auto-correlation structure to elucidate the complex time-varying peak frequency in a dynamic fashion. Likewise, it is unclear whether bounding boxes with a pre-specified overlap can capture complexes that maneuver across peak frequencies.

Response:  We thank the reviewer for this valuable insight into the methodological limitations in the detection of neural oscillations that exhibit significant fluctuations in their instantaneous frequency.  Indeed, our CHO method is also limited in the ability to detect oscillations with fluctuating instantaneous frequencies.  This is because CHO uses an auto-correlation-based approach to detect neural oscillations that exhibit two or more cycles.  If oscillations change phase position within a timeframe of a few cycles, CHO cannot detect the oscillation because the periodicity is not expressed within the auto-correlation.  This limitation can be partially overcome by relaxing the detection threshold (see Line 30 of Algorithm 1 in the revised manuscript) for the auto-correlation analysis.  However, relaxing the detection threshold, in consequence, increases the probability of detecting other aperiodic activity as well. To clarify how CHO determines the periodicity of oscillations, and to educate the reader about the tradeoff between detecting oscillations with fluctuating instantaneous frequencies and avoiding detecting other aperiod activity, we have added pseudo code and a new subsection in the Methods.

Author response table 1.

Algorithm 1

A new subsection titled “Tradeoffs in adjusting the hyper-parameters that govern the detection in CHO”.

“The ability of CHO to detect neural oscillations and determine their fundamental frequency is governed by four principal hyper-parameters.  Adjusting these parameters requires understanding their effect on the sensitivity and specificity in the detection of neural oscillations. 

The first hyper-parameter is the number of time windows (N in Line 5 in Algorithm 1), that is used to estimate the 1/f noise.  In our performance assessment of CHO, we used four windows, resulting in estimation periods of 250 ms in duration for each 1/f spectrum.  A higher number of time windows results in smaller estimation periods and thus minimizes the likelihood of observing multiple neural oscillations within this time window, which otherwise could confound the 1/f estimation.  However, a higher number of time windows and, thus, smaller time estimation periods may lead to unstable 1/f estimates. 

The second hyper-parameter defines the minimum number of cycles of a neural oscillation to be detected by CHO (see Line 23 in Algorithm 1).  In our study, we specified this parameter to be two cycles.  Increasing the number of cycles increases specificity, as it will reject spurious oscillations.  However, increasing the number also reduces sensitivity as it will reject short oscillations.

The third hyper-parameter is the significance threshold that selects positive peaks within the auto-correlation of the signal.  The magnitude of the peaks in the auto-correlation indicates the periodicity of the oscillations (see Line 26 in Algorithm 1).  Referred to as "NumSTD," this parameter denotes the number of standard errors that a positive peak has to exceed to be selected to be a true oscillation.  For this study, we set the "NumSTD" value to 1.  Increasing the "NumSTD" value increases specificity in the detection as it reduces the detection of spurious peaks in the auto-correlation.  However, increasing the "NumSTD" value also decreases the sensitivity in the detection of neural oscillations with varying instantaneous oscillatory frequencies. 

The fourth hyper-parameter is the percentage of overlap between two bounding boxes that trigger their merger (see Line 31 in Algorithm 1).  In our study, we set this parameter to 75% overlap.  Increasing this threshold yields more fragmentation in the detection of oscillations, while decreasing this threshold may reduce the accuracy in determining the onset and offset of neural oscillations.”

(3) Related to the last item, this method appears to lack implementation of statistical inferential techniques for estimating and interpreting auto-correlation and spectral structure. In standard practice, auto-correlation functions and spectral measures can be subjected to statistical inference to establish confidence intervals, often helping to determine the significance of the estimates. Doing so would be useful for expressing the likelihood that an oscillation and its harmonic has the same autocorrelation structure and fundamental frequency, or more robustly identifying harmonic peaks in the presence of spectral noise. Here, the authors appear to use auto-correlation and time-frequency decomposition more as a deterministic tool rather than an inferential one. Overall, an inferential approach would help differentiate between true effects and those that might spuriously occur due to the nature of the data. Ultimately, a more statistically principled approach might estimate harmonic structure in the presence of noise in a unified manner transmitted throughout the methodological steps.

Response:  We thank the reviewer for sharing this insight on further enhancing our method.  Indeed, CHO does not make use of statistical inferential statistics to estimate and interpret the auto-correlation and underlying spectral structure of the neural oscillation.  Implementing this approach within CHO would require calculating phase-phase coupling across all cross-frequency bands and bounding boxes.  However, as mentioned in the introduction section and Figure 1GL, phase-phase coupling analysis cannot fully ascertain whether the oscillations are phaselocked and thus are harmonics or, indeed, independent oscillations.  This ambiguity, combined with the exorbitant computational complexity of the entailed permutation test and the requirement to perform the analysis across all cross-frequency bands, channels, and trials, makes phase-phase coupling impracticable in determining the fundamental frequency of neural oscillations in real-time and, thus, the use in closed-loop neuromodulation applications.  Thus, within our study, we prioritized determining the fundamental frequency without considering the structure of harmonics.  

An inferential approach can be implemented by adjusting the significance threshold that selects positive peaks within the auto-correlation of the signal.  Currently, this threshold is set to represent the approximate confidence bounds of the periodicity of the fundamental frequency.  To clarify this issue, we added additional pseudo code and a new subsection, titled “Tradeoffs in adjusting the hyper-parameters that govern the detection in CHO,” in the Methods section.

In future studies, we will investigate the harmonic structure of neural oscillations based on a large data set.  This exploration will help us understand how non-sinusoidal properties may influence the harmonic structure.  Your input is highly appreciated, and we will diligently incorporate these considerations into our research.

See Author response table 1.

A new subsection titled “Tradeoffs in adjusting the hyper-parameters that govern the detection in CHO”.

“The ability of CHO to detect neural oscillations and determine their fundamental frequency is governed by four principal hyper-parameters.  Adjusting these parameters requires understanding their effect on the sensitivity and specificity in the detection of neural oscillations. 

The first hyper-parameter is the number of time windows (N in Line 5 in Algorithm 1), that is used to estimate the 1/f noise.  In our performance assessment of CHO, we used four windows, resulting in estimation periods of 250 ms in duration for each 1/f spectrum.  A higher number of time windows results in smaller estimation periods and thus minimizes the likelihood of observing multiple neural oscillations within this time window, which otherwise could confound the 1/f estimation.  However, a higher number of time windows and, thus, smaller time estimation periods may lead to unstable 1/f estimates. 

The second hyper-parameter defines the minimum number of cycles of a neural oscillation to be detected by CHO (see Line 23 in Algorithm 1).  In our study, we specified this parameter to be two cycles.  Increasing the number of cycles increases specificity, as it will reject spurious oscillations.  However, increasing the number also reduces sensitivity as it will reject short oscillations.

The third hyper-parameter is the significance threshold that selects positive peaks within the auto-correlation of the signal.  The magnitude of the peaks in the auto-correlation indicates the periodicity of the oscillations (see Line 26 in Algorithm 1).  Referred to as "NumSTD," this parameter denotes the number of standard errors that a positive peak has to exceed to be selected to be a true oscillation.  For this study, we set the "NumSTD" value to 1.  Increasing the "NumSTD" value increases specificity in the detection as it reduces the detection of spurious peaks in the auto-correlation.  However, increasing the "NumSTD" value also decreases the sensitivity in the detection of neural oscillations with varying instantaneous oscillatory frequencies. 

The fourth hyper-parameter is the percentage of overlap between two bounding boxes that trigger their merger (see Line 31 in Algorithm 1).  In our study, we set this parameter to 75% overlap.  Increasing this threshold yields more fragmentation in the detection of oscillations, while decreasing this threshold may reduce the accuracy in determining the onset and offset of neural oscillations.”

(4) As with any signal processing method, hyperparameters and their ability to be tuned by the user need to be clearly acknowledged, as they impact the robustness and reproducibility of the method. Here, some of the hyperparameters appear to be: a) number of cycles around which to construct bounding boxes and b) overlap percentage of bounding boxes for grouping. Any others should be highlighted by the authors and clearly explained during the course of tool dissemination to the community, ideally in tutorial format through the Github repository.

Response:  We thank the reviewer for this helpful suggestion.  In response, we added a new subsection that describes the hyper-parameters of CHO as follows:

A new subsection named “Tradeoffs in adjusting the hyper-parameters that govern the detection in CHO”.

“The ability of CHO to detect neural oscillations and determine their fundamental frequency is governed by four principal hyper-parameters.  Adjusting these parameters requires understanding their effect on the sensitivity and specificity in the detection of neural oscillations. 

The first hyper-parameter is the number of time windows (N in Line 5 in Algorithm 1), that is used to estimate the 1/f noise.  In our performance assessment of CHO, we used four windows, resulting in estimation periods of 250 ms in duration for each 1/f spectrum.  A higher number of time windows results in smaller estimation periods and thus minimizes the likelihood of observing multiple neural oscillations within this time window, which otherwise could confound the 1/f estimation.  However, a higher number of time windows and, thus, smaller time estimation periods may lead to unstable 1/f estimates. 

The second hyper-parameter defines the minimum number of cycles of a neural oscillation to be detected by CHO (see Line 23 in Algorithm 1).  In our study, we specified this parameter to be two cycles.  Increasing the number of cycles increases specificity, as it will reject spurious oscillations.  However, increasing the number also reduces sensitivity as it will reject short oscillations.

The third hyper-parameter is the significance threshold that selects positive peaks within the auto-correlation of the signal.  The magnitude of the peaks in the auto-correlation indicates the periodicity of the oscillations (see Line 26 in Algorithm 1).  Referred to as "NumSTD," this parameter denotes the number of standard errors that a positive peak has to exceed to be selected to be a true oscillation.  For this study, we set the "NumSTD" value to 1.  Increasing the "NumSTD" value increases specificity in the detection as it reduces the detection of spurious peaks in the auto-correlation.  However, increasing the "NumSTD" value also decreases the sensitivity in the detection of neural oscillations with varying instantaneous oscillatory frequencies. 

The fourth hyper-parameter is the percentage of overlap between two bounding boxes that trigger their merger (see Line 31 in Algorithm 1).  In our study, we set this parameter to 75% overlap.  Increasing this threshold yields more fragmentation in the detection of oscillations, while decreasing this threshold may reduce the accuracy in determining the onset and offset of neural oscillations.”

(5) Most of the validation demonstrations in this paper depict the detection capabilities of CHO. For example, the authors demonstrate how to use this tool to reduce false detection of oscillations made up of harmonic activity and show in simulated examples how CHO performs compared to other methods in detection specificity, sensitivity, and accuracy. However, the detection problem is not the same as the 'identity' problem that the paper originally introduced CHO to solve. That is, detecting a non-sinusoidal oscillation well does not help define or characterize its non-sinusoidal 'fingerprint'. An example problem to set up this question is: if there are multiple oscillations at the same base frequency in a dataset, how can their differing harmonic structure be used to distinguish them from each other? To address this at a minimum, Figure 4 (or a followup to it) should simulate signals at similar levels of detectability with different 'identities' (i.e. different levels and/or manifestations of harmonic structure), and evaluate CHO's potential ability to distinguish or cluster them from each other. Then, does a real-world dataset or neuroscientific problem exist in which a similar sort of exercise can be conducted and validated in some way? If the "what" question is to be sufficiently addressed by this tool, then this type of task should be within the scope of its capabilities, and validation within this scenario should be demonstrated in the paper. This is the most fundamental limitation at the paper's current state.

Response: Thank you for your insightful suggestion; we truly appreciate it. We recognize that the 'identity' problem requires further studies to develop appropriate methods. Our current approach does not fully address this issue, as it may detect asymmetric non-sinusoidal oscillations with multiple harmonic peaks, without accounting for different shapes of nonsinusoidal oscillations.

The main reason we could not fully address the “identity” problem results from the general absence of a defined ground truth, i.e., data for which we know the harmonic structure. To overcome this barrier, we would need datasets from well-characterized cognitive tasks or neural disorders.  For example, Cole et al. 2017 showed that the harmonic structure of beta oscillations can explain the degree of Parkinson’s disease, and Hu et al. 2023 showed that the number of harmonic peaks can localize the seizure onset zone. Future studies could use the data from these two studies to study whether CHO can distinguish different harmonic structures of pathological neural oscillations.

In this paper, we showed the basic identity of neural oscillations, encompassing elements such as the fundamental frequency and onset/offset. Your valuable insights contribute significantly to our ongoing efforts, and we appreciate your thoughtful consideration of these aspects. In response, we added a new paragraph in the Limitation of the discussion section as below:

“Another limitation of this study is that it does not assess the harmonic structure of neural oscillations. Thus, CHO cannot distinguish between oscillations that have the same fundamental frequency but differ in their non-sinusoidal properties.  This limitation stems from the objective of this study, which is to identify the fundamental frequency of non-sinusoidal neural oscillations.  Overcoming this limitation requires further studies to improve CHO to distinguish between different non-sinusoidal properties of pathological neural oscillations.  The data that is necessary for these further studies could be obtained from the wide range of studies that have linked the harmonic structures in the neural oscillations to various cognitive functions (van Dijk et al., 2010; Schalk, 2015; Mazaheri and Jensen, 2008) and neural disorders (Cole et al., 2017; Jackson et al., 2019; Hu et al., 2023). For example, Cole et al. 2017 showed that a harmonic structure of beta oscillations can explain the degree of Parkinson’s disease, and Hu et al. 2023 showed the number of harmonic peaks can localize the seizure onset zone. “

References:

Beck AM, He M, Gutierrez R, Purdon PL. An iterative search algorithm to identify oscillatory dynamics in neurophysiological time series. bioRxiv. 2022. p. 2022.10.30.514422.

doi:10.1101/2022.10.30.514422

Brady B, Bardouille T. Periodic/Aperiodic parameterization of transient oscillations (PAPTO)Implications for healthy ageing. Neuroimage. 2022;251: 118974.

Fabus MS, Woolrich MW, Warnaby CW, Quinn AJ. Understanding Harmonic Structures Through Instantaneous Frequency. IEEE Open J Signal Process. 2022;3: 320-334.

Jones SR, Pritchett DL, Sikora MA, Stufflebeam SM, Hämäläinen M, Moore CI. Quantitative analysis and biophysically realistic neural modeling of the MEG mu rhythm: rhythmogenesis and modulation of sensory-evoked responses. J Neurophysiol. 2009;102: 3554-3572.

He M, Das P, Hotan G, Purdon PL. Switching state-space modeling of neural signal dynamics. PLoS Comput Biol. 2023;19: e1011395.

Matsuda T, Komaki F. Time Series Decomposition into Oscillation Components and Phase Estimation. Neural Comput. 2017;29: 332-367.

Quinn AJ, Lopes-Dos-Santos V, Huang N, Liang W-K, Juan C-H, Yeh J-R, et al. Within-cycle instantaneous frequency profiles report oscillatory waveform dynamics. J Neurophysiol. 2021;126: 1190-1208.

Reviewer #2 (Public Review):

Summary:

A new toolbox is presented that builds on previous toolboxes to distinguish between real and spurious oscillatory activity, which can be induced by non-sinusoidal waveshapes. Whilst there are many toolboxes that help to distinguish between 1/f noise and oscillations, not many tools are available that help to distinguish true oscillatory activity from spurious oscillatory activity induced in harmonics of the fundamental frequency by non-sinusoidal waveshapes. The authors present a new algorithm which is based on autocorrelation to separate real from spurious oscillatory activity. The algorithm is extensively validated using synthetic (simulated) data, and various empirical datasets from EEG, intracranial EEG in various locations and domains (i.e. auditory cortex, hippocampus, etc.).

Strengths:

Distinguishing real from spurious oscillatory activity due to non-sinusoidal waveshapes is an issue that has plagued the field for quite a long time. The presented toolbox addresses this fundamental problem which will be of great use for the community. The paper is written in a very accessible and clear way so that readers less familiar with the intricacies of Fourier transform and signal processing will also be able to follow it. A particular strength is the broad validation of the toolbox, using synthetic, scalp EEG, EcoG, and stereotactic EEG in various locations and paradigms.

Weaknesses:

At many parts in the results section critical statistical comparisons are missing (e.g. FOOOF vs CHO). Another weakness concerns the methods part which only superficially describes the algorithm. Finally, a weakness is that the algorithm seems to be quite conservative in identifying oscillatory activity which may render it only useful for analysing very strong oscillatory signals (i.e.

alpha), but less suitable for weaker oscillatory signals (i.e. gamma).

Response: We thank Reviewer #2 for the assistance in improving this manuscript.  In the revised manuscript, we have added the missing statistical comparisons, detailed pseudo code, and a subsection that explains the hyper-parameters of CHO.  We also recognize the limitations of CHO in detecting gamma oscillations.  While our results demonstrate beta-band oscillations in ECoG and EEG signals (see Figures 5 and 6), we had no expectation to find gamma-band oscillations during a simple reaction time task.  This is because of the general absence of ECoG electrodes over the occipital cortex, where such gamma-band oscillations may be found. 

Nevertheless, our CHO method should be able to detect gamma-band oscillations.  This is because if there are gamma-band oscillations, they will be reflected as a bump over the 1/f fit in the power spectrum, and CHO will detect them.  We apologize for not specifying the frequency range of the synthetic non-sinusoidal oscillations.  The gamma band was also included in our simulation. We added the frequency range (1-40 Hz) of the synthetic nonsinusoidal oscillations in the subsection, the caption of Figure 4, and the result section.

Reviewer #1 (Recommendations For The Authors):

(1) The example of a sinusoidal neural oscillation in Fig 1 seems to still exhibit a great deal of nonsinusoidal behavior. Although it is largely symmetrical, it has significant peak-trough symmetry as well as sharper peak structure than typical sinusoidal activity. Nevertheless, it has less harmonic structure than the example on the left. A more precisely-stated claim might be that non-sinusoidal behavior is not the distinguishing characteristic between the two, but rather the degree of harmonic structure.

Response: We are grateful for this thoughtful observation. In response, we now recognize that the depicted example showcases pronounced peak-trough symmetry and sharpness, characteristics that might not be typically associated with sinusoidal behavior. We now better understand that the key differentiator between the examples lies not only in their nonsinusoidal behavior but also in their harmonic structure. To reflect this better understanding, we have refined our manuscript to more accurately articulate the differences in harmonic structure, in accordance with your suggestion. Specifically, we revised the caption of Fig 1 in the manuscript as follows:

The caption of the Fig 1G-L.

“We applied the same statistical test to a more sinusoidal neural oscillation (G). Since this neural oscillation more closely resembles a sinusoidal shape, it does not exhibit any prominent harmonic peaks in the alpha and beta bands within the power spectrum (H) and time-frequency domain (I).  Consequently, our test found that the phase of the theta-band and beta-band oscillations were not phase-locked (J-L).  Thus, this statistical test suggests the absence of a harmonic structure.”

(2) The statement "This suggests that most of the beta oscillations

detected by conventional methods are simply harmonics of the predominant asymmetric alpha oscillation." is potentially overstated. It is important to constrain this statement to the auditory cortex in which the authors conduct the validation, because true beta still exists elsewhere. The same goes for the beta-gamma claim later on. In general, use of "may be" is also more advisable than the definitive "are".

Response: We thank the reviewer for this thoughtful feedback. To avoid the potential overstatement of our findings we revised our statement on beta oscillations in the manuscript as follows:

Discussion:

“This suggests that most of the beta oscillations detected by conventional methods within auditory cortex may be simply harmonics of the predominant asymmetric alpha oscillation.”

Reviewer #2 (Recommendations For The Authors):

All my concerns are medium to minor and I list them as they appear in the manuscript. I do not suggest new experiments or a change in the results, instead I focus on writing issues only.

a) Line 50: A reference to the seminal paper by Klimesch et al (2007) on alpha oscillations and inhibition would seem appropriate here.

Response: We added the reference to Klimesch et al. (2007).

b) Figure 4: It is unclear which length for the simulated oscillations was used to generate the data in panels B-G.

Response: We generated oscillations that were 2.5 cycles in length and 1-3 seconds in duration. We added this information to the manuscript as follows.

Figure 4:

“We evaluated CHO by verifying its specificity, sensitivity, and accuracy in detecting the fundamental frequency of non-sinusoidal oscillatory bursts (2.5 cycles, 1–3 seconds long) convolved with 1/f noise.”

Results (page 5, lines 163-165):

“To determine the specificity and sensitivity of CHO in detecting neural oscillations, we applied CHO to synthetic non-sinusoidal oscillatory bursts (2.5 cycles, 1–3 seconds long) convolved with 1/f noise, also known as pink noise, which has a power spectral density that is inversely proportional to the frequency of the signal.”

Methods (page 20, lines 623-626):

“While empirical physiological signals are most appropriate for validating our method, they generally lack the necessary ground truth to characterize neural oscillation with sinusoidal or non-sinusoidal properties. To overcome this limitation, we first validated CHO on synthetic nonsinusoidal oscillatory bursts (2.5 cycles, 1–3 seconds long) convolved with 1/f noise to test the performance of the proposed method.”

c) Figure 5 - supplements: Would be good to re-organize the arrangement of the plots on these figures to facilitate the comparison between Foof and CHO (i.e. by presenting for each participant FOOOF and CHO together).

Response: We combined Figure 5-supplementary figures 1 and 2 into Figure 5-supplementary figure 1, Figure 6-supplementary figures 1 and 2 into Figure 6-supplementary figure 1, and Figure 8-supplementary figures 1 and 2 into Figure 8-supplementary figure 1. 

Author response image 1.

Figure 5-supplementary figure 1:

Author response image 2.

Figure 6-supplementary figure 1:

Author response image 3.

Figure 8-supplementary figure 1:

d) Statistics: Almost throughout the results section where the empirical results are described statistical comparisons are missing. For instance, in lines 212-213 the statement that CHO did not detect low gamma while FOOOF did is not backed up by the appropriate statistics. This issue is also evident in all of the following sections (i.e. EEG results, On-offsets of oscillations, SEEG results, Frequency and duration of oscillations). I feel this is probably the most important point that needs to be addressed.

Response: We added statistical comparisons to Figure 5 (ECoG), 6 (EEG), and the results section as follows.

Author response image 4.

Validation of CHO in detecting oscillations in ECoG signals. A. We applied CHO and FOOOF to determine the fundamental frequency of oscillations from ECoG signals recorded during the pre-stimulus period of an auditory reaction time task. FOOOF detected oscillations primarily in the alpha- and beta-band over STG and pre-motor area.  In contrast, CHO also detected alpha-band oscillations primarily within STG, and more focal beta-band oscillations over the pre-motor area, but not STG. B. We investigated the occurrence of each oscillation within defined cerebral regions across eight ECoG subjects. The horizontal bars and horizontal lines represent the median and median absolute deviation (MAD) of oscillations occurring across the eight subjects. An asterisk (*) indicates statistically significant differences in oscillation detection between CHO and FOOOF (Wilcoxon rank-sum test, p<0.05 after Bonferroni correction).”

Author response image 5.

Validation of CHO in detecting oscillations in EEG signals. A. We applied CHO and FOOOF to determine the fundamental frequency of oscillations from EEG signals recorded during the pre-stimulus period of an auditory reaction time task.  FOOOF primarily detected alpha-band oscillations over frontal/visual areas and beta-band oscillations across all areas (with a focus on central areas). In contrast, CHO detected alpha-band oscillations primarily within visual areas and detected more focal beta-band oscillations over the pre-motor area, similar to the ECoG results shown in Figure 5. B. We investigated the occurrence of each oscillation within the EEG signals across seven subjects. An asterisk (*) indicates statistically significant differences in oscillation detection between CHO and FOOOF (Wilcoxon rank-sum test, p<0.05 after Bonferroni correction). CHO exhibited lower entropy values of alpha and beta occurrence than FOOOF across 64 channels. C. We compared the performance of FOOO and CHO in detecting oscillation across visual and pre-motor-related EEG channels. CHO detected more alpha and beta oscillations in visual cortex than in pre-motor cortex. FOOOF detected alpha and beta oscillations in visual cortex than in pre-motor cortex.

We added additional explanations of our statistical results to the “Electrocorticographic (ECoG) results” and “Electroencephalographic (EEG) results” sections.

“We compared neural oscillation detection rates between CHO and FOOOF across eight ECoG subjects.  We used FreeSurfer to determine the associated cerebral region for each ECoG location. Each subject performed approximately 400 trials of a simple auditory reaction-time task.  We analyzed the neural oscillations during the 1.5-second-long pre-stimulus period within each trial. CHO and FOOOF demonstrated statistically comparable results in the theta and alpha bands despite CHO exhibiting smaller median occurrence rates than FOOOF across eight subjects. Notably, within the beta band, excluding specific regions such as precentral, pars opercularis, and caudal middle frontal areas, CHO's beta oscillation detection rate was significantly lower than that of FOOOF (Wilcoxon rank-sum test, p < 0.05 after Bonferroni correction). This suggests comparable detection rates between CHO and FOOOF in premotor and Broca's areas, while the detection of beta oscillations by FOOOF in other regions, such as the temporal area, may represent harmonics of theta or alpha, as illustrated in Figure 5A and B. Furthermore, FOOOF exhibited a higher sensitivity in detecting delta, theta, and low gamma oscillations overall, although both CHO and FOOOF detected only a limited number of oscillations in these frequency bands.”

“We assessed the difference in neural oscillation detection performance between CHO and FOOOF across seven EEG subjects.  We used EEG electrode locations according to the 10-10 electrode system and assigned each electrode to the appropriate underlying cortex (e.g., O1 and O2 for the visual cortex). Each subject performed 200 trials of a simple auditory reaction-time task.  We analyzed the neural oscillations during the 1.5-second-long pre-stimulus period. In the alpha band, CHO and FOOOF presented statistically comparable outcomes. However, CHO exhibited a greater alpha detection rate for the visual cortex than for the pre-motor cortex, as shown in Figures 6B and C. The entropy of CHO's alpha oscillation occurrences (3.82) was lower than that of FOOOF (4.15), with a maximal entropy across 64 electrodes of 4.16. Furthermore, in the beta band, CHO's entropy (4.05) was smaller than that of FOOOF (4.15). These findings suggest that CHO may offer a more region-specific oscillation detection than FOOOF.

As illustrated in Figure 6C, CHO found fewer alpha oscillations in pre-motor cortex (FC2 and FC4) than in occipital cortex (O1 and O2), while FOOOF found more beta oscillations occurrences in pre-motor cortex (FC2 and FC4) than in occipital cortex. However, FOOOF found more alpha and beta oscillations in visual cortex than in pre-motor cortex.

Consistent with ECoG results, FOOOF demonstrated heightened sensitivity in detecting delta, theta, and low gamma oscillations. 

Nonetheless, both CHO and FOOOF identified only a limited number of oscillations in delta and theta frequency bands.

Contrary to the ECoG results, FOOOF found more low gamma oscillations in EEG subjects than in ECoG subjects.”

e) Line 248: The authors find an oscillatory signal in the hippocampus with a frequency at around 8 Hz, which they refer to as alpha. However, several researchers (including myself) may label this fast theta, according to the previous work showing the presence of fast and slow theta oscillations in the human hippocampus (https://pubmed.ncbi.nlm.nih.gov/21538660/, https://pubmed.ncbi.nlm.nih.gov/32424312/).

Response: We replaced “alpha” with “fast theta” in the figure and text. We added a citation for Lega et al. 2012.

f) Line 332: It could also be possible that the auditory alpha rhythms don’t show up in the EEG because a referencing method was used that was not ideal for picking it up. In general, re-referencing is an important preprocessing step that can make the EEG be more susceptible to deep or superficial sources and that should be taken into account when interpreting the data.

Response: We re-referenced our signals using a common median reference (see Methods section). After close inspection of our results, we found that the EEG topography shown in Figure 6 did not show the auditory alpha oscillation because the alpha power of visual locations greatly exceeded that of those locations that reflect oscillations in the auditory cortex. Further, while our statistical analysis shows that CHO detected auditory alpha oscillations, this analysis also shows that CHO detected significantly more visual alpha oscillations.

g) Line 463: It seems that the major limitation of the algorithm lies in its low sensitivity which is discussed by the authors. The authors seem to downplay this a bit by saying that the algorithm works just fine at SNRs that are comparable to alpha oscillations. However, alpha is the strongest single in human EEG which may make the algorithm less suitable for picking up less prominent oscillatory signals, i.e. gamma, theta, ripples, etc. Is CHO only seeing the ‘tip of the iceberg’?

Response:  We performed the suggested analysis. For the theta band, this analysis generated convincing statistical results for ECoG signals (Figures 5, 6, and the results section). For theta oscillation detection, we found no statistical difference between CHO and FOOOF.  Since FOOOF has a high sensitivity even under SNRs (as shown in our simulation), our analysis suggests that CHO and FOOOF should perform equally well in the detection of theta oscillation, even when the theta oscillation amplitude is small.

To validate the ability of CHO to detect oscillations in high-frequency bands (> 40Hz), such as gamma oscillations and ripples, our follow-up study is applying CHO in the detection of highfrequency oscillations (HFOs) in electrocorticographic signals recorded during seizures.  To this end, our follow-up study analyzed 26 seizures from six patients.  In this analysis, CHO showed similar sensitivity and specificity as the epileptogenicity index (EI), which is the most commonly used method to detect seizure onset times and zones. The results of this follow-up study were presented at the American Epilepsy Society Meeting in December of 2023, and we are currently preparing a manuscript for submission to a peer-reviewed journal. 

In this study, we want to investigate the performance of CHO in detecting the most prominent neural oscillations (e.g., alpha and beta). Future studies will investigate the performance of  CHO in detecting more difficult to observe oscillations (delta in sleep stages, theta in the hippocampus during memory tasks, and high-frequency oscillation or ripples in seizure or interictal data. 

h) Methods: The methods section, especially the one describing the CHO algorithm, is lacking a lot of detail that one usually would like to see in order to rebuild the algorithm themselves. I appreciate that the code is available freely, but that does not, in my opinion, relief the authors of their duty to describe in detail how the algorithm works. This should be fixed before publishing.

Response: We now present pseudo code to describe the algorithms within the new subsection on the hyper-parameterization of CHO.

See Author response table 1.

A new subsection titled “Tradeoffs in adjusting the hyper-parameters that govern the detection in CHO.”

“The ability of CHO to detect neural oscillations and determine their fundamental frequency is governed by four principal hyper-parameters.  Adjusting these parameters requires understanding their effect on the sensitivity and specificity in the detection of neural oscillations. 

The first hyper-parameter is the number of time windows (N in Line 5 in Algorithm 1), that is used to estimate the 1/f noise.  In our performance assessment of CHO, we used four time windows, resulting in estimation periods of 250 ms in duration for each 1/f spectrum.  A higher number of time windows results in smaller estimation periods and thus minimizes the likelihood of observing multiple neural oscillations within this time window, which otherwise could confound the 1/f estimation.  However, a higher number of time windows and, thus, smaller time estimation periods may lead to unstable 1/f estimates. 

The second hyper-parameter defines the minimum number of cycles of a neural oscillation to be detected by CHO (see Line 23 in Algorithm 1).  In our study, we specified this parameter to be two cycles.  Increasing the number of cycles increases specificity, as it will reject spurious oscillations.  However, increasing the number also sensitivity as it will reject short oscillations.

The third hyper-parameter is the significance threshold that selects positive peaks within the auto-correlation of the signal.  The magnitude of the peaks in the auto-correlation indicates the periodicity of the oscillations (see Line 26 in Algorithm 1).  Referred to as "NumSTD," this parameter denotes the number of standard errors that a positive peak has to exceed to be selected to be a true oscillation.  For this study, we set the "NumSTD" value to 1 (the approximate 68% confidence bounds).  Increasing the "NumSTD" value increases specificity in the detection as it reduces the detection of spurious peaks in the auto-correlation.  However, increasing the "NumSTD" value also decreases the sensitivity in the detection of neural oscillations with varying instantaneous oscillatory frequencies. 

The fourth hyper-parameter is the percentage of overlap between two bounding boxes that trigger their merger (see Line 31 in Algorithm 1).  In our study, we set this parameter to 75% overlap.  Increasing this threshold yields more fragmentation in the detection of oscillations, while decreasing this threshold may reduce the accuracy in determining the onset and offset of neural oscillations.”

Author Response

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

Recommendations

Recommendation #1: Address potential confounds in the experimental design:

(1a) Confounding factors between baseline to early learning. While the visual display of the curved line remains constant, there are at least three changes between these two phases: 1) the presence of reward feedback (the focus of the paper); 2) a perturbation introduced to draw a hidden, mirror-symmetric curved line; 3) instructions provided to use reward feedback to trace the line on the screen (intentionally deceitful). As such, it remains unclear which of these factors are driving the changes in both behavior and bold signals between the two phases. The absence of a veridical feedback phase in which participants received reward feedback associated with the shown trajectory seems like a major limitation.

(1b) Confounding Factors Between Early and Late Learning. While the authors have focused on interpreting changes from early to late due to the explore-exploit trade-off, there are three additional factors possibly at play: 1) increasing fatigue, 2) withdrawal of attention, specifically related to individuals who have either successfully learned the perturbation within the first few trials or those who have simply given up, or 3) increasing awareness of the perturbation (not clear if subjective reports about perturbation awareness were measured.). I understand that fMRI research is resource-intensive; however, it is not clear how to rule out these alternatives with their existing data without additional control groups. [Another reviewer added the following: Why did the authors not acquire data during a control condition? How can we be confident that the neural dynamics observed are not due to the simple passage of time? Or if these effects are due to the task, what drives them? The reward component, the movement execution, increased automaticity?]

We have opted to address both of these points above within a single reply, as together they suggest potential confounding factors across the three phases of the task. We would agree that, if the results of our pairwise comparisons (e.g., Early > Baseline or Late > Early) were considered in isolation from one another, then these critiques of the study would be problematic. However, when considering the pattern of effects across the three task phases, we believe most of these critiques can be dismissed. Below, we first describe our results in this context, and then discuss how they address the reviewers’ various critiques.

Recall that from Baseline to Early learning, we observe an expansion of several cortical areas (e.g., core regions in the DMN) along the manifold (red areas in Fig. 4A, see manifold shifts in Fig. 4C) that subsequently exhibit contraction during Early to Late learning (blue areas in Fig. 4B, see manifold shifts in Fig. 4D). We show this overlap in brain areas in Author response image 1 below, panel A. Notably, several of these brain areas appear to contract back to their original, Baseline locations along the manifold during Late learning (compare Fig. 4C and D). This is evidenced by the fact that many of these same regions (e.g., DMN regions, in Author response image 1 panel A below) fail to show a significant difference between the Baseline and Late learning epochs (see Author response image 1 panel B below, which is taken from supplementary Fig 6). That is, the regions that show significant expansion and subsequent contraction (in Author response image 1 panel A below) tend not to overlap with the regions that significantly changed over the time course of the task (in Author response image 1 panel B below).

Author response image 1.

Note that this basic observation above is not only true of our regional manifold eccentricity data, but also in the underlying functional connectivity data associated with individual brain regions. To make this second point clearer, we have modified and annotated our Fig. 5 and included it below. Note the reversal in seed-based functional connectivity from Baseline to Early learning (leftmost brain plots) compared to Early to Late learning (rightmost brain plots). That is, it is generally the case that for each seed-region (A-C) the areas that increase in seed-connectivity with the seed region (in red; leftmost plot) are also the areas that decrease in seed-connectivity with the seed region (in blue; rightmost plot), and vice versa. [Also note that these connectivity reversals are conveyed through the eccentricity data — the horizontal red line in the rightmost plots denote the mean eccentricity of these brain regions during the Baseline phase, helping to highlight the fact that the eccentricity of the Late learning phase reverses back towards this Baseline level].

Author response image 2.

Critically, these reversals in brain connectivity noted above directly counter several of the critiques noted by the reviewers. For instance, this reversal pattern of effects argues against the idea that our results during Early Learning can be simply explained due to the (i) presence of reward feedback, (ii) presence of the perturbation or (iii) instructions to use reward feedback to trace the path on the screen. Indeed, all of these factors are also present during Late learning, and yet many of the patterns of brain activity during this time period revert back to the Baseline patterns of connectivity, where these factors are absent. Similarly, this reversal pattern strongly refutes the idea that the effects are simply due to the passage of time, increasing fatigue, or general awareness of the perturbation. Indeed, if any of these factors alone could explain the data, then we would have expected a gradual increase (or decrease) in eccentricity and connectivity from Baseline to Early to Late learning, which we do not observe. We believe these are all important points when interpreting the data, but which we failed to mention in our original manuscript when discussing our findings.

We have now rectified this in the revised paper, where we now write in our Discussion:

“Finally, it is important to note that the reversal pattern of effects noted above suggests that our findings during learning cannot be simply attributed to the introduction of reward feedback and/or the perturbation during Early learning, as both of these task-related features are also present during Late learning. In addition, these results cannot be simply explained due to the passage of time or increasing subject fatigue, as this would predict a consistent directional change in eccentricity across the Baseline, Early and Late learning epochs.”

However, having said the above, we acknowledge that one potential factor that our findings cannot exclude is that they are (at least partially) attributable to changes in subjects’ state of attention throughout the task. Indeed, one can certainly argue that Baseline trials in our study don’t require a great deal of attention (after all, subjects are simply tracing a curved path presented on the screen). Likewise, for subjects that have learned the hidden shape, the Late learning trials are also likely to require limited attentional resources (indeed, many subjects at this point are simply producing the same shape trial after trial). Consequently, the large shift in brain connectivity that we observe from Baseline to Early Learning, and the subsequent reversion back to Baseline-levels of connectivity during Late learning, could actually reflect a heightened allocation of attention as subjects are attempting to learn the (hidden) rewarded shape. However, we do not believe that this would reflect a ‘confound’ of our study per se — indeed, any subject who has participated in a motor learning study would agree that the early learning phase of a task is far more cognitively demanding than Baseline trials and Late learning trials. As such, it is difficult to disentangle this ‘attention’ factor from the learning process itself (and in fact, it is likely central to it).

Of course, one could have designed a ‘control’ task in which subjects must direct their attention to something other than the learning task itself (e.g., divided attention paradigm, e.g., Taylor & Thoroughman, 2007, 2008, and/or perform a secondary task concurrently (Codol et al., 2018; Holland et al., 2018), but we know that this type of manipulation impairs the learning process itself. Thus, in such a case, it wouldn’t be obvious to the experimenter what they are actually measuring in brain activity during such a task. And, to extend this argument even further, it is true that any sort of brain-based modulation can be argued to reflect some ‘attentional’ process, rather than modulations related to the specific task-based process under consideration (in our case, motor learning). In this regard, we are sympathetic to the views of Richard Andersen and colleagues who have eloquently stated that “The study of how attention interacts with other neural processing systems is a most important endeavor. However, we think that over-generalizing attention to encompass a large variety of different neural processes weakens the concept and undercuts the ability to develop a robust understanding of other cognitive functions.” (Andersen & Cui, 2007, Neuron). In short, it appears that different fields/researchers have alternate views on the usefulness of attention as an explanatory construct (see also articles from Hommel et al., 2019, “No one knows what attention is”, and Wu, 2023, “We know what attention is!”), and we personally don’t have a dog in this fight. We only highlight these issues to draw attention (no pun intended) that it is not trivial to separate these different neural processes during a motor learning study.

Nevertheless, we do believe these are important points worth flagging for the reader in our paper, as they might have similar questions. To this end, we have now included in our Discussion section the following text:

“It is also possible that some of these task-related shifts in connectivity relate to shifts in task-general processes, such as changes in the allocation of attentional resources (Bédard and Song, 2013; Rosenberg et al., 2016) or overall cognitive engagement (Aben et al., 2020), which themselves play critical roles in shaping learning (Codol et al., 2018; Holland et al., 2018; Song, 2019; Taylor and Thoroughman, 2008, 2007; for a review of these topics, see Tsay et al., 2023). Such processes are particularly important during the earlier phases of learning when sensorimotor contingencies need to be established. While these remain questions for future work, our data nevertheless suggest that this shift in connectivity may be enabled through the PMC.”

Finally, we should note that, at the end of testing, we did not assess participants' awareness of the manipulation (i.e., that they were, in fact, being rewarded based on a mirror image path). In hindsight, this would have been a good idea and provided some value to the current project. Nevertheless, it seems clear that, based on several of the learning profiles observed (e.g., subjects who exhibited very rapid learning during the Early Learning phase, more on this below), that many individuals became aware of a shape approximating the rewarded path. Note that we have included new figures (see our responses below) that give a better example of what fast versus slower learning looks like. In addition, we now note in our Methods that we did not probe participants about their subjective awareness re: the perturbation:

“Note that, at the end of testing, we did not assess participants’ awareness of the manipulation (i.e., that they were, in fact, being rewarded based on a mirror image path of the visible path).”

Recommendation #2: Provide more behavioral quantification.

(2a) The authors chose to only plot the average learning score in Figure 1D, without an indication of movement variability. I think this is quite important, to give the reader an impression of how variable the movements were at baseline, during early learning, and over the course of learning. There is evidence that baseline variability influences the 'detectability' of imposed rotations (in the case of adaptation learning), which could be relevant here. Shading the plots by movement variability would also be important to see if there was some refinement of the moment after participants performed at the ceiling (which seems to be the case ~ after trial 150). This is especially worrying given that in Fig 6A there is a clear indication that there is a large difference between subjects' solutions on the task. One subject exhibits almost a one-shot learning curve (reaching a score of 75 after one or two trials), whereas others don't seem to really learn until the near end. What does this between-subject variability mean for the authors' hypothesized neural processes?

In line with these recommendations, we have now provided much better behavioral quantification of subject-level performance in both the main manuscript and supplementary material. For instance, in a new supplemental Figure 1 (shown below), we now include mean subject (+/- SE) reaction times (RTs), movement times (MTs) and movement path variability (our computing of these measures are now defined in our Methods section).

As can be seen in the figure, all three of these variables tended to decrease over the course of the study, though we note there was a noticeable uptick in both RTs and MTs from the Baseline to Early learning phase, once subjects started receiving trial-by-trial reward feedback based on their movements. With respect to path variability, it is not obvious that there was a significant refinement of the paths created during late learning (panel D below), though there was certainly a general trend for path variability to decrease over learning.

Author response image 3.

Behavioral measures of learning across the task. (A-D) shows average participant reward scores (A), reaction times (B), movement times (C) and path variability (D) over the course of the task. In each plot, the black line denotes the mean across participants and the gray banding denotes +/- 1 SEM. The three equal-length task epochs for subsequent neural analyses are indicated by the gray shaded boxes.

In addition to these above results, we have also created a new Figure 6 in the main manuscript, which now solely focuses on individual differences in subject learning (see below). Hopefully, this figure clarifies key features of the task and its reward structure, and also depicts (in movement trajectory space) what fast versus slow learning looks like in the task. Specifically, we believe that this figure now clearly delineates for the reader the mapping between movement trajectory and the reward score feedback presented to participants, which appeared to be a source of confusion based on the reviewers’ comments below. As can be clearly observed in this figure, trajectories that approximated the ‘visible path’ (black line) resulted in fairly mediocre scores (see score color legend at right), whereas trajectories that approximated the ‘reward path’ (dashed black line, see trials 191-200 of the fast learner) resulted in fairly high scores. This figure also more clearly delineates how fPCA loadings derived from our functional data analysis were used to derive subject-level learning scores (panel C).

Author response image 4.

Individual differences in subject learning performance. (A) Examples of a good learner (bordered in green) and poor learner (bordered in red). (B) Individual subject learning curves for the task. Solid black line denotes the mean across all subjects whereas light gray lines denote individual participants. The green and red traces denote the learning curves for the example good and poor learners denoted in A. (C) Derivation of subject learning scores. We performed functional principal component analysis (fPCA) on subjects’ learning curves in order to identify the dominant patterns of variability during learning. The top component, which encodes overall learning, explained the majority of the observed variance (~75%). The green and red bands denote the effect of positive and negative component scores, respectively, relative to mean performance. Thus, subjects who learned more quickly than average have a higher loading (in green) on this ‘Learning score’ component than subjects who learned more slowly (in red) than average. The plot at right denotes the loading for each participant (open circles) onto this Learning score component.

The reviewers note that there are large individual differences in learning performance across the task. This was clearly our hope when designing the reward structure of this task, as it would allow us to further investigate the neural correlates of these individual differences (indeed, during pilot testing, we sought out a reward structure to the task that would allow for these intersubject differences). The subjects who learn early during the task end up having higher fPCA scores than the subjects who learn more gradually (or learn the task late). From our perspective, these differences are a feature, and not a bug, and they do not negate any of our original interpretations. That is, subjects who learn earlier on average tend to contract their DAN-A network during the early learning phase whereas subjects who learn more slowly on average (or learn late) instead tend to contract their DAN-A network during late learning (Fig. 7).

(2b) In the methods, the authors stated that they scaled the score such that even a perfectly traced visible path would always result in an imperfect score of 40 patients. What happens if a subject scores perfectly on the first try (which seemed to have happened for the green highlighted subject in Fig 6A), but is then permanently confronted with a score of 40 or below? Wouldn't this result in an error-clamp-like (error-based motor adaptation) design for this subject and all other high performers, which would vastly differ from the task demands for the other subjects? How did the authors factor in the wide between-subject variability?

We think the reviewers may have misinterpreted the reward structure of the task, and we apologize for not being clearer in our descriptions. The reward score that subjects received after each trial was based on how well they traced the mirror-image of the visible path. However, all the participant can see on the screen is the visible path. We hope that our inclusion of the new Figure 6 (shown above) makes the reward structure of the task, and its relationship to movement trajectories, much clearer. We should also note that, even for the highest performing subject (denoted in Fig. 6), it still required approximately 20 trials for them to reach asymptote performance.

(2c) The study would benefit from a more detailed description of participants' behavioral performance during the task. Specifically, it is crucial to understand how participants' motor skills evolve over time. Information on changes in movement speed, accuracy, and other relevant behavioral metrics would enhance the understanding of the relationship between behavior and brain activity during the learning process. Additionally, please clarify whether the display on the screen was presented continuously throughout the entire trial or only during active movement periods. Differences in display duration could potentially impact the observed differences in brain activity during learning.

We hope that with our inclusion of the new Supplementary Figure 1 (shown above) this addresses the reviewers’ recommendation. Generally, we find that RTs, MTs and path variability all decrease over the course of the task. We think this relates to the early learning phase being more attentionally demanding and requiring more conscious effort, than the later learning phases.

Also, yes, the visible path was displayed on the screen continuously throughout the trial, and only disappeared at the 4.5 second mark of each trial (when the screen was blanked and the data was saved off for 1.5 seconds prior to commencement of the next trial; 6 seconds total per trial). Thus, there were no differences in display duration across trials and phases of the task. We have now clarified this in the Methods section, where we now write the following:

“When the cursor reached the target distance, the target changed color from red to green to indicate that the trial was completed. Importantly, other than this color change in the distance marker, the visible curved path remained constant and participants never received any feedback about the position of their cursor.”

(2d) It is unclear from plots 6A, 6B, and 1D how the scale of the behavioral data matches with the scaling of the scores. Are these the 'real' scores, meaning 100 on the y-axis would be equivalent to 40 in the task? Why then do all subjects reach an asymptote at 75? Or is 75 equivalent to 40 and the axis labels are wrong?

As indicated above, we clearly did a poor job of describing the reward structure of our task in our original paper, and we now hope that our inclusion of Figure 6 makes things clear. A ‘40’ score on the y-axis would indicate that a subject has perfectly traced the visible path whereas a perfect ‘100’ score would indicate that a subject has perfectly traced the (hidden) mirror image path.

The fact that several of the subjects reach asymptote around 75 is likely a byproduct of two factors. Firstly, the subjects performed their movements in the absence of any visual error feedback (they could not see the position of a cursor that represented their hand position), which had the effect of increasing motor variability in their actions from trial to trial. Secondly, there appears to be an underestimation among subjects regarding the curvature of the concealed, mirror-image path (i.e., that the rewarded path actually had an equal but opposite curvature to that of the visible path). This is particularly evident in the case of the top-performing subject (illustrated in Figure 6A) who, even during late learning, failed to produce a completely arched movement.

(2e) Labeling of Contrasts: There is a consistent issue with the labeling of contrasts in the presented figures, causing confusion. While the text refers to the difference as "baseline to early learning," the label used in figures, such as Figure 4, reads "baseline > early." It is essential to clarify whether the presented contrast is indeed "baseline > early" or "early > baseline" to avoid any misinterpretation.

We thank the reviewers for catching this error. Indeed, the intended label was Early > Baseline, and this has now been corrected throughout.

Recommendation #3. Clarify which motor learning mechanism(s) are at play.

(3a) Participants were performing at a relatively low level, achieving around 50-60 points by the end of learning. This outcome may not be that surprising, given that reward-based learning might have a substantial explicit component and may also heavily depend on reasoning processes, beyond reinforcement learning or contextual recall (Holland et al., 2018; Tsay et al., 2023). Even within our own data, where explicit processes are isolated, average performance is low and many individuals fail to learn (Brudner et al., 2016; Tsay et al., 2022). Given this, many participants in the current study may have simply given up. A potential indicator of giving up could be a subset of participants moving straight ahead in a rote manner (a heuristic to gain moderate points). Consequently, alterations in brain networks may not reflect exploration and exploitation strategies but instead indicate levels of engagement and disengagement. Could the authors plot the average trajectory and the average curvature changes throughout learning? Are individuals indeed defaulting to moving straight ahead in learning, corresponding to an average of 50-60 points? If so, the interpretation of brain activity may need to be tempered.

We can do one better, and actually give you a sense of the learning trajectories for every subject over time. In the figure below, which we now include as Supplementary Figure 2 in our revision, we have plotted, for each subject, a subset of their movement trajectories across learning trials (every 10 trials). As can be seen in the diversity of these trajectories, the average trajectory and average curvature would do a fairly poor job of describing the pattern of learning-related changes across subjects. Moreover, it is not obvious from looking at these plots the extent to which poor learning subjects (i.e., subjects who never converge on the reward path) actually ‘give up’ in the task — rather, many of these subjects still show some modulation (albeit minor) of their movement trajectories in the later trials (see the purple and pink traces). As an aside, we are also not entirely convinced that straight ahead movements, which we don’t find many of in our dataset, can be taken as direct evidence that the subject has given up.

Author response image 5

Variability in learning across subjects. Plots show representative trajectory data from each subject (n=36) over the course of the 200 learning trials. Coloured traces show individual trials over time (each trace is separated by ten trials, e.g., trial 1, 10, 20, 30, etc.) to give a sense of the trajectory changes throughout the task (20 trials in total are shown for each subject).

We should also note that we are not entirely opposed to the idea of describing aspects of our findings in terms of subject engagement versus disengagement over time, as such processes are related at some level to exploration (i.e., cognitive engagement in finding the best solution) and exploitation (i.e., cognitively disengaging and automating one’s behavior). As noted in our reply to Recommendation #1 above, we now give some consideration of these explanations in our Discussion section, where we now write:

“It is also possible that these task-related shifts in connectivity relates to shifts in task-general processes, such as changes in the allocation of attentional resources (Bédard and Song, 2013; Rosenberg et al., 2016) or overall cognitive engagement (Aben et al., 2020), which themselves play critical roles in shaping learning (Codol et al., 2018; Holland et al., 2018; Song, 2019; Taylor and Thoroughman, 2008, 2007; for a review of these topics, see Tsay et al., 2023). Such processes are particularly important during the earlier phases of learning when sensorimotor contingencies need to be established. While these remain questions for future work, our data nevertheless suggest that this shift in connectivity may be enabled through the PMC.”

(3b) The authors are mixing two commonly used paradigms, reward-based learning, and motor adaptation, but provide no discussion of the different learning processes at play here. Which processes were they attempting to probe? Making this explicit would help the reader understand which brain regions should be implicated based on previous literature. As it stands, the task is hard to interpret. Relatedly, there is a wealth of literature on explicit vs implicit learning mechanisms in adaptation tasks now. Given that the authors are specifically looking at brain structures in the cerebral cortex that are commonly associated with explicit and strategic learning rather than implicit adaptation, how do the authors relate their findings to this literature? Are the learning processes probed in the task more explicit, more implicit, or is there a change in strategy usage over time? Did the authors acquire data on strategies used by the participants to solve the task? How does the baseline variability come into play here?

As noted in our paper, our task was directly inspired by the reward-based motor learning tasks developed by Dam et al., 2013 (Plos One) and Wu et al., 2014 (Nature Neuroscience). What drew us to these tasks is that they allowed us to study the neural bases of reward-based learning mechanisms in the absence of subjects also being able to exploit error-based mechanisms to achieve learning. Indeed, when first describing the task in the Results section of our paper we wrote the following:

“Importantly, because subjects received no visual feedback about their actual finger trajectory and could not see their own hand, they could only use the score feedback — and thus only reward-based learning mechanisms — to modify their movements from one trial to the next (Dam et al., 2013; Wu et al., 2014).”

If the reviewers are referring to ‘motor adaptation’ in the context in which that terminology is commonly used — i.e., the use of sensory prediction errors to support error-based learning — then we would argue that motor adaptation is not a feature of the current study. It is true that in our study subjects learn to ‘adapt’ their movements across trials, but this shaping of the movement trajectories must be supported through reinforcement learning mechanisms (and, of course, supplemented by the use of cognitive strategies as discussed in the nice review by Tsay et al., 2023). We apologize for not being clearer in our paper about this key distinction and we have now included new text in the introduction to our Results to directly address this:

“Importantly, because subjects received no visual feedback about their actual finger trajectory and could not see their own hand, they could only use the score feedback — and thus only reward-based learning mechanisms — to modify their movements from one trial to the next (Dam et al., 2013; Wu et al., 2014). That is, subjects could not use error-based learning mechanisms to achieve learning in our study, as this form of learning requires sensory errors that convey both the change in direction and magnitude needed to correct the movement.”

With this issue aside, we are well aware of the established framework for thinking about sensorimotor adaptation as being composed of a combination of explicit and implicit components (indeed, this has been a central feature of several of our other recent neuroimaging studies that have explored visuomotor rotation learning, e.g., Gale et al., 2022 PNAS, Areshenkoff et al., 2022 elife, Standage et al., 2023 Cerebral Cortex). However, there has been comparably little work done on these parallel components within the domain of reinforcement learning tasks (though see Codol et al., 2018; Holland et al., 2018, van Mastrigt et al., 2023; see also the Tsay et al., 2023 review), and as far as we can tell, nothing has been done to date in the reward-based motor learning area using fMRI. By design, we avoided using descriptors of ‘explicit’ or ‘implicit’ in our study because our experimental paradigm did not allow a separate measurement of those two components to learning during the task. Nevertheless, it seems clear to us from examining the subjects’ learning curves (see supplementary figure 2 above), that individuals who learn very quickly are using strategic processes (such as action exploration to identify the best path) to enhance their learning. As we noted in an above response, we did not query subjects after the fact about their strategy use, which admittedly was a missed opportunity on our part.

Author response image 6.

With respect to the comment on baseline variability and its relationship to performance, this is an interesting idea and one that was explored in the Wu et al., 2014 Nature Neuroscience paper. Prompted by the reviewers, we have now explored this idea in the current data set by testing for a relationship between movement path variability during baseline trials (all 70 baseline trials, see Supplementary Figure 1D above for reference) and subjects’ fPCA score on our learning task. However, when we performed this analysis, we did not observe a significant positive relationship between baseline variability and subject performance. Rather, we actually found a trend towards a negative relationship (though this was non-significant; r=-0.2916, p=0.0844). Admittedly, we are not sure what conclusions can be drawn from this analysis, and in any case, we believe it to be tangential to our main results. We provide the results (at right) for the reviewers if they are interested. This may be an interesting avenue for exploration in future work.

Recommendation #4: Provide stronger justification for brain imaging methods.

(4a) Observing how brain activity varies across these different networks is remarkable, especially how sensorimotor regions separate and then contract with other, more cognitive areas. However, does the signal-to-noise ratio in each area/network influence manifold eccentricity and limit the possible changes in eccentricity during learning? Specifically, if a region has a low signal-to-noise ratio, it might exhibit minimal changes during learning (a phenomenon perhaps relevant to null manifold changes in the striatum due to low signal-to-noise); conversely, regions with higher signal-to-noise (e.g., motor cortex in this sensorimotor task) might exhibit changes more easily detected. As such, it is unclear how to interpret manifold changes without considering an area/network's signal-to-noise ratio.

We appreciate where these concerns are coming from. First, we should note that the timeseries data used in our analysis were z-transformed (mean zero, 1 std) to allow normalization of the signal both over time and across regions (and thus mitigate the possibility that the changes observed could simply reflect mean overall signal changes across different regions). Nevertheless, differences in signal intensity across brain regions — particularly between cortex and striatum — are well-known, though it is not obvious how these differences may manifest in terms of a task-based modulation of MR signals.

To examine this issue in the current data set, we extracted, for each subject and time epoch (Baseline, Early and Late learning) the raw scanner data (in MR arbitrary units, a.u.) for the cortical and striatal regions and computed the (1) mean signal intensity, (2) standard deviation of the signal (Std) and (3) temporal signal to noise ratio (tSNR; calculated by mean/Std). Note that in the fMRI connectivity literature tSNR is often the preferred SNR measure as it normalizes the mean signal based on the signal’s variability over time, thus providing a general measure of overall ‘signal quality’. The results of this analysis, averaged across subjects and regions, is shown below.

Author response image 7.

Note that, as expected, the overall signal intensity (left plot) of cortex is higher than in the striatum, reflecting the closer proximity of cortex to the receiver coils in the MR head coil. In fact, the signal intensity in cortex is approximately 38% higher than that in the striatum (~625 - 450)/450). However, the signal variation in cortex is also greater than striatum (middle plot), but in this case approximately 100% greater (i.e., (~5 - 2.5)/2.5)). The result of this is that the tSNR (mean/std) for our data set and the ROI parcellations we used is actually greater in the striatum than in cortex (right plot). Thus, all else being equal, there seems to have been sufficient tSNR in the striatum for us to have detected motor-learning related effects. As such, we suspect the null effects for the striatum in our study actually stem from two sources.

The first likely source is the relatively lower number of striatal regions (12) as compared to cortical regions (998) used in our analysis, coupled with our use of PCA on these data (which, by design, identifies the largest sources of variation in connectivity). In future studies, this unbalance could be rectified by using finer parcellations of the striatum (even down to the voxel level) while keeping the same parcellation of cortex (i.e., equate the number of ‘regions’ in each of striatum and cortex). The second likely source is our use of a striatal atlas (the Harvard-Oxford atlas) that divides brain regions based on their neuroanatomy rather than their function. In future work, we plan on addressing this latter concern by using finer, more functionally relevant parcellations of striatum (such as in Tian et al., 2020, Nature Neuroscience). Note that we sought to capture these interrelated possible explanations in our Discussion section, where we wrote the following:

“While we identified several changes in the cortical manifold that are associated with reward-based motor learning, it is noteworthy that we did not observe any significant changes in manifold eccentricity within the striatum. While clearly the evidence indicates that this region plays a key role in reward-guided behavior (Averbeck and O’Doherty, 2022; O’Doherty et al., 2017), there are several possible reasons why our manifold approach did not identify this collection of brain areas. First, the relatively small size of the striatum may mean that our analysis approach was too coarse to identify changes in the connectivity of this region. Though we used a 3T scanner and employed a widely-used parcellation scheme that divided the striatum into its constituent anatomical regions (e.g., hippocampus, caudate, etc.), both of these approaches may have obscured important differences in connectivity that exist within each of these regions. For example, areas such the hippocampus and caudate are not homogenous areas but themselves exhibit gradients of connectivity (e.g., head versus tail) that can only be revealed at the voxel level (Tian et al., 2020; Vos de Wael et al., 2021). Second, while our dimension reduction approach, by design, aims to identify gradients of functional connectivity that account for the largest amounts of variance, the limited number of striatal regions (as compared to cortex) necessitates that their contribution to the total whole-brain variance is relatively small. Consistent with this perspective, we found that the low-dimensional manifold architecture in cortex did not strongly depend on whether or not striatal regions were included in the analysis (see Supplementary Fig. 6). As such, selective changes in the patterns of functional connectivity at the level of the striatum may be obscured using our cortex x striatum dimension reduction approach. Future work can help address some of these limitations by using both finer parcellations of striatal cortex (perhaps even down to the voxel level)(Tian et al., 2020) and by focusing specifically on changes in the interactions between the striatum and cortex during learning. The latter can be accomplished by selectively performing dimension reduction on the slice of the functional connectivity matrix that corresponds to functional coupling between striatum and cortex.”

(4b) Could the authors clarify how activity in the dorsal attention network (DAN) changes throughout learning, and how these changes also relate to individual differences in learning performance? Specifically, on average, the DAN seems to expand early and contract late, relative to the baseline. This is interpreted to signify that the DAN exhibits lesser connectivity followed by greater connectivity with other brain regions. However, in terms of how these changes relate to behavior, participants who go against the average trend (DAN exhibits more contraction early in learning, and expansion from early to late) seem to exhibit better learning performance. This finding is quite puzzling. Does this mean that the average trend of expansion and contraction is not facilitative, but rather detrimental, to learning? [Another reviewer added: The authors do not state any explicit hypotheses, but only establish that DMN coordinates activity among several regions. What predictions can we derive from this? What are the authors looking for in the data? The work seems more descriptive than hypothesis-driven. This is fine but should be clarified in the introduction.]

These are good questions, and we are glad the reviewers appreciated the subtlety here. The reviewers are indeed correct that the relationship of the DAN-A network to behavioral performance appears to go against the grain of the group-level results that we found for the entire DAN network (which we note is composed of both the DAN-A and DAN-B networks). That is, subjects who exhibited greater contraction from Baseline to Early learning and likewise, greater expansion from Early to Late learning, tended to perform better in the task (according to our fPCA scores). However, on this point it is worth noting that it was mainly the DAN-B network which exhibited group-level expansion from Baseline to Early Learning whereas the DAN-A network exhibited negligible expansion. This can be seen in Author response image 8 below, which shows the pattern of expansion and contraction (as in Fig. 4), but instead broken down into the 17-network parcellation. The red asterisk denotes the expansion from Baseline to Early learning for the DAN-B network, which is much greater than that observed for the DAN-A network (which is basically around the zero difference line).

Author response image 8.

Thus, it appears that the DAN-A and DAN-B networks are modulated to a different extent during the task, which likely contributes to the perceived discrepancy between the group-level effects (reported using the 7-network parcellation) and the individual differences effects (reported using the finer 17-network parcellation). Based on the reviewers’ comments, this seems like an important distinction to clarify in the manuscript, and we have now described this nuance in our Results section where we now write:

“...Using this permutation testing approach, we found that it was only the change in eccentricity of the DAN-A network that correlated with Learning score (see Fig. 7C), such that the more the DAN-A network decreased in eccentricity from Baseline to Early learning (i.e., contracted along the manifold), the better subjects performed at the task (see Fig. 7C, scatterplot at right). Consistent with the notion that changes in the eccentricity of the DAN-A network are linked to learning performance, we also found the inverse pattern of effects during Late learning, whereby the more that this same network increased in eccentricity from Early to Late learning (i.e., expanded along the manifold), the better subjects performed at the task (Fig. 7D). We should note that this pattern of performance effects for the DAN-A — i.e., greater contraction during Early learning and greater expansion during Late learning being associated with better learning — appears at odds with the group-level effects described in Fig. 4A and B, where we generally find the opposite pattern for the entire DAN network (composed of the DAN-A and DAN-B subnetworks). However, this potential discrepancy can be explained when examining the changes in eccentricity using the 17-network parcellation (see Supplementary Figure 8). At this higher resolution level we find that these group-level effects for the entire DAN network are being largely driven by eccentricity changes in the DAN-B network (areas in anterior superior parietal cortex and premotor cortex), and not by mean changes in the DAN-A network. By contrast, our present results suggest that it is the contraction and expansion of areas of the DAN-A network (and not DAN-B network) that are selectively associated with differences in subject learning performance.”

Finally, re: the reviewers’ comments that we do not state any explicit hypotheses etc., we acknowledge that, beyond our general hypothesis stated at the outset about the DMN being involved in reward-based motor learning, our study is quite descriptive and exploratory in nature. Such little work has been done in this research area (i.e., using manifold learning approaches to study motor learning with fMRI) that it would be disingenuous to have any stronger hypotheses than those stated in our Introduction. Thus, to make the exploratory nature of our study clear to the reader, we have added the following text (in red) to our Introduction:

“Here we applied this manifold approach to explore how brain activity across widely distributed cortical and striatal systems is coordinated during reward-based motor learning. We were particularly interested in characterizing how connectivity between regions within the DMN and the rest of the brain changes as participants shift from learning the relationship between motor commands and reward feedback, during early learning, to subsequently using this information, during late learning. We were also interested in exploring whether learning-dependent changes in manifold structure relate to variation in subject motor performance.”

We hope these changes now make it obvious the intention of our study.

(4c) The paper examines a type of motor adaptation task with a reward-based learning component. This, to me, strongly implicates the cerebellum, given that it has a long-established crucial role in adaptation and has recently been implicated in reward-based learning (see work by Wagner & Galea). Why is there no mention of the cerebellum and why it was left out of this study? Especially given that the authors state in the abstract they examine cortical and subcortical structures. It's evident from the methods that the authors did not acquire data from the cerebellum or had too small a FOV to fully cover it (34 slices at 4 mm thickness 136 mm which is likely a bit short to fully cover the cerebellum in many participants). What was the rationale behind this methodological choice? It would be good to clarify this for the reader. Related to this, the authors need to rephrase their statements on 'whole-brain' connectivity matrices or analyses - it is not whole-brain when it excludes the cerebellum.

As we noted above, we do not believe this task to be a motor adaptation task, in the sense that subjects are not able to use sensory prediction errors (and thus error-based learning mechanisms) to improve their performance. Rather, by denying subjects this sensory error feedback they are only able to use reinforcement learning processes, along with cognitive strategies (nicely covered in Tsay et al., 2023), to improve performance. Nevertheless, we recognize that the cerebellum has been increasingly implicated in facets of reward-based learning, particularly within the rodent domain (e.g., Wagner et al., 2017; Heffley et al., 2018; Kostadinov et al., 2019, etc.). In our study, we did indeed collect data from the cerebellum but did not include it in our original analyses, as we wanted (1) the current paper to build on prior work in the human and macaque reward-learning domain (which focuses solely on striatum and cortex, and which rarely discusses cerebellum, see Averbeck & O’Doherty, 2022 & Klein-Flugge et al., 2022 for recent reviews), and, (2) allow this to be a more targeted focus of future work (specifically we plan on focusing on striatal-cerebellar interactions during learning, which are hypothesized based on the neuroanatomical tract tracing work of Bostan and Strick, etc.). We hope the reviewers respect our decisions in this regard.

Nevertheless, we acknowledge that based on our statements about ‘whole-brain’ connectivity and vagueness about what we mean by ‘subcortex,’ that this may be confusing for the reader. We have now removed and/or corrected such references throughout the paper (however, note that in some cases it is difficult to avoid reference to “whole-brain” — e.g., “whole-brain correlation map” or “whole-brain false discovery rate correction”, which is standard terminology in the field).

In addition, we are now explicit in our Methods section that the cerebellum was not included in our analyses.

“Each volume comprised 34 contiguous (no gap) oblique slices acquired at a ~30° caudal tilt with respect to the plane of the anterior and posterior commissure (AC-PC), providing whole-brain coverage of the cerebrum and cerebellum. Note that for the current study, we did not examine changes in cerebellar activity during learning.”

(4d) The authors centered the matrices before further analyses to remove variance associated with the subject. Why not run a PCA on the connectivity matrices and remove the PC that is associated with subject variance? What is the advantage of first centering the connectivity matrices? Is this standard practice in the field?

Centering in some form has become reasonably common in the functional connectivity literature, as there is considerable evidence that task-related (or cognitive) changes in whole-brain connectivity are dwarfed by static, subject-level differences (e.g., Gratton, et al, 2018, Neuron). If covariance matrices were ordinary scalar values, then isolating task-related changes could be accomplished simply by subtracting a baseline scan or mean score; but because the space of covariance matrices is non-Euclidean, the actual computations involved in this subtraction are more complex (see our Methods). However, fundamentally (and conceptually) our procedure is simply ordinary mean-centering, but adapted to this non-Euclidean space. Despite the added complexity, there is considerable evidence that such computations — adapted directly to the geometry of the space of covariance matrices — outperform simpler methods, which treat covariance matrices as arrays of real numbers (e.g. naive substraction, see Dodero et al. & Ng et al., references below). Moreover, our previous work has found that this procedure works quite well to isolate changes associated with different task conditions (Areshenkoff et al., 2021, Neuroimage; Areshenkoff et al., 2022, elife).

Although PCA can be adapted to work well with covariance matrix valued data, it would at best be a less direct solution than simply subtracting subjects' mean connectivity. This is because the top components from applying PCA would be dominated by both subject-specific effects (not of interest here), and by the large-scale connectivity structure typically observed in component based analyses of whole-brain connectivity (i.e. the principal gradient), whereas changes associated with task-condition (the thing of interest here) would be buried among the less reliable components. By contrast, our procedure directly isolates these task changes.

References cited above:

Dodero, L., Minh, H. Q., San Biagio, M., Murino, V., & Sona, D. (2015, April). Kernel-based classification for brain connectivity graphs on the Riemannian manifold of positive definite matrices. In 2015 IEEE 12th international symposium on biomedical imaging (ISBI) (pp. 42-45). IEEE.

Ng, B., Dressler, M., Varoquaux, G., Poline, J. B., Greicius, M., & Thirion, B. (2014). Transport on Riemannian manifold for functional connectivity-based classification. In Medical Image Computing and Computer-Assisted Intervention–MICCAI 2014: 17th International Conference, Boston, MA, USA, September 14-18, 2014, Proceedings, Part II 17 (pp. 405-412). Springer International Publishing.

(4e) Seems like a missed opportunity that the authors just use a single, PCA-derived measure to quantify learning, where multiple measures could have been of interest, especially given that the introduction established some interesting learning-related concepts related to exploration and exploitation, which could be conceptualized as movement variability and movement accuracy. It is unclear why the authors designed a task that was this novel and interesting, drawing on several psychological concepts, but then chose to ignore these concepts in the analysis.

We were disappointed to hear that the reviewers did not appreciate our functional PCA-derived measure to quantify subject learning. This is a novel data-driven analysis approach that we have previously used with success in recent work (e.g., Areshenkoff et al., 2022, elife) and, from our perspective, we thought it was quite elegant that we were able to describe the entire trajectory of learning across all participants along a single axis that explained the majority (~75%) of the variance in the patterns of behavioral learning data. Moreover, the creation of a single behavioral measure per participant (what we call a ‘Learning score’, see Fig. 6C) helped simplify our brain-behavior correlation analyses considerably, as it provided a single measure that accounts for the natural auto-correlation in subjects’ learning curves (i.e., that subjects who learn quickly also tend to be better overall learners by the end of the learning phase). It also avoids the difficulty (and sometimes arbitrariness) of having to select specific trial bins for behavioral analysis (e.g., choosing the first 5, 10, 20 or 25 trials as a measure of ‘early learning’, and so on). Of course, one of the major alternatives to our approach would have involved fitting an exponential to each subject’s learning curves and taking measures like learning rate etc., but in our experience we have found that these types of models don’t always fit well, or derive robust/reliable parameters at the individual subject level. To strengthen the motivation for our approach, we have now included the following text in our Results:

“To quantify this variation in subject performance in a manner that accounted the auto-correlation in learning performance over time (i.e., subjects who learned more quickly tend to exhibit better performance by the end of learning), we opted for a pure data-driven approach and performed functional principal component analysis (fPCA; (Shang, 2014)) on subjects’ learning curves. This approach allowed us to isolate the dominant patterns of variability in subject’s learning curves over time (see Methods for further details; see also Areshenkoff et al., 2022).”

In any case, the reviewers may be pleased to hear that in current work in the lab we are using more model-based approaches to attempt to derive sets of parameters (per participant) that relate to some of the variables of interest described by the reviewers, but that we relate to much more dynamical (shorter-term) changes in brain activity.

(4f) Overall Changes in Activity: The manuscript should delve into the potential influence of overall changes in brain activity on the results. The choice of using Euclidean distance as a metric for quantifying changes in connectivity is sensitive to scaling in overall activity. Therefore, it is crucial to discuss whether activity in task-relevant areas increases from baseline to early learning and decreases from early to late learning, or if other patterns emerge. A comprehensive analysis of overall activity changes will provide a more complete understanding of the findings.

These are good questions and we are happy to explore this in the data. However, as mentioned in our response to query 4a above, it is important to note that the timeseries data for each brain region was z-scored prior to analysis, with the aim of removing any mean changes in activity levels (note that this is a standard preprocessing step when performing functional connectivity analysis, given that mean signal changes are not the focus of interest in functional connectivity analyses).

To further emphasize these points, we have taken our z-scored timeseries data and calculated the mean signal for each region within each task epoch (Baseline, Early and Late learning, see panel A in figure below). The point of showing this data (where each z-score map looks near identical across the top, middle and bottom plots) is to demonstrate just how miniscule the mean signal changes are in the z-scored timeseries data. This point can also be observed when plotting the mean z-score signal across regions for each epoch (see panel B in figure below). Here we find that Baseline and Early learning have a near identical mean activation level across regions (albeit with slightly different variability across subjects), whereas there is a slight increase during late learning — though it should be noted that our y-axis, which measures in the thousandths, really magnifies this effect.

To more directly address the reviewers’ comments, using the z-score signal per region we have also performed the same statistical pairwise comparisons (Early > Baseline and Late>Early) as we performed in the main manuscript Fig. 4 (see panel C in Author response image 9 below). In this plot, areas in red denote an increase in activity from Baseline to Early learning (top plot) and from Early to Late learning (bottom plot), whereas areas in blue denote a decrease for those same comparisons. The important thing to emphasize here is that the spatial maps resulting from this analysis are generally quite different from the maps of eccentricity that we report in Fig. 4 in our paper. For instance, in the figure below, we see significant changes in the activity of visual cortex between epochs but this is not found in our eccentricity results (compare with Fig. 4). Likewise, in our eccentricity results (Fig. 4), we find significant changes in the manifold positioning of areas in medial prefrontal cortex (MPFC), but this is not observed in the activation levels of these regions (panel C below). Again, we are hesitant to make too much of these results, as the activation differences denoted as significant in the figure below are likely to be an effect on the order of thousandths of a z-score (e.g., 0.002 > 0.001), but this hopefully assuages reviewers’ concerns that our manifold results are solely attributable to changes in overall activity levels.

We are hesitant to include the results below in our paper as we feel that they don’t add much to the interpretation (as the purpose of z-scoring was to remove large activation differences). However, if the reviewers strongly believe otherwise, we would consider including them in the supplement.

Author response image 9.

Examination of overall changes in activity across regions. (A) Mean z-score maps across subjects for the Baseline (top), Early Learning (middle) and Late learning (bottom) epochs. (B) Mean z-score across brain regions for each epoch. Error bars represent +/- 1 SEM. (C) Pairwise contrasts of the z-score signal between task epochs. Positive (red) and negative (blue) values show significant increases and decreases in z-score signal, respectively, following FDR correction for region-wise paired t-tests (at q<0.05).

Author response:

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

Reviewer #1 (Public Review):

Summary:

This manuscript explores the impact of serotonin on olfactory coding in the antennal lobe of locusts and odor-evoked behavior. The authors use serotonin injections paired with an odorevoked palp-opening response assay and bath application of serotonin with intracellular recordings of odor-evoked responses from projection neurons (PNs).

Strengths:

The authors make several interesting observations, including that serotonin enhances behavioral responses to appetitive odors in starved and fed animals, induces spontaneous bursting in PNs, directly impacts PN excitability, and uniformly enhances PN responses to odors.

Weaknesses:

The one remaining issue to be resolved is the theoretical discrepancy between the physiology and the behavior. The authors provide a computational model that could explain this discrepancy and provide the caveat that while the physiological data was collected from the antennal lobe, but there could be other olfactory processing stages involved. Indeed other processing stages could be the sites for the computational functions proposed by the model. There is an additional caveat which is that the physiological data were collected 5-10 minutes after serotonin application whereas the behavioral data were collected 3 hours after serotonin application. It is difficult to link physiological processes induced 5 minutes into serotonin application to behavioral consequences 3 hours subsequent to serotonin application. The discrepancy between physiology and behavior could easily reflect the timing of action of serotonin (i.e. differences between immediate and longer-term impact).

For our behavioral experiments, we waited 3 hours after serotonin injection to allow serotonin to penetrate through the layers of air sacks and the sheath, and for the locusts to calm down and recover their baseline POR activity levels. For the physiology experiments, we noticed that the quality of the patch decreased over time after serotonin introduction. Hence, it was difficult to hold cells for that long. However, the point raised by the reviewer is well-taken. We have performed additional experiments to show that the changes in POR levels to different odorants are rapid and can be observed within 15 minutes of injecting serotonin (Author response image 2) and that the physiological changes in PNs (bursting spontaneous activity, maintenance of temporal firing patterns, and increase odor-evoked responses) persists when the cells are held for longer duration (i.e. 3 hours akin to our behavioral experiments). It is worth noting that 3-hour in-vivo intracellular recordings are not easily achievable and come with many experimental constraints. So far, we have managed to record from two PNs that were held for this long and add them to this rebuttal to support our conclusions. (Author response image 1).

Author response image 1.

Spontaneous and odor-evoked responses in individual PNs remain consistent for three hours after serotonin introduction into the recording chamber/bath. (A) Representative intracellular recording showing membrane potential fluctuations in a projection neuron (PN) in the antennal lobe. Spontaneous and odor-evoked responses to four odorants (pink color bars, 4 s duration) are shown before (control) and after serotonin application (5HT). Voltage traces 30 minutes (30min), 1 hour (1h), 2 hours (2h), and 3 hours (3h) after 5HT application are shown to illustrate the persisting effect of serotonin during spontaneous and odor-evoked activity periods. (B) Rasterized spiking activities in two recorded PNs are shown. Spontaneous and odor-evoked responses are shown in all 5 consecutive trials. Note that the odor-evoked response patterns are maintained, but the spontaneous activity patterns are altered after serotonin introduction.

Author response image 2.

Palp-opening response (POR) patterns to different odorants remain consistent following serotonin introduction. The probability of PORs is shown as a bar plot for four different odorants; hexanol (green), benzaldehyde (blue), linalool (red), and ammonium (purple). PORs before serotonin injection (solid bars) are compared against response levels after serotonin injection (striped bars). As can be noted, PORs to the four odorants remain consistent when tested 15 minutes and 3 hours after (5HT) serotonin injection.

Overall, the study demonstrates the impact of serotonin on odor-evoked responses of PNs and odor-guided behavior in locusts. Serotonin appears to have non-linear effects including changing the firing patterns of PNs from monotonic to bursting and altering behavioral responses in an odor-specific manner, rather than uniformly across all stimuli presented.

We thank the reviewer for again providing very useful feedback for improving our manuscript.

Reviewer #2 (Public Review):

Summary:

The authors investigate the influence of serotonin on feeding behavior and electrophysiological responses in the antennal lobe of locusts. They find that serotonin injection changes behavior in an odor-specific way. In physiology experiments, they can show that projection neurons in the antennal lobe generally increase their baseline firing and odor responses upon serotonin injection. Using a modeling approach the authors propose a framework on how a general increase in antennal lobe output can lead to odor-specific changes in behavior.

Strengths:

This study shows that serotonin affects feeding behavior and odor processing in the antennal lobe of locusts, as serotonin injection increases activity levels of projection neurons. This study provides another piece of evidence that serotonin is a general neuromodulator within the early olfactory processing system across insects and even phyla.

Weaknesses:

I still have several concerns regarding the generalizability of the model and interpretation of results. The authors cannot provide evidence that serotonin modulation of projection neurons impacts behavior.

This is true and likely to be true for any study linking neural responses to behavior. There are multiple circuits and pathways that would get impacted by a neuromodulator like serotonin. What we showed with our physiology is how spontaneous and odor-evoked responses in the very first neural network that receives olfactory sensory neuron input are altered by serotonin. Given the specificity of the changes in behavioral outcomes (i.e. odor-specific increase and decrease in an appetitive behavior) and non-specificity in the changes at the level of individual PNs (general increase in odor-evoked spiking activity), we presented a relatively simple computational model to address the apparent mismatch between neural and behavioral responses. (Author response image 4).

The authors show that odor identity is maintained after 5-HT injection, however, the authors do not show if PN responses to different odors were differently affected after serotonin exposure.

The PN responses to different odorants changed in a qualitatively similar fashion. (Author response image 3)

Author response image 3.

PN activity before and after 5HT application are compared for different cellodor combinations. As can be noted, the changes are qualitatively similar in all cases. After 5HT application, the baseline activity became more bursty, but the odor-evoked response patterns were robustly maintained for all odorants.

Regarding the model, the authors show that the model works for odors with non-overlapping PN activation. However, only one appetitive, one neutral, and one aversive odor has been tested and modeled here. Can the fixed-weight model also hold for other appetitive and aversive odors that might share more overlap between active PNs? How could the model generate BZA attraction in 5-HT exposed animals (as seen in behavior data in Figure 1) if the same PNs just get activated more?

Author response image 4.

Testing the generality of the proposed computational model. To test the generality of the model proposed we used a published dataset [Chandak and Raman, 2023]: Neural dataset – 89 PN responses to a panel of twenty-two odorants; Behavioral dataset – probability of POR responses to the same twenty-two odorants. We built the model using just the three odorants overlapping between the two datasets: hexanol, benzaldehyde and linalool. The true probability of POR values of the twenty odorants and the POR probability predicted by the model are shown for all twenty-two odorants as a scatter plot. As can be noted, there is a high correlation (0.79) between the true and the predicted values.

The authors should still not exclude the possibility that serotonin injections could affect behavior via modulation of other cell types than projection neurons. This should still be discussed, serotonin might rather shut down baseline activation of local inhibitory neurons - and thus lead to the interesting bursting phenotypes, which can also be seen in the baseline response, due to local PN-to-LN feedback.

As we agreed, there could be other cells that are impacted by serotonin release. Our goal in this study was to characterize how spontaneous and odor-evoked responses in the very first neural network that receives olfactory sensory neuron input are altered by serotonin. Within this circuit, there are local inhibitory neurons (LNs), as correctly indicated by this reviewer. Surprisingly, our preliminary data indicates that LNs are not shut down but also have an enhanced odor-evoked neural response. (Author response image 5.) Further data would be needed to verify this observation and determine the mechanism that mediate the changes in PN excitability. Irrespective, since PN activity should incorporate the effects of changes in the local neuron responses and is the sole output from the antennal lobe that drives all downstream odor-evoked activity, we focused on them in this study.

Author response image 5.

Representative traces showing intracellular recording from a local neuron in the antennal lobe. Five consecutive trials are shown. Note that LNs in the locust antennal lobe are non-spiking. The LN activity before, during, and after the presentation of benzaldehyde and hexanol (colored bar; 4s) are shown. The Left and Right panels show LN activity before and after the application of 5HT. As can be noted, 5HT did not shut down odor-evoked activity in this local neuron.

The authors did not fully tone down their claims regarding causality between serotonin and starved state behavioral responses. There is no proof that serotonin injection mimics starved behavioral responses.

Specific minor issues:<br /> It is still unclear how naturalistic the chosen odor concentrations are. This is especially important as behavioral responses to different concentrations of odors are differently modulated after serotonin injection (Figure 2: Linalool and Ammonium). The new method part does not indicate the concentrations of odors used for electrophysiology.

All odorants were diluted to 0.01-10% concentration by volume in either mineral oil or distilled water. This information is included in the Methods section. For most odorants used in the study, the lower concentrations only evoked a very weak neural response, and the higher concentrations evoked more robust responses. The POR responses for these odorants at various concentrations chosen are included in Figure 2. Note, that the responses to linalool and ammonium remained weak throughout the concentration changes, compared to hexanol and benzaldehyde.

Did all tested PNs respond to all odorants?

No, only a subset of them responses to each odorant. These responses have been well characterized in earlier publications [included refs].

The authors do not show if PN responses to different odors were differently affected after serotonin exposure. They describe that ON responses were robust, but OFF responses were less consistent after 5-HT injection. Was this true across all odors tested? Example traces are shown, but the odor is not indicated in Figure 4A. Figure 4D shows that many odor-PN combinations did not change their peak spiking activity - was this true across odorants? In Figure 5 - are PNs ordered by odor-type exposure?

Also, Figure 6A only shows example trajectories for odorants - how does the average look? Regarding the data used for the model - can the new dataset from the 82 odor-PN pairs reproduce the activation pattern of the previously collected dataset of 89 pairs?

What is shown in Figure 6A is the trial-averaged response trajectory combining activities of all 82 odor-PN pairs. 82 odor-PN pair was collected intracellularly examining the responses to four odorants before and after 5HT application. The second dataset involving 89 PN responses to 22 odorants was collected extracellularly. They have qualitative similarities in each odorant activate a unique subset of those neurons.

The authors toned down their claims that serotonin injection can mimic the starved state behavioral response. However, some sentences still indicate this finding and should also be toned down:

last sentence of introduction - "In sum, our results provide a more systems-level view of how a specific neuromodulator (serotonin) alters neural circuits to produce flexible behavioral outcomes."

We believe we showed this with our computational model, how uniform changes in the neural responses could lead to variable and odor-specific changes in behavioral PORs.

discussion: "Finally, fed locusts injected with serotonin generated similar appetitive responses to food-related odorants as starved locusts indicating the role of serotonin in hunger statedependent modulation of odor-evoked responses." This claim is not supported.

Figure 7 shows that the fed locusts had lower POR to hex and bza. The POR responses significantly increased after the 5HT application. However, we have rephrased this sentence to limit our claims to this result. "Finally, fed locusts injected with serotonin generated similar appetitive palp-opening responses to food-related odorants as observed in starved locusts”

last results: "However, consistent with results from the hungry locusts, the introduction of serotonin increased the appetitive POR responses to HEX and BZA. Intriguingly, the appetitive responses of fed locusts treated with 5HT were comparable or slightly higher than the responses of hungry locusts to the same set of odorants."

Again this sentence simply describes the result shown in Figure 7.

In Figure 7 - BZA response seems unchanged in hungry and fed animals and only 5-HT injection enhances the response. There is only one example where 5-HT application and starvation induce the same change in behavior - N=1 is not enough to conclude that serotonin influences food-driven behaviors.

The reviewer is ignoring the lack of changes to PORs to linalool and ammonium. Taken together, serotonin increased PORs to only two of the four odorants in starved locusts. The responses after 5HT modulation to these four odorants were similar in fed locusts treated with 5HT and starved locusts.

Also, this seems to be wrongly interpreted in Figure 7: "It is worth noting that responses to LOOL and AMN, non-food related odorants with weaker PORs, remained unchanged in fed locusts treated with 5HT." The authors indicate a significant reduction in POR after 5-HT injection on LOOL response in Figure 7.

Revised.<br /> It is worth noting that responses to LOOL and AMN, non-food related odorants with weaker PORs, and reduced in fed locusts treated with 5HT."

Also, the newly added sentence at the end of the discussion does not make sense: "However, since 5HT increased behavioral responses in both fed and hungry locusts, the precise role of 5HT modulation and whether it underlies hunger-state dependent modulation of appetitive behavior still remains to be determined."<br /> The authors did not test 5-HT injection in starved animals

The results shown in Figure 1 compare the POR responses of starved locusts before and after 5HT introduction.

We again thank the reviewer for useful feedback to further improve our manuscript.

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

Reviewer #1 (Public Review):

Summary:

This manuscript explores the impact of serotonin on olfactory coding in the antennal lobe of locusts and odor-evoked behavior. The authors use serotonin injections paired with an odor-evoked palp-opening response assay and bath application of serotonin with intracellular recordings of odor-evoked responses from projection neurons (PNs).

Strengths:

The authors make several interesting observations, including that serotonin enhances behavioral responses to appetitive odors in starved and fed animals, induces spontaneous bursting in PNs, and uniformly enhances PN responses to odors. Overall, I had no technical concerns. Weaknesses:

While there are several interesting observations, the conclusions that serotonin enhanced sensitivity specifically and that serotonin had feeding-state-specific effects, were not supported by the evidence provided. Furthermore, there were other instances in which much more clarification was needed for me to follow the assumptions being made and inadequate statistical testing was reported.

Major concerns.

• To enhance olfactory sensitivity, the expected results would be that serotonin causes locusts to perceive each odor as being at a relatively higher concentration. The authors recapitulate a classic olfactory behavioral phenomenon where higher odor concentrations evoke weaker responses which is indicative of the odors becoming aversive. If serotonin enhanced the sensitivity to odors, then the dose-response curve should have shifted to the left, resulting in a more pronounced aversion to high odor concentrations. However, the authors show an increase in response magnitude across all odor concentrations. I don't think the authors can claim that serotonin enhances the behavioral sensitivity to odors because the locusts no longer show concentration-dependent aversion. Instead, I think the authors can claim that serotonin induces increased olfactory arousal.

The reviewer makes a valid point. Bath application of serotonin increased POR behavioral responses across all odor concentrations, and concentration-dependent aversion was also not observed. Furthermore, the monotonic relationship between projection neuron responses and the intensity of current injection is altered when serotonin is exogenously introduced (see Author response image 1; see below for more explanation). Hence, our data suggests that serotonin alters the dose-response relationship between neural/behavioral responses and odor intensity. As recommended, we have followed what the reviewer has suggested and revised our claim to serotonin inducing increase in olfactory arousal. The new physiology data has been added as Supplementary Figure 3 to the revised manuscript.

• The authors report that 5-HT causes PNs to change from tonic to bursting and conclude that this stems from a change in excitability. However, excitability tests (such as I/V plots) were not included, so it's difficult to disambiguate excitability changes from changes in synaptic input from other network components.

To confirm that the PN excitability did indeed change after serotonin application, we performed a new set of current-clamp recordings. In these experiments, we monitored the spiking activities in individual PNs as we injected different levels of current injections (200 – 1000 pico Amperes). Note that locust LNs that provide recurrent inhibition arborize and integrate inputs from a large number of sensory neurons and projection neurons. Therefore, activating a single PN should not activate the local neurons and therefore the antennal lobe network.

We found that the total spiking activity monotonically increased with the magnitude of the current injection in all four PNs recorded (Author response image 1). However, after serotonin injection, we found that the spiking activity remained relatively stable and did not systematically vary with the magnitude of the current injection. While the changes in odor-evoked responses may incorporate both excitability changes in individual PNs and recurrent feedback inhibition through GABAergic LNs, these results from our current injection experiments unambiguously indicate that there are changes in excitability at the level of individual PNs. We have added this result to the revised manuscript.

Author response image 1.

Current-injection induced spiking activity in individual PNs is altered after serotonin application. (A) Representative intracellular recordings showing membrane potential fluctuations as a function of time for one projection neuron (PNs) in the locust antennal lobe. A two-second window when a positive 200-1000pA current was applied is shown. Firing patterns before (left) and after (right) serotonin application are shown for comparison. Note, the spiking activity changes after the 5HT application. The black bar represents the 20mV scale. (B) Dose-response curves showing the average number of action potentials (across 5 trials) during the 2second current pulse before (green) and after (purple) serotonin for each recorded PN. Note that the current intensity was systematically increased from 200 pA to 1000 pA. The (C) The mean number of spikes across the four recorded cells during current injection is shown. The color progression represents the intensity of applied current ranging 200pA (leftmost bar) to 1000pA (rightmost bar). The dose-response trends before (green) and after (purple) 5HT application are shown for comparison. The error bars represent SEM across the four cells.

• There is another explanation for the theoretical discrepancy between physiology and behavior, which is that odor coding is further processing in higher brain regions (ie. Other than the antennal lobe) not studied in the physiological component of this study. This should at least be discussed.

This is a valid argument. For our model of neural mapping onto behavior to work, we only need the odorant that evokes or suppresses PORs to activate a distinct set of neurons. Having said that, our extracellular recording results (Fig. 6E) indicate that hexanol (high POR) and linalool (low POR) do activate highly non-overlapping sets of PNs in the antennal lobe. Hence, our results suggest that the segregation of neural activity based on behavioral relevance already begins in the antennal lobe. We have added this clarification to the discussion section.

• The authors cannot claim that serotonin underlies a hunger state-dependent modulation, only that serotonin impacts responses to appetitive odors. Serotonin enhanced PORs for starved and fed locusts, so the conclusion would be that serotonin enhances responses regardless of the hunger state. If the authors had antagonized 5-HT receptors and shown that feeding no longer impacts POR, then they could make the claim that serotonin underlies this effect. As it stands, these appear to be two independent phenomena.

This is also a valid point. We have clarified this in the revised manuscript.

Reviewer #2 (Public Review):

Summary:

The authors investigate the influence of serotonin on feeding behavior and electrophysiological responses in the antennal lobe of locusts. They find that serotonin injection changes behavior in an odorspecific way. In physiology experiments, they can show that antennal lobe neurons generally increase their baseline firing and odor responses upon serotonin injection. Using a modeling approach the authors propose a framework on how a general increase in antennal lobe output can lead to odorspecific changes in behavior. The authors finally suggest that serotonin injection can mimic a change in a hunger state.

Strengths:

This study shows that serotonin affects feeding behavior and odor processing in the antennal lobe of locusts, as serotonin injection increases activity levels of antennal lobe neurons. This study provides another piece of evidence that serotonin is a general neuromodulator within the early olfactory processing system across insects and even phyla. Weaknesses:

I have several concerns regarding missing control experiments, unclear data analysis, and interpretation of results.

A detailed description of the behavioral experiments is lacking. Did the authors also provide a mineral oil control and did they analyze the baseline POR response? Is there an increase in baseline response after serotonin exposure already at the behavioral output level? It is generally unclear how naturalistic the chosen odor concentrations are. This is especially important as behavioral responses to different concentrations of odors are differently modulated after serotonin injection (Figure 2: Linalool and Ammonium).

POR protocol: Sixth instar locusts (Schistocera americana) of either sex were starved for 24-48 hours before the experiment or taken straight from the colony and fed blades of grass for the satiated condition. Locusts were immobilized by placing them in the plastic tube and securing their body with black electric tape (see Author response image 2). Locusts were given 20 - 30 minutes to acclimatize after placement in the immobilization tube. As can be noted, the head of the locusts along with the antenna and maxillary palps protruded out of this immobilization tube so they can be freely moved by the locusts. Note that the maxillary palps are sensory organs close to the mouth parts that are used to grab food and help with the feeding process.

It is worth noting that our earlier studies had shown that the presentation of ‘appetitive odorants’ triggers the locust to open their maxillary palps even when no food is presented (Saha et al., 2017; Nizampatnam et al., 2018; Nizampatnam et al., 2022; Chandak and Raman, 2023.) Furthermore, our earlies results indicate that the probability of palp opening varies across different odorants (Chandak and Raman, 2023). We chose four odorants that had a diverse range of palp-opening: supra-median (hexanol), median (benzaldehyde), and sub-median (linaool). Therefore, each locust in our experiments was presented with one concentration of four odorants (hexanol, benzaldehyde, linalool, and ammonium) in a pseudorandomized order. The odorants were chosen based on our physiology results such that they evoked different levels of spiking activities.

The odor pulse was 4 s in duration and the inter-pulse interval was set to 60 s. The experiments were recorded using a web camera (Microsoft) placed right in front of the locusts. The camera was fully automated with the custom MATLAB script to start recording 2 seconds before the odor pulse and end recording at odor termination. An LED was used to track the stimulus onset/offset. The POR responses were manually scored offline. Responses to each odorant were scored a 0 or 1 depending on if the palps remained closed or opened. A positive POR was defined as a movement of the maxillary palps during the odor presentation time window as shown on the locust schematic (Main Paper Figure 1).

Author response image 2.

Pictures showing the behavior experiment setup and representative palp-opening responses in a locust.

As the reviewer inquired, we performed a new series of POR experiments, where we explored POR responses to mineral oil and hexanol, before and after serotonin injection. For this study, we used 10 locusts that were starved 24-48 hours before the experiment. Note that hexanol was diluted at 1% (v/v) concentration in mineral oil. Our results reveal that locusts PORs to hexanol (~ 50% PORs) were significantly higher than those triggered by mineral oil (~10% PORs). Injection of serotonin increased the POR response rate to hexanol but did not alter the PORs evoked by mineral oil (Author response image 3).

Author response image 3.

Serotonin does not alter the palp-opening responses evoked by paraffin oil. The PORs before and after (5HT) serotonin injection are summarized and shown as a bar plot for hexanol and paraffin oil. Striped bars signify the data collected after 5HT injection. Significant differences are identified in the plot (one-tailed paired-sample t-test; (*p<0.05).

Regarding recordings of potential PNs - the authors do not provide evidence that they did record from projection neurons and not other types of antennal lobe neurons. Thus, these claims should be phrased more carefully.

In the locust antennal lobe, only the cholinergic projection neurons fire full-blown sodium spikes. The GABAergic local neurons only fire calcium ‘spikelets’ (Laurent, TINS, 1996; Stopfer et al., 2003; see Author response image 4 for an example). Hence, we are pretty confident that we are only recording from PNs. Furthermore, due to the physiological properties of the LNs, their signals being too small, they are also not detected in the extracellular recordings from the locust antennal lobe. Hence, we are confident with our claims and conclusion.

Author response image 4.

PN vs LN physiological differences: Left: A representative raw voltage traces recorded from a local neuron before, during, and after a 4-second odor pulse are shown. Note that the local neurons in the locust antennal lobe do not fire full-blown sodium spikes but only fire small calcium spikelets. On the right: A representative raw voltage trace recorded from a representative projection neuron is shown for comparison. Clear sodium spikes are clearly visible during spontaneous and odor-evoked periods. The gray bar represents 4 seconds of odor pulse. The vertical black bar represents the 40mV.

The presented model suggests labeled lines in the antennal lobe output of locusts. Could the presented model also explain a shift in behavior from aversion to attraction - such as seen in locusts when they switch from a solitarious to a gregarious state? The authors might want to discuss other possible scenarios, such as that odor evaluation and decision-making take place in higher brain regions, or that other neuromodulators might affect behavioral output. Serotonin injections could affect behavior via modulation of other cell types than antennal lobe neurons. This should also be discussed - the same is true for potential PNs - serotonin might not directly affect this cell type, but might rather shut down local inhibitory neurons.

There are multiple questions here. First, regarding solitary vs. gregarious states, we are currently repeating these experiments on solitary locusts. Our preliminary results (not included in the manuscript) indicate that the solitary animals have increased olfactory arousal and respond with a higher POR but are less selective and respond similarly to multiple odorants. We are examining the physiology to determine whether the model for mapping neural responses onto behavior could also explain observations in solitary animals.

Second, this reviewer makes the point raised by Reviewer 1. We agree that odor evaluation and decisionmaking might take place in higher brain regions. All we could conclude based on our data is that a segregation of neural activity based on behavioral relevance might provide the simplest approach to map non-specific increase in stimulus-evoked neural responses onto odor-specific changes in behavioral outcome. Furthermore, our results indicate that hexanol and linalool, two odorants that had an increase and decrease in PORs after serotonin injection, had only minimal neural response overlap in the antennal lobe. These results suggest that the formatting of neural activity to support varying behavioral outcomes might already begin in the antennal lobe. We have added this to our discussion.

Third, regarding serotonin impacting PNs, we performed a new set of current-clamp experiments to examine this issue (Author response image 1). Our results clearly show that projection neuron activity in response to current injections (that should not incorporate feedback inhibition through local neurons) was altered after serotonin injection. Therefore, the observed changes in the odor-evoked neural ensemble activity should incorporate modulation at both individual PN level and at the network level. We have added this to our discussion as well.

Finally, the authors claim that serotonin injection can mimic the starved state behavioral response. However, this is only shown for one of the four odors that are tested for behavior (HEX), thus the data does not support this claim.

We note that Hex is the only appetitive odorant in the panel. But, as reviewer 1 has also brought up a similar point, we have toned down our claims and will investigate this carefully in a future study.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

• Was the POR of the locusts towards linalool and ammonium higher than towards a blank odor cartridge? I ask because the locusts appear to be less likely to respond to these odors and so I am concerned that this assay is not relevant to the ecological context of these odors. In other words, perhaps serotonin did not enhance the responses to these odors in this assay, because this is not a context in which locusts would normally respond to these odors.

The POR response to linalool and ammonium is lower and comparable to that of paraffin oil. Serotonin does not increase POR responses to paraffin oil but does increase response to hexanol (an appetitive odorant). We have clarified this using new data (Author response image 5).

• It seems to me that Figure 5C is the crux for understanding the potential impact of 5-HT on odor coding, but it is somewhat confusing and underutilized. Is the implication that 5-HT decorrelates spontaneous activity such that when an odor stimulus arrives, the odor-evoked activity deviates to a greater degree? The authors make claims about this figure that require the reader to guess as to the aspect of the figure to which they are referring.

The reviewer makes an astute observation. Yes, the spontaneous activity in the antennal lobe network before serotonin introduction is not correlated with the ensemble spontaneous activity after serotonin bath application. Remarkably, the odor-evoked responses were highly similar, both in the reduced PCA space and when assayed using high-dimensional ensemble neural activity vectors. Whether the changes in network spontaneous activity have a function in odor detection and recognition is not fully understood and cannot be convincingly answered using our data. But this is something that we had pondered.

• The modeling component summarized in Figure 6 needs clarification and more detail. Perhaps example traces associated with positive weighting within neural ensemble 1 relative to neural ensemble 2? I struggled to understand conceptually how the model resolved the theoretical discrepancy between physiology and behavior.

As recommended, here is a plot showing the responses of four PNs that had positive weights to hexanol and linalool. As can be expected, each PN in this group had higher responses to hexanol and no response to linalool. Further, the four PNs that received negative weights had response only to linalool.

Author response image 5.

Odor-evoked responses of four PNs that received positive weights in the model (top panel), and four PNs that were assigned negative weights in the model (bottom).

• Was there a significant difference between the PORs of hungry vs. fed locusts? The authors state that they differ and provide statistics for the comparisons to locusts injected with 5-HT, but then don't provide any statistical analyses of hungry vs. fed animals.

The POR responses to HEX (an appetitive odorant) were significantly different between the hungry and starved locusts.

Author response image 6.

A bar plot summarizing PORs to all four odors for satiated locust (highlighted with stripes), before (dark shade), and after 5HT injection (lighter shade). To allow comparison before 5HT injection for starved locust plotted as well (without stripes). The significance was determined using a one-tailed paired-sample ttest(*p<0.05).

• Were any of the effects of 5-HT on odor-evoked PN responses significant? No statistics are provided.

We examined the distribution of odor-evoked responses in PNs before and after 5HT introduction. We found that the overall distribution was not significantly different between the two (one-tailed pairedsample t-test; p = 0.93).

Author response image 7.

Comparison of the distribution of odor-evoked PN responses before (green) and after (purple) 5HT introduction. One-tailed paired sample t-test was used to compare the two distributions.

• The authors interchangeably use "serotonin", "5HT" and "5-HT" throughout the manuscript, but this should be consistent.

This has been fixed in the revised manuscript.

• On page 2 the authors provide an ecological relevance for linalool as being an additive in pesticides, however, linalool is a common floral volatile chemical. Is the implication that locusts have learned to associate linalool with pesticides?

Linalool is a terpenoid alcohol that has a floral odor but has also been used as a pesticide and insect repellent [Beier et al., 2014]. As shown in Author response image 2, it evoked the least POR responses amongst a diverse panel of 22 odorants that were tested. We have clarified how we chose odorants based on the prior dataset in the Methods section.

• In Figure 1, there should be a legend in the figure itself indicating that the black box indicates the absence of POR and the white box indicates presence, rather than just having it in the legend text.

Done.

• In Figure 2, the raw data from each animal can be moved to the supplements. The way it is presented is overwhelming and the order of comparisons is difficult to follow.

Done.

• For the induction of bursting in PNs by the application of 5-HT, were there any other metrics observed such as period, duration of bursts, or peak burst frequency? The authors rely on ISI, but there are other bursting metrics that could also be included to understand the nature of this observation. In particular, whether the bursts are likely due to changes in intrinsic biophysical properties of the PNs or polysynaptic effects.

We could use other metrics as the reviewer suggests. Our main point is that the spontaneous activity of individual PNs changed. We have added a new current-injection experiments to show that the PNs output to square pulses of current becomes different after serotonin application (Author response image 1)

• Were 4-vinyl anisole, 1-nonanol, and octanoic acid selected as additional odors because they had particular ecological relevance, or was it for the diversity of chemical structure?

These odorants were selected based on both, chemical structure and ecological relevance. The logic behind this was to have a very diverse odor panel that consisted of food odorant – Hexanol, aggregation pheromone – 4-vinyl anisole, sex pheromone – benzaldehyde, acid – octanoic acid, base – ammonium, and alcohol – 1-nonanol. Additionally, we selected these odors based on previous neural and behavioral data on these odorants (Chandak and Raman, 2023, Traner and Raman, 2023, Nizampatnam et al, 2022 & 2018; Saha et al., 2017 & 2013).

Reviewer #2 (Recommendations For The Authors):

The electrophysiology dataset combines all performed experiments across all tested different PN-odor pairs. How many odors have been tested in a single PN and how many PNs have been tested for a single odor? This information is not present in the current manuscript. Can the authors exclude that there are odor-specific modulations?

In total, our dataset includes recordings from 19 PNs. Seven PNs were tested on a panel of seven odorants (4-vinyl anisole, 1-nonanol, octanoic acid, Hex, Bza, Lool, and Amn), and the remaining twelve were tested with the four main odorants used in the study (Hex, Bza, Lool, and Amn). This information has been added to the Methods section

How did the authors choose the concentrations of serotonin injections and bath applications - is this a naturalistic amount?

The serotonin concentration for ephys experiments was chosen based on trial-error experiments:

0.01mM was the highest concentration that did not cause cell death. For the behavioral experiments, we increased the concentration (0.1 M) due to the presence of anatomical structures in the locust's head such as air sacks, sheath as well as hemolymph which causes some degree of dilution that we cannot control.

Behavior experiments were performed 3 hours after injection - ephys experiments 5-10 minutes following bath application. Can the authors exclude that serotonin affects neural processing differently on these different timescales?

We cannot exclude this possibility. We did ePhys experiments 5-10 minutes after bath application as it would be extremely hard to hold cells for that long.

A longer delay was required for our behavioral experiments as the locusts tended to be a bit more agitated with larger spontaneous movements of palps as well as exhibited unprompted vomiting. A 3hour period allowed the locust to regain its baseline level movements after 5HT introduction. [This information has been added to the methods section of the revised manuscript]

Concerning the analysis of electrophysiological data. The authors should correct for changes in the baseline before performing PCA analysis. And how much of the variance is explained by PC1 and PC2?

We did not correct for baseline changes or subtract baseline as we wanted to show that the odor-evoked neural responses still robustly encoded information about the identity of the odorant.

The authors should perform dye injections after recordings to visualize the cell type they recorded from. Serotonin might affect also other cell types in the antennal lobe.

As mentioned above, in the locust antennal lobe only PNs fire full-blown sodium spikes, and LNs only fire calcium spikelets (Author response image 4). Since these signals are small, they will be buried under the noise floor when using extracellular recording electrodes for monitoring responses in the AL antennal lobe.

Hence we are pretty certain what type of cells we are recording from.

There were several typos in the manuscript, please check again.

We have fixed many of the grammatical errors and typos in the revised version.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

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

Strengths

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

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

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

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

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

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

Weaknesses

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

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

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

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

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

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

Author response image 1.

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

We modified the text to clarify these points:

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

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

Reviewer #2 (Public Review):

Summary:

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

Strengths:

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

We thank the Reviewer for the summary and comments.

Weaknesses:

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

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

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

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

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

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

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

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

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

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

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

Reviewer #3 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

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

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Classifier:

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

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

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

Normalization Model:

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

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

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

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

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

Two-Direction Experiment:

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

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

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

Reviewer #2 (Recommendations For The Authors):

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

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

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

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

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

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

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

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

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

Reviewer #3 (Recommendations For The Authors):

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

We thank the Reviewer for the comments.

Specific suggestions:

(1) Intro para 3

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

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

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

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

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

(2) Analysis clarifications

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

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

We have clarified these points on page 13.

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

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

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

(3) Figure 5

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

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

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

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

𝑅_e = 𝑎𝑅_f + (1 − 𝑎)𝑅_s,

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

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

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

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

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

(4) Figure 7

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

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

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

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

(5) Attention task

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

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

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

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

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

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

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

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

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

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

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

Author Response

We would like to thank the Editors and Reviewers for their comprehensive review of the manuscript. We appreciate your feedback, and we will carefully consider all your comments in the revision of the manuscript. Below are our provisional responses to your comments.

eLife assessment

This manuscript reveals important insights into the role of ipsilateral descending pathways in locomotion, especially following unilateral spinal cord injury. The study provides solid evidence that this method improves the injured side's ability to support weight, and as such the findings may lead to new treatments for stroke, spinal cord injuries, or unilateral cerebral injuries. However, the methods and results need to be better detailed, and some of the statistical analysis enhanced.

Thank you for your assessment. We will incorporate various textual enhancements in the final version of the manuscript to address the weaknesses you have pointed out. The specific improvements are outlined below.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This manuscript provides potentially important new information about ipsilateral cortical impact on locomotion. A number of issues need to be addressed.

Strengths:

The primary appeal and contribution of this manuscript are that it provides a range of different measures of ipsilateral cortical impact on locomotion in the setting of impaired contralateral control. While the pathways and mechanisms underlying these various measures are not fully defined and their functional impacts remain uncertain, they comprise a rich body of results that can inform and guide future efforts to understand cortical control of locomotion and to develop more effective rehabilitation protocols.

Weaknesses:

1. The authors state that they used a cortical stimulation location that produced the largest ankle flexion response (lines 102-104). Did other stimulation locations always produce similar, but smaller responses (aside from the two rats that showed ipsilateral neuromodulation)? Was there any site-specific difference in response to stimulation location?

We derived motor maps in each rat, akin to the representation depicted in Fig 6. In each rat, alternative cortical sites did, indeed, produce distal or proximal contralateral leg flexion responses. Distal responses were more likely to be evoked in the rostral portion of the array, similarly to proximal responses early after injury. This distribution in responses across different cortical sites is reported in this study (Fig. 6) and is consistent with our prior work. The Results section will be revised to provide additional clarification and context for the data presented in Figure 6.

1. Figure 2: There does not appear to be a strong relationship between the percentage of spared tissue and the ladder score. For example, the animal with the mild injury (based on its ladder score) in the lower left corner of Figure 2A has less than 50% spared tissue, which is less spared tissue than in any animal other than the two severe injuries with the most tissue loss. Is it possible that the ladder test does not capture the deficits produced by this spinal cord injury? Have the authors looked for a region of the spinal cord that correlates better with the deficits that the ladder test produces? The extent of damage to the region at the base of the dorsal column containing the corticospinal tract would be an appropriate target area to quantify and compare with functional measures.

In Fig. S6 of our 2021 publication "Bonizzato and Martinez, Science Translational Medicine", we investigated the predictive value of tissue sparing in specific sub-regions of the spinal cord for ladder performance. Specifically, we examined the correlation between the accuracy of left leg ladder performance in the acute state and the preservation of the corticospinal tract (CST). Our results indicated that dorsal CST sparing serves as a mild predictor for ladder deficits, confirming the results obtain in this study.

1. Lines 219-221: The authors state that "phase-coherent stimulation reinstated the function of this muscle, leading to increased burst duration (90{plus minus}18% of the deficit, p=0.004, t-test, Fig. 4B) and total activation (56{plus minus}13% of the deficit, p=0.014, t-test, Fig. 3B). This way of expressing the data is unclear. For example, the previous sentence states that after SCI, burst duration decreased by 72%. Does this mean that the burst duration after stimulation was 90% higher than the -72% level seen with SCI alone, i.e., 90% + -72% = +18%? Or does it mean that the stimulation recovered 90% of the portion of the burst duration that had been lost after SCI, i.e., -72% * (100%-90%)= -7%? The data in Figure 4 suggests the latter. It would be clearer to express both these SCI alone and SCI plus stimulation results in the text as a percent of the pre-SCI results, as done in Figure 4.

Your assessment is correct; we intended to report that the stimulation recovered 90% of the portion of the burst duration that had been lost after SCI. This point will be addressed in the revision of the manuscript.

1. Lines 227-229: The authors claim that the phase-dependent stimulation effects in SCI rats are immediate, but they don't say how long it takes for these effects to be expressed. Are these effects evident in the response to the first stimulus train, or does it take seconds or minutes for the effects to be expressed? After the initial expression of these effects, are there any gradual changes in the responses over time, e.g., habituation or potentiation?

The effects are immediately expressed at the very first occurrence of stimulation. We never tested a rat completely naïve to stimuli, as each treadmill session involves prior cortical mapping to identify a suitable active site for involvement in locomotor experiments. Yet, as demonstrated in Supplementary Video 1 accompanying our 2021 publication on contralateral effects of cortical stimulation, "Bonizzato and Martinez, Science Translational Medicine," the impact of phase-dependent cortical stimulation on movement modulation is instantaneous and ceases promptly upon discontinuation of the stimulation. We did not quantify potential gradual changes in responsiveness over time, but we cannot exclude that for long stimulation sessions (e.g., 30 min or more), stimulus amplitude may need to be slightly increased over time to compensate habituation.

1. Awake motor maps (lines 250-277): The analysis of the motor maps appears to be based on measurements of the percentage of channels in which a response can be detected. This analytic approach seems incomplete in that it only assesses the spatial aspect of the cortical drive to the musculature. One channel could have a just-above-threshold response, while another could have a large response; in either case, the two channels would be treated as the same positive result. An additional analysis that takes response intensity into account would add further insight into the data, and might even correlate with the measures of functional recovery. Also, a single stimulation intensity was used; the results may have been different at different stimulus intensities.

We confirm that maps of cortical stimulation responsiveness may vary at different stimulus amplitudes. To establish an objective metric of excitability, we identified 100µA as a reliable stimulation amplitude across rats and used this value to build the ipsilateral motor representation results in Figure 6. This choice allows direct comparison with Figure 6 of our 2021 article, related to contralateral motor representation. The comparison reveals a lack of correlation with functional recovery metrics in the ipsilateral case, in contrast to the successful correlation achieved in the contralateral case.

Regarding the incorporation of stimulation amplitudes into the analysis, as detailed in the Method section (lines 770-771), we systematically tested various stimulation amplitudes to determine the minimal threshold required for eliciting a muscle twitch, identified as the threshold value. This process was conducted for each electrode site. Upon reviewing these data, we considered the possibility of presenting an additional assessment of ipsilateral cortical motor representation based on stimulation thresholds. However, the representation depicted in the figure did not differ significantly from the data presented in Figure 6A. Furthermore, this representation introduced an additional weakness, as it was unclear how to represent the absence of a response in the threshold scale. We chose to arbitrarily designate it as zero on the inverse logarithmic scale, where, for reference, 100 µA is positioned at 0.2 and 50 µA at 0.5.

In conclusion, we believe that the conclusions drawn from this analysis align substantially with those in the text. The addition of the threshold analysis, in our assessment, would not contribute significantly to improving the manuscript.

Author response image 1.

Threshold analysis

Author response image 2.

Original occurrence probability analysis, for comparison.

1. Lines 858-860: The authors state that "All tests were one-sided because all hypotheses were strictly defined in the direction of motor improvement." By using the one-sided test, the authors are using a lower standard for assessing statistical significance that the overwhelming majority of studies in this field use. More importantly, ipsilateral stimulation of particular kinds or particular sites might conceivably impair function, and that is ignored if the analysis is confined to detecting improvement. Thus, a two-sided analysis or comparable method should be used. This appropriate change would not greatly modify the authors' current conclusions about improvements.

Our original hypothesis, drawn from previous studies involving cortical stimulation in rats and cats, as well as other neurostimulation research for movement restoration, posited a favorable impact of neurostimulation on movement. Consistent with this hypothesis, we designed our experiments with a focus on enhancing movement, emphasizing a strict direction of improvement.

It's important to note that a one-sided test is the appropriate match for a one-sided hypothesis, and it is not a lower standard in statistics. Each experiment we conducted was constructed around a strictly one-sided hypothesis: the inclusion of an extensor-inducing stimulus would enhance extension, and the inclusion of a flexion-inducing stimulus would enhance flexion. This rationale guided our choice of the appropriate statistical test.

We acknowledge your concern regarding the potential for ipsilateral stimulation to have negative effects on locomotion, which might not be captured when designing experiments based on one-sided hypotheses. This concern is valid, and we will explicitly mention it in the statistics section. Nonetheless, even if such observations were made, they could serve as the basis for triggering an ad-hoc follow-up study.

Reviewer #2 (Public Review):

Summary:

The authors' long-term goals are to understand the utility of precisely phased cortex stimulation regimes on recovery of function after spinal cord injury (SCI). In prior work, the authors explored the effects of contralesion cortex stimulation. Here, they explore ipsilesion cortex stimulation in which the corticospinal fibers that cross at the pyramidal decussation are spared. The authors explore the effects of such stimulation in intact rats and rats with a hemisection lesion at the thoracic level ipsilateral to the stimulated cortex. The appropriately phased microstimulation enhances contralateral flexion and ipsilateral extension, presumably through lumbar spinal cord crossed-extension interneuron systems. This microstimulation improves weight bearing in the ipsilesion hindlimb soon after injury, before any normal recovery of function would be seen. The contralateral homologous cortex can be lesioned in intact rats without impacting the microstimulation effect on flexion and extension during gait. In two rats ipsilateral flexion responses are noted, but these are not clearly demonstrated to be independent of the contralateral homologous cortex remaining intact.

Strengths:

This paper adds to prior data on cortical microstimulation by the laboratory in interesting ways. First, the strong effects of the spared crossed fibers from the ipsi-lesional cortex in parts of the ipsi-lesion leg's step cycle and weight support function are solidly demonstrated. This raises the interesting possibility that stimulating the contra-lesion cortex as reported previously may execute some of its effects through callosal coordination with the ipsi-lesion cortex tested here. This is not fully discussed by the authors but may represent a significant aspect of these data. The authors demonstrate solidly that ablation of the contra-lesional cortex does not impede the effects reported here. I believe this has not been shown for the contra-lesional cortex microstimulation effects reported earlier, but I may be wrong. Effects and neuroprosthetic control of these effects are explored well in the ipsi-lesion cortex tests here.

In the revised version of the manuscript, we will incorporate various text improvements to address the points you have highlighted below. Additionally, we will integrate the suggested discussion topic on callosal coordination related to contralateral cortical stimulation.

Weaknesses:

Some data is based on very few rats. For example (N=2) for ipsilateral flexion effects of microstimulation. N=3 for homologous cortex ablation, and only ipsi extension is tested it seems. There is no explicit demonstration that the ipsilateral flexion effects in only 2 rats reported can survive the contra-lateral cortex ablation. We agree with this assessment. The ipsilateral flexion representation is here reported as a rare but consistent phenomenon, which we believe to have robustly described with Figure 7 experiments. We will underline in the text that the ablation experiment did not conclude on the unilateral-cortical nature of ipsilateral flexion effects.

Some improvements in clarity and precision of descriptions are needed, as well as fuller definitions of terms and algorithms.

Likely Impacts: This data adds in significant ways to prior work by the authors, and an understanding of how phased stimulation in cortical neuroprosthetics may aid in recovery of function after SCI, especially if a few ambiguities in writing and interpretation are fully resolved.

The manuscript text will be revised in its final version, and we seek to eliminate any ambiguity in writing, data interpretation and algorithms.

Reviewer #3 (Public Review):

Summary:

This article aims to investigate the impact of neuroprosthesis (intracortical microstimulation) implanted unilaterally on the lesion side in the context of locomotor recovery following unilateral thoracic spinal cord injury.

Strength:

The study reveals that stimulating the left motor cortex, on the same side as the lesion, not only activates the expected right (contralateral) muscle activity but also influences unexpected muscle activity on the left (ipsilateral) side. These muscle activities resulted in a substantial enhancement in lift during the swing phase of the contralateral limb and improved trunk-limb support for the ipsilateral limb. They used different experimental and stimulation conditions to show the ipsilateral limb control evoked by the stimulation. This outcome holds significance, shedding light on the engagement of the "contralateral projecting" corticospinal tract in activating not only the contralateral but also the ipsilateral spinal network.

The experimental design and findings align with the investigation of the stimulation effect of contralateral projecting corticospinal tracts. They carefully examined the recovery of ipsilateral limb control with motor maps. They also tested the effective sites of cortical stimulation. The study successfully demonstrates the impact of electrical stimulation on the contralateral projecting neurons on ipsilateral limb control during locomotion, as well as identifying important stimulation spots for such an effect. These results contribute to our understanding of how these neurons influence bilateral spinal circuitry. The study's findings contribute valuable insights to the broader neuroscience and rehabilitation communities.

Thank you for your assessment of this manuscript. The final version of the manuscript will incorporate your suggestions for improving term clarity and will also enhance the discussion on the mechanism of spinal network engagement, as outlined below.

Weakness:

The term "ipsilateral" lacks a clear definition in the title, abstract, introduction, and discussion, potentially causing confusion for the reader. In the next revision of the manuscript, we will provide a clear definition of the term "ipsilateral."

The unexpected ipsilateral (left) muscle activity is most likely due to the left corticospinal neurons recruiting not only the right spinal network but also the left spinal network. This is probably due to the joint efforts of the neuroprosthesis and activation of spinal motor networks which work bilaterally at the spinal level. However, in my opinion, readers can easily link the ipsilateral cortical network to the ipsilateral-projecting corticospinal tract, which is less likely to play a role in ipsilateral limb control in this study since this tract is disrupted by the thoracic spinal injury.

We agree with your assessment. The discussion section paragraph presenting putative mechanisms of cortico-spinal transmission in the effects presented in the results will be enhanced to reflect these suggestions.

Author Response

Reviewer #1 (Public Review):

The authors introduce a computational model that simulates the dendrites of developing neurons in a 2D plane, subject to constraints inspired by known biological mechanisms such as diffusing trophic factors, trafficked resources, and an activity-dependent pruning rule. The resulting arbors are analyzed in terms of their structure, dynamics, and responses to certain manipulations. The authors conclude that 1) their model recapitulates a stereotyped timecourse of neuronal development: outgrowth, overshoot, and pruning 2) Neurons achieve near-optimal wiring lengths, and Such models can be useful to test proposed biological mechanisms- for example, to ask whether a given set of growth rules can explain a given observed phenomenon - as developmental neuroscientists are working to understand the factors that give rise to the intricate structures and functions of the many cell types of our nervous system.

Overall, my reaction to this work is that this is just one instantiation of many models that the author could have built, given their stated goals. Would other models behave similarly? This question is not well explored, and as a result, claims about interpreting these models and using them to make experimental predictions should be taken warily. I give more detailed and specific comments below.

We thank the reviewer for the summary of the work. We find the criticism “that this is one instantiation of many models [we] could have built” can apply to any model. To quote George Box, “all models are wrong, but some models are useful” was the moto that drove our modeling approach. In principle, there are infinitely many possible models. We chose one of the most minimalistic models which implements known biological mechanisms including activity-independent and -dependent phases of dendritic growth, and constrained parameters based on experimental data. We compare the proposed model to other alternatives in the Discussion section, especially to the models of Hermann Cuntz which propose very different strategies for growth.

However, the reviewer is right that within the type of model we chose, we could have more extensively explored the sensitivity to parameters. In the revised manuscript we will investigate the sensitivity of model output to variations of specific parameters, as explained below.

Point 1.1. Line 109. After reading the rest of the manuscript, I worry about the conclusion voiced here, which implies that the model will extrapolate well to manipulations of all the model components. How were the values of model parameters selected? The text implies that these were selected to be biologically plausible, but many seem far off. The density of potential synapses, for example, seems very low in the simulations compared to the density of axons/boutons in the cortex; what constitutes a potential synapse? The perfect correlations between synapses in the activity groups is flawed, even for synapses belonging to the same presynaptic cell. The density of postsynaptic cells is also orders of magnitude of, etc. Ideally, every claim made about the model's output should be supported by a parameter sensitivity study. The authors performed few explorations of parameter sensitivity and many of the choices made seem ad hoc.

It is indeed important to clarify how the model parameters were selected. Here we provide a short justification for some of these parameters, which will be included in the revised manuscript.

1) Potential synapse density: We modelled 1,500 potential synapses in a cortical sheet of size 185x185 microns squared. We used 1 pixel per μm to capture approximately 1 μm thick dendrites. Therefore, we started with initial density of 0.044 potential synapses per μm^2. From Author Response Image 1 we can see that at the end of our simulation time ~1,000 potential synapses remain. So in fact, the density of potential synapses is totally sufficient, since not many potential synapses end up connected. The rapid slowing down of growth in our model is not due to a depletion of potential synaptic partners as the number of potential synapses remains high. Nonetheless, we will explore this in the revised manuscript. (this figure will be included in the revised submission):

2) Stabilized synapse density: Since ~1,000 of the potential synapses in the modeled cortical sheet remain available, ~500 become connected to the dendrites of the 9 somas in the modeled cortical sheet. This means that the density of stable connected synapses is approximately 0.015 synapses per μm^2. This is also the number that is shown in Figure 3b, which is about 60 synapses stabilized per cell. This density is much easier to compare to experimental data, and below we provide some numbers from literature we already cited in the manuscript as well as a recent preprint.

In the developing cortex:

• Leighton, Cheyne and Lohmann 2023 https://doi.org/10.1101/2023.03.02.530772 find up to 0.4 synapses per μm in pyramidal neurons in vivo in the developing mouse visual cortex at P8 to P13. This is almost identical to our value of 0.4 synapses per μm.

• Ultanir et al., 2007 https://doi.org/10.1073/pnas.0704031104 find 0.7 to 1.7 spines per μm in pyramidal neurons in vivo in L2/3 of the developing mouse cortex, at P10 to P20.

• Glynn et al., 2011 https://doi.org/10.1038/nn.2764 find 0.1 to 0.7 spines per μm^2 in pyramidal neurons in vivo and in vitro in L2/3 of the developing mouse cortex, at P8 to P60.

In the developing hippocampus:

• Yang et al., 2014 https://doi.org/10.1016/j.celrep.2014.03.040 find 0.75 to 1 spines per μm in pyramidal neurons in vivo in CA1 of the developing mouse hippocampus, at one month of age.

• Koshimizu et al., 2009 https://doi.org/10.1186/1756-6606-2-27 find 0.1 to 0.4 spines per μm in pyramidal neurons in slice in the developing rat hippocampus, at (Embryonic Day) ED18 to ED20.

• Tyler and Pozzo-Miller, 2001 https://doi.org/10.1523/JNEUROSCI.21-12-04249.2001 find 0.28 to 0.1 spines per μm in slice in the developing mouse hippocampus, at P7 (14 DIV, days in vitro).

Although these values vary somewhat across experiments, in most cases they are in agreement with our chosen values, especially when taking into account that we are modeling development (rather than adulthood).

3) Soma/neuron density: Indeed, we did not exactly mention this number anywhere in the paper. But from the figures we can infer 9 somas growing dendrites on an area of ~34,000 μm^2. Thus, neuron density would be 300 neurons per mm^2. This number seems a bit low after a short search through the literature. For e.g. Keller et al., 2018 https://www.frontiersin.org/articles/10.3389/fnana.2018.00083/full reports about 90,000 neurons per mm^3, albeit in adulthood.

We are also performing a sensitivity analysis where some of these parameters are varied and will include this in the revised manuscript. In particular:

(1) We will vary the nature of the input correlations. In the current model, the synapses in each correlated group receive spike trains with a perfect correlation and there are no correlations across the groups. We will reduce the correlations within group and add non-zero correlations across the groups.

(2) We will vary the density of the neuronal somas. We expect that higher densities of somas will either yield smaller dendritic areas because the different neurons compete more or result in a state where nearby neurons have to complement each other regarding their activity preferences.

(3) We will introduce dynamics in the potential synapses to model the dynamics of axons. We plan to explore several scenarios. We could introduce a gradual increase in the density of potential synapses and implement a cap on the number of synapses that can be alive at the same time, and vary that cap. We could also introduce a lifetime of each synapse (following for example a lognormal distribution). A potential synapse can disappear if it does not form a stable synapse in its lifetime, in which case it could move to a different location.

Point 1.2. Many potentially important phenomena seem to be excluded. I realize that no model can be complete, but the choice of which phenomena to include or exclude from this model could bias studies that make use of it and is worth serious discussion. The development of axons is concurrent with dendrite outgrowth, is highly dynamic, and perhaps better understood mechanistically. In this model, the inputs are essentially static. Growing dendrites acquire and lose growth cones that are associated with rapid extension, but these do not seem to be modeled. Postsynaptic firing does not appear to be modeled, which may be critical to activity-dependent plasticity. For example, changes in firing are a potential explanation for the global changes in dendritic pruning that occur following the outgrowth phase.

As the reviewer concludes, no model can be complete. In agreement with this, here we would like to quote a paragraph from a very nice paper by Larry Abbott (“Theoretical Neuroscience Rising, Neuron 2008 https://www.sciencedirect.com/science/article/pii/S0896627308008921) which although published more than 10 years ago, still applies today:

“Identifying the minimum set of features needed to account for a particular phenomenon and describing these accurately enough to do the job is a key component of model building. Anything more than this minimum set makes the model harder to understand and more difficult to evaluate. The term ‘‘realistic’’ model is a sociological rather than a scientific term. The truly realistic model is as impossible and useless a concept as Borges’ ‘‘map of the empire that was of the same scale as the empire and that coincided with it point for point’’ (Borges, 1975). […] The art of modeling lies in deciding what this subset should be and how it should be described.”

We have clearly stated in the Introduction (e.g. lines 37-75) which phenomena we include in the model and why. The Discussion also compares our model to others (lines 315-373), pointing out that most models either focus on activity-independent or activity-dependent phases. We include both, combining literature on molecular gradients and growth factors, with activity-dependent connectivity refinements instructed by spontaneous activity. We could not think of a more tractable, more minimalist model that would include both activity-independent or activity-dependent aspects. Therefore, we feel that the current manuscript provides sufficient motivation but also a discussion of limitations of the current model.

Regarding including the concurrent development of axons, we agree this is very interesting and currently not addressed in the model. As noted at the bottom of our reply to point 1.1, bullet (3) we are now revising the manuscript to include a simplified form of axonal dynamics by allowing changes in the lifetime and location of potential synapses, which come from axons of presynaptic partners.

Regarding postsynaptic firing, this is indeed super relevant and an important point to consider. In one of our recent publications (Kirchner and Gjorgjieva, 2021 https://www.nature.com/articles/s41467-021-23557-3), we studied only an activity-dependent model for the organization of synaptic inputs on non-growing dendrites which have a fixed length. There, we considered the effect of postsynaptic firing and demonstrated that it plays an important role in establishing a global organization of synapses on the entire dendritic tree of the neuron, and not just local dendritic branches. For example, we showed that could that it could lead to the emergence of retinotopic maps which have been found experimentally (Iacaruso et al., 2017 https://www.nature.com/articles/nature23019). Since we use the same activity-dependent plasticity model in this paper, we expect that the somatic firing will have the same effect on establishing synaptic distributions on the entire dendritic tree. We will make a note of this in the Discussion in the revised paper.

Point 1.3. Line 167. There are many ways to include activity -independent and -dependent components into a model and not every such model shows stability. A key feature seems to be that larger arbors result in reduced growth and/or increased retraction, but this could be achieved in many ways (whether activity dependent or not). It's not clear that this result is due to the combination of activity-dependent and independent components in the model, or conceptually why that should be the case.

We never argued for model uniqueness. There are always going to be many different models (at different spatial and temporal scales, at different levels of abstraction). We can never study all of them and like any modeling study in systems neuroscience we have chosen one model approach and investigated this approach. We do compare the current model to others in the Discussion. If the reviewers have a specific implementation that we should compare our model to as an alternative, we could try, but not if this means doing a completely separate project.

Point 1.4. Line 183. The explanation of overshoot in terms of the different timescales of synaptic additions versus activity-dependent retractions was not something I had previously encountered and is an interesting proposal. Have these timescales been measured experimentally? To what extent is this a result of fine-tuning of simulation parameters?

We found that varying the amount of BDNF controls the timescale of the activity-dependent plasticity (see our Figure 5c). Hence, changing the balance between synaptic additions vs. retractions is already explored in Figure 5e and f. Here we show that the overshoot and retraction does not have to be fine-tuned but may be abolished if there is too much activity-dependent plasticity.

Regarding the relative timescales of synaptic additions vs. retractions: since the first is mainly due to activity-independent factors, and the second due to activity-dependent plasticity, the questions is really about the timescales of the latter two. As we write in the Introduction (lines 60-62), manipulating activity-dependent synaptic transmission has been found to not affect morphology but rather the density and specificity of synaptic connections (Ultanir et al. 2007 https://doi.org/10.1073/pnas.0704031104), supporting the sequential model we have (although we do not impose the sequence, as both activity-independent and activity-dependent mechanisms are always “on”; but note that activity-dependent plasticity can only operate on synapses that have already formed).

Point 1.5. Line 203. This result seems at odds with results that show only a very weak bias in the tuning distribution of inputs to strongly tuned cortical neurons (e.g. work by Arthur Konnerth's group). This discrepancy should be discussed.

First, we note that the correlated activity experienced by our modeled synapses (and resulting synaptic organization) does not necessarily correspond to visual orientation, or any stimulus feature, for that matter.

Nonetheless, this is a very interesting question and there is some variability in what the experimental data show. Many studies have shown that synapses on dendrites are organized into functional synaptic clusters: across brain regions, developmental ages and diverse species from rodent to primate (Kleindienst et al. 2011; Takahashi et al. 2012; Winnubst et al. 2015; Gökçe et al., 2016; Wilson et al. 2016; Iacaruso et al., 2017; Scholl et al., 2017; Niculescu et al. 2018; Kerlin et al. 2019; Ju et al. 2020). Interestingly, some in vivo studies have reported lack of fine-scale synaptic organization (Varga et al. 2011; X. Chen et al. 2011; T.-W. Chen et al. 2013; Jia et al. 2010; Jia et al. 2014), while others reported clustering for different stimulus features in different species. For example, dendritic branches in the ferret visual cortex exhibit local clustering of orientation selectivity but do not exhibit global organization of inputs according to spatial location and receptive field properties (Wilson et al. 2016; Scholl et al., 2017). In contrast, synaptic inputs in mouse visual cortex do not cluster locally by orientation, but only by receptive field overlap, and exhibit a global retinotopic organization along the proximal-distal axis (Iacaruso et al., 2017). We proposed a theoretical framework to reconcile these data: combining activity-dependent plasticity similar to the BDNF-proBDNF model that we used in the current work, and a receptive field model for the different species (Kirchner and Gjorgjieva, 2021 https://www.nature.com/articles/s41467-021-23557-3). We can mention this aspect in the revised manuscript.

Point 1.6. Line 268. How does the large variability in the size of the simulated arbors relate to the relatively consistent size of arbors of cortical cells of a given cell type? This variability suggests to me that these simulations could be sensitive to small changes in parameters (e.g. to the density or layout of presynapses).

As noted at the bottom of our reply to point 1.1, bullet (3) we are now revising the manuscript to include changes in the lifetime and location of potential synapses.

Point 1.7. The modeling of dendrites as two-dimensional will likely limit the usefulness of this model. Many phenomena- such as diffusion, random walks, topological properties, etc - fundamentally differ between two and three dimensions.

The reviewer is right about there being differences between two and three dimensions. But a simpler model does not mean a useless model even if not completely realistic. We have ongoing work that extends the current model to 3D but is beyond the scope of the current paper. In systems neuroscience, people have found very interesting results making such simplified geometric assumptions about networks, for instance the one-dimensional ring model has been used to uncover fundamental insights about computations even though highly simplified and abstracted.

Point 1.8. The description of wiring lengths as 'approximately optimal' in this text is problematic. The plotted data show that the wiring lengths are several deviations away from optimal, and the random model is not a valid instantiation of the 2D non-overlapping constraints the authors imposed. A more appropriate null should be considered.

We did not use the term “optimal” in line with previous literature. We wrongly referred to the minimal wiring length as the optimal wiring length, but neurons can optimize their wiring not only by minimizing their dendritic length (e.g. work of Hermann Cuntz). In the revised manuscript, we will replace the term “optimal wiring” with “minimal wiring”. Then we will compare the wiring length in the model with the theoretically minimal wiring length, the random wiring length and the actual data.

Point 1.9. It's not clear to me what the authors are trying to convey by repeatedly labeling this model as 'mechanistic'. The mechanisms implemented in the model are inspired by biological phenomena, but the implementations have little resemblance to the underlying biophysical mechanisms. Overall my impression is that this is a phenomenological model intended to show under what conditions particular patterns are possible. Line 363, describing another model as computational but not mechanistic, was especially unclear to me in this context.

What we mean by mechanistic is that we implement equations that model specific mechanisms i.e. we have a set of equations that implement the activity-independent attraction to potential synapses (with parameters such as the density of synapses, their spatial influence, etc) and the activity-dependent refinement of synapses (with parameters such as the ratio of BDNF and proBDNF to induce potentiation vs depression, the activity-dependent conversion of one factor to the other, etc). This is a bottom-up approach where we combine multiple elements together to get to neuronal growth and synaptic organization. This approach is in stark contrast to the so-called top-down or normative approaches where the method would involve defining an objective function (e.g. minimal dendritic length) which depends on a set of parameters and then applying a gradient descent or other mathematical optimization technique to get at the parameters that optimize the objective function. This latter approach we would not call mechanistic because it involves an abstract objective function (who could say what a neuron or a circuit should be trying to optimize) and a mathematical technique for how to optimize the function (we don’t know of neurons can compute gradients of abstract objective functions).

Hence our model is mechanistic, but it does operate at a particular level of abstraction/simplification. We don’t model individual ion channels, or biophysics of synaptic plasticity (opening and closing of NMDA channels, accumulation of proteins at synapses, protein synthesis). We do, however, provide a biophysical implementation of the plasticity mechanism though the BDNF/proBDNF model which is more than most models of plasticity achieve, because they typically model a phenomenological STDP or Hebbian rule that just uses activity patterns to potential or depress synaptic weights, disregarding how it could be implemented.

Reviewer #2 (Public Review):

This work combines a model of two-dimensional dendritic growth with attraction and stabilisation by synaptic activity. The authors find that constraining growth models with competition for synaptic inputs produces artificial dendrites that match some key features of real neurons both over development and in terms of final structure. In particular, incorporating distance-dependent competition between synapses of the same dendrite naturally produces distinct phases of dendritic growth (overshoot, pruning, and stabilisation) that are observed biologically and leads to local synaptic organisation with functional relevance. The approach is elegant and well-explained, but makes some significant modelling assumptions that might impact the biological relevance of the results.

Strengths:

The main strength of the work is the general concept of combining morphological models of growth with synaptic plasticity and stabilisation. This is an interesting way to bridge two distinct areas of neuroscience in a manner that leads to findings that could be significant for both. The modelling of both dendritic growth and distance-dependent synaptic competition is carefully done, constrained by reasonable biological mechanisms, and well-described in the text. The paper also links its findings, for example in terms of phases of dendritic growth or final morphological structure, to known data well.

Weaknesses:

The major weaknesses of the paper are the simplifying modelling assumptions that are likely to have an impact on the results. These assumptions are not discussed in enough detail in the current version of the paper.

1) Axonal dynamics.

A major, and lightly acknowledged, assumption of this paper is that potential synapses, which must come from axons, are fixed in space. This is not realistic for many neural systems, as multiple undifferentiated neurites typically grow from the soma before an axon is specified (Polleux & Snider, 2010). Further, axons are also dynamic structures in early development and, at least in some systems, undergo activity-dependent morphological changes too (O'Leary, 1987; Hall 2000). This paper does not consider the implications of joint pre- and post-synaptic growth and stabilisation.

We thank the reviewer for the summary of the strengths and weaknesses of the work. While we feel that including a full model of axonal dynamics is beyond the scope of the current manuscript, some aspects of axonal dynamics can be included. In a revised model, we will introduce a gradual increase in the density of potential synapses and implement a cap on the number of synapses that can be alive at the same time, and vary that cap. We plan to also introduce a lifetime of each synapse (following for example a lognormal distribution). A potential synapse can disappear if it does not form a stable synapse in its lifetime, in which case it could move to a different location. See also our reply to reviewer comment 1.1, bullet (3).

2) Activity correlations

On a related note, the synapses in the manuscript display correlated activity, but there is no relationship between the distance between synapses and their correlation. In reality, nearby synapses are far more likely to share the same axon and so display correlated activity. If the input activity is spatially correlated and synaptic plasticity displays distance-dependent competition in the dendrites, there is likely to be a non-trivial interaction between these two features with a major impact on the organisation of synaptic contacts onto each neuron.

We are exploring the amount of correlation (between and within correlated groups) to include in the revised manuscript (see also our reply to reviewer comment 1.1, bullet (1)).

However, previous experimental work, (Kleindienst et al., 2011 https://doi.org/10.1016/j.neuron.2011.10.015) has provided anatomical and functional analyses that it is unlikely that the functional synaptic clustering on dendritic branches is the result of individual axons making more than one synapse (see pg. 1019).

3) BDNF dynamics

The models are quite sensitive to the ratio of BDNF to proBDNF (eg Figure 5c). This ratio is also activity-dependent as synaptic activation converts proBDNF into BDNF. The models assume a fixed ratio that is not affected by synaptic activity. There should at least be more justification for this assumption, as there is likely to be a positive feedback relationship between levels of BDNF and synaptic activation.

The reviewer is correct. We used the BDNF-proBDNF model for synaptic plasticity based on our previous work: Kirchner and Gjorgjieva, 2021 https://www.nature.com/articles/s41467-021-23557-3.

There, we explored only the emergence of functionally clustered synapses on static dendrites which do not grow. In the Methods section (Parameters and data fitting) we justify the choice of the ratio of BDNF to proBDNF from published experimental work. We also performed sensitivity analysis (Supplementary Fig. 1) and perturbation simulations (Supplementary Fig. 3), which showed that the ratio is crucial in regulating the overall amount of potentiation and depression of synaptic efficacy, and therefore has a strong impact on the emergence and maintenance of synaptic organization. Since we already performed all this analysis, we do not expect there will be any differences in the current model which includes dendritic growth, as the activity-dependent mechanism has such a different timescale.

A further weakness is in the discussion of how the final morphologies conform to principles of optimal wiring, which is quite imprecise. 'Optimal wiring' in the sense of dendrites and axons (Cajal, 1895; Chklovskii, 2004; Cuntz et al, 2007, Budd et al, 2010) is not usually synonymous with 'shortest wiring' as implied here. Instead, there is assumed to be a balance between minimising total dendritic length and minimising the tree distance (ie Figure 4c here) between synapses and the site of input integration, typically the soma. The level of this balance gives the deviation from the theoretical minimum length as direct paths to synapses typically require longer dendrites. In the model this is generated by the guidance of dendritic growth directly towards the synaptic targets. The interpretation of the deviation in this results section discussing optimal wiring, with hampered diffusion of signalling molecules, does not seem to be correct.

We agree with this comment. We had wrongly used the term “optimal wiring” as neurons can optimize their wiring not only by minimizing their dendritic length but other factors as noted by the reviewer. In the revised manuscript will replace the term “optimal wiring” with “minimal wiring” and discuss these differences to previous work.

Reviewer #3 (Public Review):

The authors propose a mechanistic model of how the interplay between activity-independent growth and an activity-dependent synaptic strengthening/weaken model influences the dendrite shape, complexity and distribution of synapses. The authors focus on a model for stellate cells, which have multiple dendrites emerging from a soma. The activity independent component is provided by a random pool of presynaptic sites that represent potential synapses and that release a diffusible signal that promotes dendritic growth. Then a spontaneous activity pattern with some correlation structure is imposed at those presynaptic sites. The strength of these synapses follow a learning rule previously proposed by the lab: synapses strengthen when there is correlated firing across multiple sites, and synapses weaken if there is uncorrelated firing with the relative strength of these processes controlled by available levels of BDNF/proBDNF. Once a synapse is weakened below a threshold, the dendrite branch at that site retracts and loses its sensitivity to the growth signal

The authors run the simulation and map out how dendrites and synapses evolve and stabilize. They show that dendritic trees growing rapidly and then stabilize by balancing growth and retraction (Figure 2). They also that there is an initial bout of synaptogenesis followed by loss of synapses, reflecting the longer amount of time it takes to weaken a synapse (Figure 3). They analyze how this evolution of dendrites and synapses depends on the correlated firing of synapses (i.e. defined as being in the same "activity group"). They show that in the stabilized phase, synapses that remain connected to a given dendritic branch are likely to be from same activity group (Figure 4). The authors systemically alter the learning rule by changing the available concentration of BDNF, which alters the relative amount of synaptic strengthening, which in turn affects stabilization, density of synapses and interestingly how selective for an activity group one dendrite is (Figure 5). In addition the authors look at how altering the activity-independent factors influences outgrowth (Figure 6). Finally, one of the interesting outcomes is that the resulting dendritic trees represent "optimal wiring" solutions in the sense that dendrites use the shortest distance given the distribution of synapses. They compare this distribute to one published data to see how the model compared to what has been observed experimentally.

There are many strengths to this study. The consequence of adding the activity-dependent contribution to models of synapto- and dendritogenesis is novel. There is some exploration of parameters space with the motivation of keeping the parameters as well as the generated outcomes close to anatomical data of real dendrites. The paper is also scholarly in its comparison of this approach to previous generative models. This work represented an important advance to our understanding of how learning rules can contribute to dendrite morphogenesis

We thank the reviewer for the positive evaluation of the work and the suggestions below.

Author Response

eLife assessment

This potentially valuable study uses classic neuroanatomical techniques and synchrotron X-ray tomography to investigate the mapping of the trunk within the brainstem nuclei of the elephant brain. Given its unique specializations, understanding the somatosensory projections from the elephant trunk would be of general interest to evolutionary neurobiologists, comparative neuroscientists, and animal behavior scientists. However, the anatomical analysis is inadequate to support the authors' conclusion that they have identified the elephant trigeminal sensory nuclei rather than a different brain region, specifically the inferior olive.

Comment: We are happy that our paper is considered to be potentially valuable. Also, the editors highlight the potential interest of our work for evolutionary neurobiologists, comparative neuroscientists, and animal behavior scientists. The editors are more negative when it comes to our evidence on the identification of the trigeminal nucleus vs the inferior olive. We have five comments on this assessment. (i) We think this assessment is heavily biased by the comments of referee 2. We will show that the referee’s comments are more about us than about our paper. Hence, the referee failed to do their job (refereeing our paper) and should not have succeeded in leveling our paper. (ii) We have no ad hoc knock-out experiments to distinguish the trigeminal nucleus vs the inferior olive. Such experiments (extracellular recording & electrolytic lesions, viral tracing would be done in a week in mice, but they cannot and should not be done in elephants. (iii) We have extraordinary evidence. Nobody has ever described a similarly astonishing match of body (trunk folds) and myeloarchitecture in the trigeminal system before. (iv) We will show that our assignment of the trigeminal nucleus vs the inferior olive is more plausible than the current hypothesis about the assignment of the trigeminal nucleus vs the inferior olive as defended by referee 2. We think this is why it is important to publish our paper. (v) We think eLife is the perfect place for our publication because the deviating views of referee 2 are published along.

Change: We performed additional peripherin-antibody staining to differentiate the inferior olive and trigeminal nucleus. Peripherin is a cytoskeletal protein that is found in peripheral nerves and climbing fibers. Specifically, climbing fibers of various species (mouse, rabbit, pig, cow, and human; Errante et al., 1998) are stained intensely with peripherin-antibodies. What is tricky for our purposes is that there is also some peripherin-antibody reactivity in the trigeminal nuclei (Errante et al., 1998). Such peripherin-antibody reactivity is weaker, however, and lacks the distinct axonal bundle signature that stems from the strong climbing fiber peripherin-reactivity as seen in the inferior olive (Errante et al., 1998). As can be seen in Author response image 1, we observe peripherin-reactivity in axonal bundles (i.e. in putative climbing fibers), in what we think is the inferior olive. We also observe weak peripherin-reactivity, in what we think is the trigeminal nucleus, but not the distinct and strong labeling of axonal bundles. These observations are in line with our ideas but are difficult to reconcile with the views of the referee. Specifically, the lack of peripherin-reactive axon bundles suggests that there are no climbing fibres in what the referee thinks is the inferior olive.

Errante, L., Tang, D., Gardon, M., Sekerkova, G., Mugnaini, E., & Shaw, G. (1998). The intermediate filament protein peripherin is a marker for cerebellar climbing fibres. Journal of neurocytology, 27, 69-84.

Author response image 1.

The putative inferior olive but not the putative trigeminal nucleus contains peripherin-positive axon bundles (presumptive climbing fibers). (A) Overview picture of a brainstem section stained with anti-peripherin-antibodies (white color). Anti-peripherin-antibodies stain climbing fibers in a wide variety of mammals. The section comes from the posterior brainstem of African elephant cow Bibi; in this posterior region, both putative inferior olive and trigeminal nucleus are visible. Note the bright staining of the dorsolateral nucleus, the putative inferior olive according to Reveyaz et al., and the trigeminal nucleus according to Maseko et al., 2013. (B) High magnification view of the dorsolateral nucleus (corresponding to the upper red rectangle in A). Anti-peripherin-positive axon bundles (putative climbing fibers) are seen in support of the inferior olive hypothesis of Reveyaz et al. (C) High magnification view of the ventromedial nucleus (corresponding to the lower red rectangle in A). The ventromedial nucleus is weakly positive for peripherin but contains no anti-peripherin-positive axon bundles (i.e. no putative climbing fibers) in support of the trigeminal nucleus hypothesis of Reveyaz et al. Note that myelin stripes – weakly visible as dark omissions – are clearly anti-peripherin-negative.

Reviewer #1:

Summary:

This fundamental study provides compelling neuroanatomical evidence underscoring the sensory function of the trunk in African and Asian elephants. Whereas myelinated tracts are classically appreciated as mediating neuronal connections, the authors speculate that myelinated bundles provide functional separation of trunk folds and display elaboration related to the "finger" projections. The authors avail themselves of many classical neuroanatomical techniques (including cytochrome oxidase stains, Golgi stains, and myelin stains) along with modern synchrotron X-ray tomography. This work will be of interest to evolutionary neurobiologists, comparative neuroscientists, and the general public, with its fascinating exploration of the brainstem of an icon sensory specialist.

Comment: We are incredibly grateful for this positive assessment.

Changes: None.

Strengths:

• The authors made excellent use of the precious sample materials from 9 captive elephants.

• The authors adopt a battery of neuroanatomical techniques to comprehensively characterize the structure of the trigeminal subnuclei and properly re-examine the "inferior olive".

• Based on their exceptional histological preparation, the authors reveal broadly segregated patterns of metabolic activity, similar to the classical "barrel" organization related to rodent whiskers.

Comment: The referee provides a concise summary of our findings.

Changes: None.

Weaknesses:

• As the authors acknowledge, somewhat limited functional description can be provided using histological analysis (compared to more invasive techniques).

• The correlation between myelinated stripes and trunk fold patterns is intriguing, and Figure 4 presents this idea beautifully. I wonder - is the number of stripes consistent with the number of trunk folds? Does this hold for both species?

Comment: We agree with the referee’s assessment. We note that cytochrome-oxidase staining is an at least partially functional stain, as it reveals constitutive metabolic activity. A significant problem of the work in elephants is that our recording possibilities are limited, which in turn limits functional analysis. As indicated in Figure 4 for the African elephant Indra, there was an excellent match of trunk folds and myelin stripes. Asian elephants have more, and less conspicuous trunk folds than African elephants. As illustrated in Figure 6, Asian elephants have more, and less conspicuous myelin stripes. Thus, species differences in myelin stripes correlate with species differences in trunk folds.

Changes: We clarify the relation of myelin stripe and trunk fold patterns in our discussion of Figure 6.  

Reviewer #2 (Public Review):

The authors describe what they assert to be a very unusual trigeminal nuclear complex in the brainstem of elephants, and based on this, follow with many speculations about how the trigeminal nuclear complex, as identified by them, might be organized in terms of the sensory capacity of the elephant trunk.

Comment: We agree with the referee’s assessment that the putative trigeminal nucleus described in our paper is highly unusual in size, position, vascularization, and myeloarchitecture. This is why we wrote this paper. We think these unusual features reflect the unique facial specializations of elephants, i.e. their highly derived trunk. Because we have no access to recordings from the elephant brainstem, we cannot back up all our functional interpretations with electrophysiological evidence; it is therefore fair to call them speculative.

Changes: None.

The identification of the trigeminal nuclear complex/inferior olivary nuclear complex in the elephant brainstem is the central pillar of this manuscript from which everything else follows, and if this is incorrect, then the entire manuscript fails, and all the associated speculations become completely unsupported.

Comment: We agree.

Changes: None.

The authors note that what they identify as the trigeminal nuclear complex has been identified as the inferior olivary nuclear complex by other authors, citing Shoshani et al. (2006; 10.1016/j.brainresbull.2006.03.016) and Maseko et al (2013; 10.1159/000352004), but fail to cite either Verhaart and Kramer (1958; PMID 13841799) or Verhaart (1962; 10.1515/9783112519882-001). These four studies are in agreement, but the current study differs.

Comment & Change: We were not aware of the papers of Verhaart and included them in the revised ms.

Let's assume for the moment that the four previous studies are all incorrect and the current study is correct. This would mean that the entire architecture and organization of the elephant brainstem is significantly rearranged in comparison to ALL other mammals, including humans, previously studied (e.g. Kappers et al. 1965, The Comparative Anatomy of the Nervous System of Vertebrates, Including Man, Volume 1 pp. 668-695) and the closely related manatee (10.1002/ar.20573). This rearrangement necessitates that the trigeminal nuclei would have had to "migrate" and shorten rostrocaudally, specifically and only, from the lateral aspect of the brainstem where these nuclei extend from the pons through to the cervical spinal cord (e.g. the Paxinos and Watson rat brain atlases), the to the spatially restricted ventromedial region of specifically and only the rostral medulla oblongata. According to the current paper, the inferior olivary complex of the elephant is very small and located lateral to their trigeminal nuclear complex, and the region from where the trigeminal nuclei are located by others appears to be just "lateral nuclei" with no suggestion of what might be there instead.

Comment: We have three comments here:

1) The referee correctly notes that we argue the elephant brainstem underwent fairly major rearrangements. In particular, we argue that the elephant inferior olive was displaced laterally, by a very large cell mass, which we argue is an unusually large trigeminal nucleus. To our knowledge, such a large compact cell mass is not seen in the ventral brain stem of any other mammal.

2) The referee makes it sound as if it is our private idea that the elephant brainstem underwent major rearrangements and that the rest of the evidence points to a conventional ‘rodent-like’ architecture. This is far from the truth, however. Already from the outside appearance (see our Figure 1B and Figure 6A) it is clear that the elephant brainstem has huge ventral bumps not seen in any other mammal. An extraordinary architecture also holds at the organizational level of nuclei. Specifically, the facial nucleus – the most carefully investigated nucleus in the elephant brainstem – has an appearance distinct from that of the facial nuclei of all other mammals (Maseko et al., 2013; Kaufmann et al., 2022). If both the overall shape and the constituting nuclei of the brainstem are very different from other mammals, it is very unlikely if not impossible that the elephant brainstem follows in all regards a conventional ‘rodent-like’ architecture.

3) The inferior olive is an impressive nucleus in the partitioning scheme we propose (Author response image 1). In fact – together with the putative trigeminal nucleus we describe – it’s the most distinctive nucleus in the elephant brainstem. We have not done volumetric measurements and cell counts here, but think this is an important direction for future work. What has informed our work is that the inferior olive nucleus we describe has the serrated organization seen in the inferior olive of all mammals. We will discuss these matters in depth below.

Changes: None.

Such an extraordinary rearrangement of brainstem nuclei would require a major transformation in the manner in which the mutations, patterning, and expression of genes and associated molecules during development occur. Such a major change is likely to lead to lethal phenotypes, making such a transformation extremely unlikely. Variations in mammalian brainstem anatomy are most commonly associated with quantitative changes rather than qualitative changes (10.1016/B978-0-12-804042-3.00045-2).

Comment: We have two comments here:

1) The referee claims that it is impossible that the elephant brainstem differs from a conventional brainstem architecture because this would lead to lethal phenotypes etc. Following our previous response, this argument does not hold. It is out of the question that the elephant brainstem looks very different from the brainstem of other mammals. Yet, it is also evident that elephants live. The debate we need to have is not if the elephant brainstem differs from other mammals, but how it differs from other mammals.

2). In principle we agree with the referee’s thinking that the model of the elephant brainstem that is most likely correct is the one that requires the least amount of rearrangements to other mammals. We therefore prepared a comparison of the model the referee is proposing (Maseko et al., 2013; see Author response table 1 below) with our proposition. We scored these models on their similarity to other mammals. We find that the referee’s ideas (Maseko et al., 2013) require more rearrangements relative to other mammals than our suggestion.

Changes: Inclusion of Author response table 1, which we discuss in depth below.

The impetus for the identification of the unusual brainstem trigeminal nuclei in the current study rests upon a previous study from the same laboratory (10.1016/j.cub.2021.12.051) that estimated that the number of axons contained in the infraorbital branch of the trigeminal nerve that innervate the sensory surfaces of the trunk is approximately 400 000. Is this number unusual? In a much smaller mammal with a highly specialized trigeminal system, the platypus, the number of axons innervating the sensory surface of the platypus bill skin comes to 1 344 000 (10.1159/000113185). Yet, there is no complex rearrangement of the brainstem trigeminal nuclei in the brain of the developing or adult platypus (Ashwell, 2013, Neurobiology of Monotremes), despite the brainstem trigeminal nuclei being very large in the platypus (10.1159/000067195). Even in other large-brained mammals, such as large whales that do not have a trunk, the number of axons in the trigeminal nerve ranges between 400,000 and 500,000 (10.1007/978-3-319-47829-6_988-1). The lack of comparative support for the argument forwarded in the previous and current study from this laboratory, and that the comparative data indicates that the brainstem nuclei do not change in the manner suggested in the elephant, argues against the identification of the trigeminal nuclei as outlined in the current study. Moreover, the comparative studies undermine the prior claim of the authors, informing the current study, that "the elephant trigeminal ganglion ... point to a high degree of tactile specialization in elephants" (10.1016/j.cub.2021.12.051). While clearly, the elephant has tactile sensitivity in the trunk, it is questionable as to whether what has been observed in elephants is indeed "truly extraordinary".

Comment: These comments made us think that the referee is not talking about the paper we submitted, but that the referee is talking about us and our work in general. Specifically, the referee refers to the platypus and other animals dismissing our earlier work, which argued for a high degree of tactile specialization in elephants. We think the referee’s intuitions are wrong and our earlier work is valid.

Changes: We prepared a Author response image 2 (below) that puts the platypus brain, a monkey brain, and the elephant trigeminal ganglion (which contains a large part of the trunk innervating cells) in perspective.

Author response image 2.

The elephant trigeminal ganglion is comparatively large. Platypus brain, monkey brain, and elephant ganglion. The elephant has two trigeminal ganglia, which contain the first-order somatosensory neurons. They serve mainly for tactile processing and are large compared to a platypus brain (from the comparative brain collection) and are similar in size to a monkey brain. The idea that elephants might be highly specialized for trunk touch is also supported by the analysis of the sensory nerves of these animals (Purkart et al., 2022). Specifically, we find that the infraorbital nerve (which innervates the trunk) is much thicker than the optic nerve (which mediates vision) and the vestibulocochlear nerve (which mediates hearing). Thus, not everything is large about elephants; instead, the data argue that these animals are heavily specialized for trunk touch.

But let's look more specifically at the justification outlined in the current study to support their identification of the unusually located trigeminal sensory nuclei of the brainstem.

(1) Intense cytochrome oxidase reactivity.

(2) Large size of the putative trunk module.

(3) Elongation of the putative trunk module.

(4) The arrangement of these putative modules corresponds to elephant head anatomy.

(5) Myelin stripes within the putative trunk module that apparently match trunk folds.

(6) Location apparently matches other mammals.

(7) Repetitive modular organization apparently similar to other mammals.

(8) The inferior olive described by other authors lacks the lamellated appearance of this structure in other mammals.

Comment: We agree those are key issues.

Changes: None.

Let's examine these justifications more closely.

(1) Cytochrome oxidase histochemistry is typically used as an indicative marker of neuronal energy metabolism. The authors indicate, based on the "truly extraordinary" somatosensory capacities of the elephant trunk, that any nuclei processing this tactile information should be highly metabolically active, and thus should react intensely when stained for cytochrome oxidase. We are told in the methods section that the protocols used are described by Purkart et al (2022) and Kaufmann et al (2022). In neither of these cited papers is there any description, nor mention, of the cytochrome oxidase histochemistry methodology, thus we have no idea of how this histochemical staining was done. To obtain the best results for cytochrome oxidase histochemistry, the tissue is either processed very rapidly after buffer perfusion to remove blood or in recently perfusion-fixed tissue (e.g., 10.1016/0165-0270(93)90122-8). Given: (1) the presumably long post-mortem interval between death and fixation - "it often takes days to dissect elephants"; (2) subsequent fixation of the brains in 4% paraformaldehyde for "several weeks"; (3) The intense cytochrome oxidase reactivity in the inferior olivary complex of the laboratory rat (Gonzalez-Lima, 1998, Cytochrome oxidase in neuronal metabolism and Alzheimer's diseases); and (4) The lack of any comparative images from other stained portions of the elephant brainstem; it is difficult to support the justification as forwarded by the authors. The histochemical staining observed is likely background reactivity from the use of diaminobenzidine in the staining protocol. Thus, this first justification is unsupported.

Comment: The referee correctly notes the description of our cytochrome-oxidase reactivity staining was lacking. This is a serious mistake of ours for which we apologize very much. The referee then makes it sound as if we messed up our cytochrome-oxidase staining, which is not the case. All successful (n = 3; please see our technical comments in the recommendation section) cytochrome-oxidase stainings were done with elephants with short post-mortem times (≤ 2 days) to brain removal/cooling and only brief immersion fixation (≤ 1 day). Cytochrome-oxidase reactivity in elephant brains appears to be more sensitive to quenching by fixation than is the case for rodent brains. We think it is a good idea to include a cytochrome-oxidase staining overview picture because we understood from the referee’s comments that we need to compare our partitioning scheme of the brainstem with that of other authors. To this end, we add a cytochrome-oxidase staining overview picture (Author response image 3) along with an alternative interpretation from Maseko et al., 2013.

Changes: 1) We added details on our cytochrome-oxidase reactivity staining protocol and the cytochrome-oxidase reactivity in the elephant brain in general recommendation.

2) We provide a detailed discussion of the technicalities of cytochrome-oxidase staining below in the recommendation section, where the referee raised further criticisms.

3) We include a cytochrome-oxidase staining overview picture (Author response image 2) along with an alternative interpretation from Maseko et al., 2013.

Author response image 3.

Cytochrome-oxidase staining overview along with the Maseko et al. (2013) scheme Left, coronal cytochrome-oxidase staining overview from African elephant cow Indra; the section is taken a few millimeters posterior to the facial nucleus. Brown is putatively neural cytochrome-reactivity, and white is the background. Black is myelin diffraction and (seen at higher resolution, when you zoom in) erythrocyte cytochrome-reactivity in blood vessels (see our Figure 1E-G); such blood vessel cytochrome-reactivity is seen, because we could not perfuse the animal. There appears to be a minimal outside-in-fixation artifact (i.e. a more whitish/non-brownish appearance of the section toward the borders of the brain). This artifact is not seen in sections from Indra that we processed earlier or in other elephant brains processed at shorter post-mortem/fixation delays (see our Figure 1C). Right, coronal partitioning scheme of Maseko et al. (2013) for the elephant brainstem at an approximately similar anterior-posterior level.

The same structures can be recognized left and right. The section is taken at an anterior-posterior level, where we encounter the trigeminal nuclei in pretty much all mammals. Note that the neural cytochrome reactivity is very high, in what we refer to as the trigeminal-nuclei-trunk-module and what Maseko et al. refer to as inferior olive. Myelin stripes can be recognized here as white omissions.

At the same time, the cytochrome-oxidase-reactivity is very low in what Maseko et al. refer to as trigeminal nuclei. The indistinct appearance and low cytochrome-oxidase-reactivity of the trigeminal nuclei in the scheme of Maseko et al. (2013) is unexpected because trigeminal nuclei stain intensely for cytochrome-oxidase-reactivity in most mammals and because the trigeminal nuclei represent the elephant’s most important body part, the trunk. Staining patterns of the trigeminal nuclei as identified by Maseko et al. (2013) are very different at more posterior levels; we will discuss this matter below.

Justifications (2), (3), and (4) are sequelae from justification (1). In this sense, they do not count as justifications, but rather unsupported extensions.

Comment: These are key points of our paper that the referee does not discuss.

Changes: None.

(4) and (5) These are interesting justifications, as the paper has clear internal contradictions, and (5) is a sequelae of (4). The reader is led to the concept that the myelin tracts divide the nuclei into sub-modules that match the folding of the skin on the elephant trunk. One would then readily presume that these myelin tracts are in the incoming sensory axons from the trigeminal nerve. However, the authors note that this is not the case: "Our observations on trunk module myelin stripes are at odds with this view of myelin. Specifically, myelin stripes show no tapering (which we would expect if axons divert off into the tissue). More than that, there is no correlation between myelin stripe thickness (which presumably correlates with axon numbers) and trigeminal module neuron numbers. Thus, there are numerous myelinated axons, where we observe few or no trigeminal neurons. These observations are incompatible with the idea that myelin stripes form an axonal 'supply' system or that their prime function is to connect neurons. What do myelin stripe axons do, if they do not connect neurons? We suggest that myelin stripes serve to separate rather than connect neurons." So, we are left with the observation that the myelin stripes do not pass afferent trigeminal sensory information from the "truly extraordinary" trunk skin somatic sensory system, and rather function as units that separate neurons - but to what end? It appears that the myelin stripes are more likely to be efferent axonal bundles leaving the nuclei (to form the olivocerebellar tract). This justification is unsupported.

Comment: The referee cites some of our observations on myelin stripes, which we find unusual. We stand by the observations and comments. The referee does not discuss the most crucial finding we report on myelin stripes, namely that they correspond remarkably well to trunk folds.

Changes: None.

(6) The authors indicate that the location of these nuclei matches that of the trigeminal nuclei in other mammals. This is not supported in any way. In ALL other mammals in which the trigeminal nuclei of the brainstem have been reported they are found in the lateral aspect of the brainstem, bordered laterally by the spinal trigeminal tract. This is most readily seen and accessible in the Paxinos and Watson rat brain atlases. The authors indicate that the trigeminal nuclei are medial to the facial nerve nucleus, but in every other species, the trigeminal sensory nuclei are found lateral to the facial nerve nucleus. This is most salient when examining a close relative, the manatee (10.1002/ar.20573), where the location of the inferior olive and the trigeminal nuclei matches that described by Maseko et al (2013) for the African elephant. This justification is not supported.

Comment: The referee notes that we incorrectly state that the position of the trigeminal nuclei matches that of other mammals. We think this criticism is justified.

Changes: We prepared a comparison of the Maseko et al. (2013) scheme of the elephant brainstem with our scheme of the elephant brainstem (see Author response table 1). Here we acknowledge the referee’s argument and we also changed the manuscript accordingly.

(7) The dual to quadruple repetition of rostrocaudal modules within the putative trigeminal nucleus as identified by the authors relies on the fact that in the neurotypical mammal, there are several trigeminal sensory nuclei arranged in a column running from the pons to the cervical spinal cord, these include (nomenclature from Paxinos and Watson in roughly rostral to caudal order) the Pr5VL, Pr5DM, Sp5O, Sp5I, and Sp5C. However, these nuclei are all located far from the midline and lateral to the facial nerve nucleus, unlike what the authors describe in the elephants. These rostrocaudal modules are expanded upon in Figure 2, and it is apparent from what is shown that the authors are attributing other brainstem nuclei to the putative trigeminal nuclei to confirm their conclusion. For example, what they identify as the inferior olive in Figure 2D is likely the lateral reticular nucleus as identified by Maseko et al (2013). This justification is not supported.

Comment: The referee again compares our findings to the scheme of Maseko et al. (2013) and rejects our conclusions on those grounds. We think such a comparison of our scheme is needed, indeed.

Changes: We prepared a comparison of the Maseko et al. (2013) scheme of the elephant brainstem with our scheme of the elephant brainstem (see Author response table 1).

(8) In primates and related species, there is a distinct banded appearance of the inferior olive, but what has been termed the inferior olive in the elephant by other authors does not have this appearance, rather, and specifically, the largest nuclear mass in the region (termed the principal nucleus of the inferior olive by Maseko et al, 2013, but Pr5, the principal trigeminal nucleus in the current paper) overshadows the partial banded appearance of the remaining nuclei in the region (but also drawn by the authors of the current paper). Thus, what is at debate here is whether the principal nucleus of the inferior olive can take on a nuclear shape rather than evince a banded appearance. The authors of this paper use this variance as justification that this cluster of nuclei could not possibly be the inferior olive. Such a "semi-nuclear/banded" arrangement of the inferior olive is seen in, for example, giraffe (10.1016/j.jchemneu.2007.05.003), domestic dog, polar bear, and most specifically the manatee (a close relative of the elephant) (brainmuseum.org; 10.1002/ar.20573). This justification is not supported.

Comment: We carefully looked at the brain sections referred to by the referee in the brainmuseum.org collection. We found contrary to the referee’s claims that dogs, polar bears, and manatees have a perfectly serrated (a cellular arrangement in curved bands) appearance of the inferior olive. Accordingly, we think the referee is not reporting the comparative evidence fairly and we wonder why this is the case.

Changes: None.

Thus, all the justifications forwarded by the authors are unsupported. Based on methodological concerns, prior comparative mammalian neuroanatomy, and prior studies in the elephant and closely related species, the authors fail to support their notion that what was previously termed the inferior olive in the elephant is actually the trigeminal sensory nuclei. Given this failure, the justifications provided above that are sequelae also fail. In this sense, the entire manuscript and all the sequelae are not supported.

Comment: We disagree. To summarize:

(1) Our description of the cytochrome oxidase staining lacked methodological detail, which we have now added; the cytochrome oxidase reactivity data are great and support our conclusions.

(2)–(5)The referee does not really discuss our evidence on these points.

(6) We were wrong and have now fixed this mistake.

(7) The referee asks for a comparison to the Maseko et al. (2013) scheme (agreed, see Author response image 4 4 and Author response table 1).

(8) The referee bends the comparative evidence against us.

Changes: None.

A comparison of the elephant brainstem partitioning schemes put forward by Maseko et al 2013 and by Reveyaz et al.

To start with, we would like to express our admiration for the work of Maseko et al. (2013). These authors did pioneering work on obtaining high-quality histology samples from elephants. Moreover, they made a heroic neuroanatomical effort, in which they assigned 147 brain structures to putative anatomical entities. Most of their data appear to refer to staining in a single elephant and one coronal sectioning plane. The data quality and the illustration of results are excellent.

We studied mainly two large nuclei in six (now 7) elephants in three (coronal, parasagittal, and horizontal) sectioning planes. The two nuclei in question are the two most distinct nuclei in the elephant brainstem, namely an anterior ventromedial nucleus (the trigeminal trunk module in our terminology; the inferior olive in the terminology of Maseko et al., 2013) and a more posterior lateral nucleus (the inferior olive in our terminology; the posterior part of the trigeminal nuclei in the terminology of Maseko et al., 2013).

Author response image 4 gives an overview of the two partitioning schemes for inferior olive/trigeminal nuclei along with the rodent organization (see below).

Author response image 4.

Overview of the brainstem organization in rodents & elephants according to Maseko et. (2013) and Reveyaz et al. (this paper).

The strength of the Maseko et al. (2013) scheme is the excellent match of the position of elephant nuclei to the position of nuclei in the rodent (Author response image 4). We think this positional match reflects the fact that Maseko et al. (2013) mapped a rodent partitioning scheme on the elephant brainstem. To us, this is a perfectly reasonable mapping approach. As the referee correctly points out, the positional similarity of both elephant inferior olive and trigeminal nuclei to the rodent strongly argues in favor of the Maseko et al. (2013), because brainstem nuclei are positionally very conservative.

Other features of the Maseko et al. (2013) scheme are less favorable. The scheme marries two cyto-architectonically very distinct divisions (an anterior indistinct part) and a super-distinct serrated posterior part to be the trigeminal nuclei. We think merging entirely distinct subdivisions into one nucleus is a byproduct of mapping a rodent partitioning scheme on the elephant brainstem. Neither of the two subdivisions resemble the trigeminal nuclei of other mammals. The cytochrome oxidase staining patterns differ markedly across the anterior indistinct part (see our Author response image 4) and the posterior part of the trigeminal nuclei and do not match with the intense cytochrome oxidase reactivity of other mammalian trigeminal nuclei (Referee Figure 3). Our anti-peripherin staining indicates that there probably no climbing fibers, in what Maseko et al. think. is inferior olive; this is a potentially fatal problem for the hypothesis. The posterior part of Maseko et al. (2013) trigeminal nuclei has a distinct serrated appearance that is characteristic of the inferior olive in other mammals. Moreover, the inferior olive of Maseko et al. (2013) lacks the serrated appearance of the inferior olive seen in pretty much all mammals; this is a serious problem.

The partitioning scheme of Reveyaz et al. comes with poor positional similarity but avoids the other problems of the Maseko et al. (2013) scheme. Our explanation for the positionally deviating location of trigeminal nuclei is that the elephant grew one of the if not the largest trigeminal systems of all mammals. As a result, the trigeminal nuclei grew through the floor of the brainstem. We understand this is a post hoc just-so explanation, but at least it is an explanation.

The scheme of Reveyaz et al. was derived in an entirely different way from the Maseko model. Specifically, we were convinced that the elephant trigeminal nuclei ought to be very special because of the gigantic trigeminal ganglia (Purkart et al., 2022). Cytochrome-oxidase staining revealed a large distinct nucleus with an elongated shape. Initially, we were freaked out by the position of the nucleus and the fact that it was referred to as inferior olive by other authors. When we found an inferior-olive-like nucleus at a nearby (although at an admittedly unusual) location, we were less worried. We then optimized the visualization of myelin stripes (brightfield imaging etc.) and were able to collect an entire elephant trunk along with the brain (African elephant cow Indra). When we made the one-to-one match of Indra’s trunk folds and myelin stripes (Figure 4) we were certain that we had identified the trunk module of the trigeminal nuclei. We already noted at the outset of our rebuttal that we now consider such certainty a fallacy of overconfidence. In light of the comments of Referee 2, we feel that a further discussion of our ideas is warranted. A strength of the Reveyaz model is that nuclei look like single anatomical entities. The trigeminal nuclei look like trigeminal nuclei of other mammals, the trunk module has a striking resemblance to the trunk and the inferior olive looks like the inferior olive of other mammals.

We evaluated the fit of the two models in the form of a table (Author response table 1; below). Unsurprisingly, Author response table 1 aligns with our views of elephant brainstem partitioning.

Author response table 1.

Qualitative evaluation of elephant brainstem partitioning schemes

++ = Very attractive; + = attractive; - = unattractive; -- = very unattractive We scored features that are clear and shared by all mammals – as far as we know them – as very attractive. We scored features that are clear and are not shared by all mammals – as far as we know them – as very unattractive. Attractive features are either less clear or less well-shared features. Unattractive features are either less clear or less clearly not shared features.

Author response table 1 suggests two conclusions to us. (i) The Reveyaz et al. model has mainly favorable properties. The Maseko et al. (2013) model has mainly unfavorable properties. Hence, the Reveyaz et al. model is more likely to be true. (ii) The outcome is not black and white, i.e., both models have favorable and unfavorable properties. Accordingly, we overstated our case in our initial submission and toned down our claims in the revised manuscript.

What the authors have not done is to trace the pathway of the large trigeminal nerve in the elephant brainstem, as was done by Maseko et al (2013), which clearly shows the internal pathways of this nerve, from the branch that leads to the fifth mesencephalic nucleus adjacent to the periventricular grey matter, through to the spinal trigeminal tract that extends from the pons to the spinal cord in a manner very similar to all other mammals. Nor have they shown how the supposed trigeminal information reaches the putative trigeminal nuclei in the ventromedial rostral medulla oblongata. These are but two examples of many specific lines of evidence that would be required to support their conclusions. Clearly, tract tracing methods, such as cholera toxin tracing of peripheral nerves cannot be done in elephants, thus the neuroanatomy must be done properly and with attention to detail to support the major changes indicated by the authors.

Comment: The referee claims that Maseko et al. (2013) showed by ‘tract tracing’ that the structures they refer to trigeminal nuclei receive trigeminal input. This statement is at least slightly misleading. There is nothing of what amounts to proper ‘tract tracing’ in the Maseko et al. (2013) paper, i.e. tracing of tracts with post-mortem tracers. We tried proper post-mortem tracing but failed (no tracer transport) probably as a result of the limitations of our elephant material. What Maseko et al. (2013) actually did is look a bit for putative trigeminal fibers and where they might go. We also used this approach. In our hands, such ‘pseudo tract tracing’ works best in unstained material under bright field illumination, because myelin is very well visualized. In such material, we find: (i) massive fiber tracts descending dorsoventrally roughly from where both Maseko et al. 2013 and we think the trigeminal tract runs. (ii) These fiber tracts run dorsoventrally and approach, what we think is the trigeminal nuclei from lateral.

Changes: Ad hoc tract tracing see above.

So what are these "bumps" in the elephant brainstem?

Four previous authors indicate that these bumps are the inferior olivary nuclear complex. Can this be supported?

The inferior olivary nuclear complex acts "as a relay station between the spinal cord (n.b. trigeminal input does reach the spinal cord via the spinal trigeminal tract) and the cerebellum, integrating motor and sensory information to provide feedback and training to cerebellar neurons" (https://www.ncbi.nlm.nih.gov/books/NBK542242/). The inferior olivary nuclear complex is located dorsal and medial to the pyramidal tracts (which were not labeled in the current study by the authors but are clearly present in Fig. 1C and 2A) in the ventromedial aspect of the rostral medulla oblongata. This is precisely where previous authors have identified the inferior olivary nuclear complex and what the current authors assign to their putative trigeminal nuclei. The neurons of the inferior olivary nuclei project, via the olivocerebellar tract to the cerebellum to terminate in the climbing fibres of the cerebellar cortex.

Comment: We agree with the referee that in the Maseko et al. (2013) scheme the inferior olive is exactly where we expect it from pretty much all other mammals. Hence, this is a strong argument in favor of the Maseko et al. (2013) scheme and a strong argument against the partitioning scheme suggested by us.

Changes: Please see our discussion above.

Elephants have the largest (relative and absolute) cerebellum of all mammals (10.1002/ar.22425), this cerebellum contains 257 x109 neurons (10.3389/fnana.2014.00046; three times more than the entire human brain, 10.3389/neuro.09.031.2009). Each of these neurons appears to be more structurally complex than the homologous neurons in other mammals (10.1159/000345565; 10.1007/s00429-010-0288-3). In the African elephant, the neurons of the inferior olivary nuclear complex are described by Maseko et al (2013) as being both calbindin and calretinin immunoreactive. Climbing fibres in the cerebellar cortex of the African elephant are clearly calretinin immunopositive and also are likely to contain calbindin (10.1159/000345565). Given this, would it be surprising that the inferior olivary nuclear complex of the elephant is enlarged enough to create a very distinct bump in exactly the same place where these nuclei are identified in other mammals?

Comment: We agree with the referee that it is possible and even expected from other mammals that there is an enlargement of the inferior olive in elephants. Hence, a priori one might expect the ventral brain stem bumps to the inferior olive, this is perfectly reasonable and is what was done by previous authors. The referee also refers to calbindin and calretinin antibody reactivity. Such antibody reactivity is indeed in line with the referee’s ideas and we considered these findings in our Referee Table 1. The problem is, however, that neither calbindin nor calretinin antibody reactivity are highly specific and indeed both nuclei in discussion (trigeminal nuclei and inferior olive) show such reactivity. Unlike the peripherin-antibody staining advanced by us, calbindin nor calretinin antibody reactivity cannot distinguish the two hypotheses debated.

Changes: Please see our discussion above.

What about the myelin stripes? These are most likely to be the origin of the olivocerebellar tract and probably only have a coincidental relationship with the trunk. Thus, given what we know, the inferior olivary nuclear complex as described in other studies, and the putative trigeminal nuclear complex as described in the current study, is the elephant inferior olivary nuclear complex. It is not what the authors believe it to be, and they do not provide any evidence that discounts the previous studies. The authors are quite simply put, wrong. All the speculations that flow from this major neuroanatomical error are therefore science fiction rather than useful additions to the scientific literature.

Comment: It is unlikely that the myelin stripes are the origin of the olivocerebellar tract as suggested by the referee. Specifically, the lack of peripherin-reactivity indicates that these fibers are not climbing fibers (Referee Figure 1). In general, we feel the referee does not want to discuss the myelin stripes and obviously thinks we made up the strange correspondence of myelin stripes and trunk folds.

Changes: Please see our discussion above.

What do the authors actually have?

The authors have interesting data, based on their Golgi staining and analysis, of the inferior olivary nuclear complex in the elephant.

Comment: The referee reiterates their views.

Changes: None.

Reviewer #3 (Public Review):

Summary:

The study claims to investigate trunk representations in elephant trigeminal nuclei located in the brainstem. The researchers identified large protrusions visible from the ventral surface of the brainstem, which they examined using a range of histological methods. However, this ventral location is usually where the inferior olivary complex is found, which challenges the author's assertions about the nucleus under analysis. They find that this brainstem nucleus of elephants contains repeating modules, with a focus on the anterior and largest unit which they define as the putative nucleus principalis trunk module of the trigeminal. The nucleus exhibits low neuron density, with glia outnumbering neurons significantly. The study also utilizes synchrotron X-ray phase contrast tomography to suggest that myelin-stripe-axons traverse this module. The analysis maps myelin-rich stripes in several specimens and concludes that based on their number and patterning they likely correspond with trunk folds; however, this conclusion is not well supported if the nucleus has been misidentified.

Comment: The referee gives a concise summary of our findings. The referee acknowledges the depth of our analysis and also notes our cellular results. The referee – in line with the comments of Referee 2 – also points out that a misidentification of the nucleus under study is potentially fatal for our analysis. We thank the referee for this fair assessment.

Changes: We feel that we need to alert the reader more broadly to the misidentification concern. We think the critical comments of Referee 2, which will be published along with our manuscript, will go a long way in doing so. We think the eLife publishing format is fantastic in this regard. We will also include pointers to these concerns in the revised manuscript.

Strengths:

The strength of this research lies in its comprehensive use of various anatomical methods, including Nissl staining, myelin staining, Golgi staining, cytochrome oxidase labeling, and synchrotron X-ray phase contrast tomography. The inclusion of quantitative data on cell numbers and sizes, dendritic orientation and morphology, and blood vessel density across the nucleus adds a quantitative dimension. Furthermore, the research is commendable for its high-quality and abundant images and figures, effectively illustrating the anatomy under investigation.

Comment: Again, a very fair and balanced set of comments. We are thankful for these comments.

Changes: None.

Weaknesses:

While the research provides potentially valuable insights if revised to focus on the structure that appears to be the inferior olivary nucleus, there are certain additional weaknesses that warrant further consideration. First, the suggestion that myelin stripes solely serve to separate sensory or motor modules rather than functioning as an "axonal supply system" lacks substantial support due to the absence of information about the neuronal origins and the termination targets of the axons. Postmortem fixed brain tissue limits the ability to trace full axon projections. While the study acknowledges these limitations, it is important to exercise caution in drawing conclusions about the precise role of myelin stripes without a more comprehensive understanding of their neural connections.

Comment: The referee points out a significant weakness of our study, namely our limited understanding of the origin and targets of the axons constituting the myelin stripes. We are very much aware of this problem and this is also why we directed high-powered methodology like synchrotron X-ray tomograms to elucidate the structure of myelin stripes. Such analysis led to advances, i.e., we now think, what looks like stripes are bundles and we understand the constituting axons tend to transverse the module. Such advances are insufficient, however, to provide a clear picture of myelin stripe connectivity.

Changes: We think solving the problems raised by the referee will require long-term methodological advances and hence we will not be able to solve these problems in the current revision. Our long-term plans for confronting these issues are the following: (i) Improving our understanding of long-range connectivity by post-mortem tracing and MR-based techniques such as Diffusion-Tensor-Imaging. (ii) Improving our understanding of mid and short-range connectivity by applying even larger synchrotron X-ray tomograms and possible serial EM.

Second, the quantification presented in the study lacks comparison to other species or other relevant variables within the elephant specimens (i.e., whole brain or brainstem volume). The absence of comparative data for different species limits the ability to fully evaluate the significance of the findings. Comparative analyses could provide a broader context for understanding whether the observed features are unique to elephants or more common across species. This limitation in comparative data hinders a more comprehensive assessment of the implications of the research within the broader field of neuroanatomy. Furthermore, the quantitative comparisons between African and Asian elephant specimens should include some measure of overall brain size as a covariate in the analyses. Addressing these weaknesses would enable a richer interpretation of the study's findings.

Comment: The referee suggests another series of topics, which include the analysis of brain parts volumes or overall brain size. We agree these are important issues, but we also think such questions are beyond the scope of our study.

Changes: We hope to publish comparative data on elephant brain size and shape later this year.  

Author response:

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

Summary: 

Laura Morano and colleagues have performed a screen to identify compounds that interfere with the formation of TopBP1 condensates. TopBP1 plays a crucial role in the DNA damage response, and specifically the activation of ATR. They found that the GSK-3b inhibitor AZD2858 reduced the formation of TopBP1 condensates and activation of ATR and its downstream target CHK1 in colorectal cancer cell lines treated with the clinically relevant irinotecan active metabolite SN-38. This inhibition of TopBP1 condensates by AZD2858 was independent from its effect on GSK-3b enzymatic activity. Mechanistically, they show that AZD2858 thus can interfere with intra-S-phase checkpoint signaling, resulting in enhanced cytostatic and cytotoxic effects of SN-38 (or SN-38+Fluoracil aka FOLFIRI) in vitro in colorectal carcinoma cell lines. 

Major comments: 

Overall the work is rigorous and the main conclusions are convincing. However, they only show the effects of their combination treatments on colorectal cancer cell lines. I'm worried that blocking the formation of TopB1 condensates will also be detrimental in non-transformed cells. Furthermore it is somewhat disappointing that it remains unclear how AZD2858 blocks selfassembly of TopBP1 condensates, although I understand that unraveling this would be complex and somewhat out-of-reach for now. 

We appreciate your feedback and fully recognize the importance of understanding how AZD2858 blocks the assembly of TopBP1 condensates. While we understand your disappointment, addressing this question remains a key focus for us. Keeping in mind that unravelling such a mechanism in vitro or in vivo is rather challenging, we have consulted an expert who has made efforts to predict the potential docking sites of AZD2858 on TopBP1, which may provide valuable insights for future experimental investigations. Using an AlphaFold model (no crystal or cryo-EM structure available) and looking for suitable pockets or cavities in which AZD2858 could bind, the analyses, though requiring cautious interpretation, suggested that AZD2858 may target the BRCT1 and BRCT8 domains (as shown below, two pockets n°1 and 7 with sufficient volume and surrounded by b-sheets structures like other GSK3 inhibitor) of TopBP1.

However, these are preliminary results that require further exploration and experimental validation to confirm their significance and mechanistic implications.

Author response image 1.

Here are some specific points for improvement: 

(1) The authors conclude that "These data supports [sic] the feasibility of targeting condensates formed in response to DNA damage to improve chemotherapy-based cancer treatments". To support this conclusion the authors need to show that proliferating non-transformed cells (e.g. primary cell cultures or organoids) can tolerate the combination of AZD2858 + SN-38 (or FOLFIRI) better than colorectal cancer cells. 

We would like to thank the reviewer for this vital suggestion to prove that this combination is effective on tumor cells and not very toxic on healthy cells. We therefore used a healthy colon cell line (CCD841) and tested the efficacy of each treatment alone (FOLFIRI and AZD2858) as well as the combination FOLFIRI+AZD2858. We compared the results obtained in the CCD841 cell line with those obtained in the HCT116 colorectal cancer cell line. The results presented below show not only that each treatment alone is much less effective on CCD841 lines, but also that the combination is not synergistic.

Author response image 2.

Page 19 "This suggests that the combination... arrests the cell cycle before mitosis in a DNAPKsc-dependent manner." I find the remark that this arrest would be DNA-PKcs-dependent too speculative. I suppose that the authors base this claim on reference 55 but if they want to support this claim they need to prove this by adding DNA-PKcs inhibitors to their treated cells. 

Thank you for your thoughtful comment. We agree with the reviewer that claiming the G2/M arrest is DNA-PKcs-dependent without direct experimental evidence is speculative. While we initially based this hypothesis on reference 55, we acknowledge that further experiments, such as the use of DNA-PKcs inhibitors, would be necessary to robustly support this claim.

Given that this observation was intended as a potential explanation for the G2/M arrest observed at 6 and 12 hours of treatment with AZD2858 + SN-38 (compared to SN-38 alone), and considering that exploring this pathway is not the primary focus of our study, we have decided to remove this hypothesis from both the figure and the text to avoid any ambiguity.

We appreciate the reviewer’s input and will consider investigating this pathway in future studies.

(2) When discussing Figure S5B the authors claim that SN-38 + AZD2858 progressively increases the fractions of BrdU positive cells, but this is not supported by statistical analysis.

The fractions are still very small, so I would like to see statistics on these data. Alternatively, the authors could take out this conclusion. 

Thank you for your valuable comment. In response, we have conducted a statistical analysis (Mann-Whitney test) on the data, and the results have been added to Figure S5C for the 6-hour time point and Figure S5D for the 12-hour time point, based on three independent biological replicates. We hope this provides the necessary clarification.

Minor comments: 

- Page 5 Materials and methods - Cell culture. Last sentence "Add in what medium you cultured them" looks like an internal review remark and should probably be removed? 

We apologize for this oversight. The medium has now been specified, and the sentence has been removed.

- The numbers in all the synergy matrices (in white font) are extremely small and virtually unreadable, and visually distracting. I recommend taking these out altogether. 

We believe that the reduction in figure quality may be due to the PDF compression, which affected the resolution of the figures. We are happy to provide high-resolution versions of the figures separately for clarity. If the issue persists even with the higher resolution, we will consider removing the numbers, as suggested.

- The legends of the synergy matrices (for example Fig 1D, 4E, 5, 6) are often extremely small, making it difficult to understand them intuitively. Please enlarge them and label them more clearly, and use larger fonts. In the legend of Figure 5D,E a green matrix indicating % live cells is mentioned but I don't see it. Do they mean the grey matrix? 

We have enlarged the figure legends and will provide high-resolution versions of the figures to ensure all details are clearly readable. Regarding Figure 5D,E: we acknowledge that the color may appear differently (more green or gray) depending on the display or printer settings. To avoid any confusion, we have corrected the legend to specify that the color in question is khaki, rather than green. Moreover, following suggestions of the reviewer #2, these figures have been respectively moved to Figure S6B and S6C.

- Figure S2. Perhaps I misunderstand the PML body experiment but the authors seem to use PML body formation to support their idea that AZD2858 blocks TopBP1 condensate formation and not just any condensate formation. However, if this is the case they would need a proper positive control, i.e. an additional experimental condition in which they do see PLM bodies. 

Arsenic is a well-known positive control for experiments involving PML bodies due to its ability to induce specific responses in PML proteins and modify PML nuclear bodies (NBs) structure and function (Jaffray et al., 2023, JCB ; Zhu et al., 1997, PNAS). Thus, we used Arsenic as a positive control and observed a significant increase in PML NBs vs the other conditions (Kruskal-Wallis test) as indicated below. We thus implemented the results in the corresponding figure S2B and text.

Author response image 3.

PML condensates were tested after 2 h of incubation. AZD2858 : 100nM ; SN-38 : 300nM ; Arsenic : 6µM. ****: p<0.0001 (Kruskal-Wallis test).

- The quantification of the flow cytometry data needs to be clarified. I find it strange that in the figures (for example Figure 3A and 3C) representative examples are shown of apparently 3 replicates, and that the percentages shown in these examples are then the given in the text as the overall numbers; for example on page 18 "...BrdU incorporation increased from 16.11% (SN38 alone) to 41.83% (combination)...". This type of description is done in multiple places in the Results section and is confusing. It would be clearer if the authors show proper quantifications (mean +/- sem) of the percentages of (the relevant) gated populations. Besides, I don't think it make a lot of sense to mention in the text the percentages with 2 decimals behind the comma. This suggests a level of precision that does not seem justified in flow cytometry data. Finally, all flow cytometry plots look visually very busy and all the text is crammed in with really small fonts. Cleaning them up and enlarging the fonts of the remaining text/numbers would really improve the readability of the figures. 

Thank you for your helpful comments. We understand your concern regarding the flow cytometry quantification. Indeed, the percentages presented in the figures are derived from representative replicates, and we acknowledge that this presentation could be confusing. To address this, we have included a table summarizing the data from all replicates to improve readability [Table S2 and S3 in the new version]. Second, we specified in the text that the data are representative biological replicates when needed. Third, we have performed statistical analyses on the three replicates when necessary, as shown in Supplementary Figure S5C-F in the new version. The text has been revised to reflect the correct statistical interpretation.

Regarding the use of two decimal, we are unable to remove them due to limitations in the software (Kaluza) used for flow cytometry analysis. However, we agree that this level of precision may not be warranted, and we have revised the text where appropriate to reduce confusion.

- In Figure 5G the authors show that FOLFIRI + AZD2858 are synergistic in two SN-38-resistant cell lines. They conclude that this combination may overcome drug resistance. But tried to figure out the used FOLFIRI concentrations used in these cell lines and they still seem far higher than the SN-38-sensitive HCT116 cell lines, so I would like to see a bit more nuance in their interpretation. I think overcoming drug resistance is an overstatement, and perhaps alleviating would be a better term 

Thank you for highlighting this important point; we have adjusted the text accordingly.

- The legend in Table S2 refers to Figure 5A-B; this should be Figure 4A-B. 

Thank you, this has been corrected and Table S2 is now moved to Table S4 .

Reviewer #1 (Significance (Required)): 

The finding that AZD2858 block TOPbp1 condensate formation via a pleiotropic effect of this compound is interesting and convincing. To my best knowledge it's a novel finding which is interesting to the potential target audience mentioned below. Their findings that inhibition of TOPbp1 condensation and ATR signaling via AZD2858 may synergize with FOLFIRI therapy in colorectal cancer cells are still very preliminary, because the effects on non-cancerous cells are not tested. 

Researchers involved in early cancer drug discovery and cell biologists studying DNA damage responses in cancer cells seem to me typical audience interested and influenced by this paper. 

I'm a cell biologist studying cell cycle fate decisions, and adaptation of cancer cells & stem cells to (drug-induced) stress. My expertise aligns well with the work presented throughout this paper. 

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

The authors have extended their previous research to develop TOPBP1 as a potential drug target for colorectal cancer by inhibiting its condensation. Utilizing an optogenetic approach, they identified the small molecule AZD2858, which inhibits TOPBP1 condensation and works synergistically with first-line chemotherapy to suppress colorectal cancer cell growth. The authors investigated the mechanism and discovered that disrupting TOPBP1 assembly inhibits the ATR/Chk1 signaling pathway, leading to increased DNA damage and apoptosis, even in drug-resistant colorectal cancer cell lines. Addressing the following concerns would enhance clarity and further in vivo work may improve significance: 

(1) How does the optogenetic method for inducing condensates compare to the DNA damage induction mechanism? 

Optogenetics provides a versatile and precise approach for controlling the condensation of scaffold proteins in both space and time. This method enables us to study the role of biomolecular condensates with minute-scale resolution, separating their formation from potentially confounding upstream events, such as DNA damage, and providing valuable insights into their specific function. Importantly, based on our previous publications on TopBP1 or SLX4 optogenetic condensates, we have substantial evidence indicating that light-induced condensates closely mimic those formed in response to DNA damage:

- Functional similarity: Optogenetic condensates recapitulate endogenous condensates formed upon exposure of the cells of DNA damaging agents, and include most known partner proteins involved in the DNA damage response. It was shown for light induced-TopBP1 and SLX4 condensates (1-3).

- Dynamic reversibility: Optogenetic condensates and DNA damage induced condensates are both dynamic and reversible. They dissolve within 15 minutes of light deactivation or after removal of the damaging agent (1,3).

- Chromatin association: Both optogenetic and DNA damage-induced condensates are bound to chromatin or localized at sites of DNA damage (3).

- Regulation: Both types of condensates are regulated similarly, with their formation triggered by the same signaling pathways. ATR basal activity drives the nucleation of opto-TopBP1 condensates and endogenous TopBP1 structures upon light exposure (1). Likewise, sumoylation modifications regulate the formation of opto-SLX4 condensates and endogenous SLX4 condensates (3).

- Structurally: Using super-resolution imaging by stimulation-emission-depletion (STED) microscopy, we observed that endogenous SLX4 nanocondensates formed globular clusters that were indistinguishable from recombinant light induced SLX4 condensates (1,3).  

(1) Frattini C, Promonet A, Alghoul E, Vidal-Eychenie S, Lamarque M, Blanchard MP, et al. TopBP1 assembles nuclear condensates to switch on ATR signaling. Molecular Cell. 18 mars 2021;81(6):1231-1245.e8. 

(2) Alghoul E, Basbous J, Constantinou A. An optogenetic proximity labeling approach to probe the composition of inducible biomolecular condensates in cultured cells. STAR Protocols. 2021;2(3):100677. 

(3) Alghoul E, Basbous J, Constantinou A. Compartmentalization of the DNA damage response: Mechanisms and functions. DNA Repair. août 2023;128:103524.

(2) Why wasn't the initial screen conducted on the HCT116-SN50 resistant cell line? 

Thank you for raising this important question, which we also considered at the outset of the project. After careful consideration, we decided to use the HCT116 WT cells in order to obtain initial data from an unmodified cell line. It is worth mentioning that HCT116-SN50 cells exhibit slower proliferation compared to WT cells, and they also express an efflux pump capable of pumping out SN38. We were concerned that these factors might interfere with the optogenetic assay, which is why we chose to perform the screen using the WT HCT116 cells.

(3) The labels in Fig. 1D are difficult to recognize. 

This issue was also raised by Reviewer #1. We suspect that the PDF conversion may have reduced the resolution of the figures, so we will provide them separately in high resolution. In addition, we have increased the size of some labels to improve their clarity.

The selected cell image in Fig. 2A for SN-38 seems over-representative; unselected cells appear similar to other groups. Why does AZD2858 itself induce TopBP1 condensates in the plot, yet this is not evident in the images? 

Thank you for your comment; we have updated the figure with a more representative image. We indeed observe that AZD2858 alone induces a slight increase in TopBP1 condensates. However, this increase did not lead to the activation of the ATR/Chk1 signaling pathway, as shown by the Western blot data presented in Fig. 2B. In addition, AZD2858 specifically prevents the formation of TopBP1 condensates induced by SN38 treatment, and the level of TopBP1 condensates does not return to the basal levels observed in untreated cells, but rather to those observed with AZD2858 treatment. During the 2-hour AZD2858 treatment, the progression of replication forks was unaffected (Fig. 3A and 3B). However, when AZD2858 was added alone to the Xenopus egg extracts, there was increased recruitment of TopBP1 to the chromatin (Fig. 2E). This result suggests that AZD2858 alone can induce the assembly of TopBP1 on chromatin to initiate DNA replication (a well-established role of TopBP1), but the number and concentration of TopBP1 molecules did not reach levels sufficient to activate the ATR/Chk1 pathway.

(4) In Fig. 3A, despite the drastic change in the FACS plot shape, the quantifications appear quite similar. 

Thank you for this insightful observation. The gates for the S phase were intentionally set wider to avoid biasing the results and inadvertently excluding the population that incorporates BrdU weakly (but still incorporates it) in the SN-38 only condition. As a result, the percentage of cells within this gate remains similar, even though the overall shape of the FACS plot changes, reflecting a shift in the distribution of BrdU incorporation. This point has now been clarified in the legend of the Figure 3A.

This effect can also be attributed to the relatively short treatment time (2 hours), which captures early changes in DNA synthesis. The effect becomes more pronounced at later time points, as shown in Figure 3C. For example, after 6 hours of treatment, the percentage of BrdU-positive cells increases from 15% with SN-38 alone to 41% with the AZD2858 combination, demonstrating a clearer impact on DNA synthesis. A graph summarizing the statistical analysis has been added to Figure S5C for the 6-hour time point and Figure S5D for the 12-hour time point, based on data from three independent biological replicates.

(5) The results section is imbalanced; Figs. 5 and 6 could be combined into one figure. 

We have combined Figures 5 and 6 into a single figure to optimize the presentation of results. To avoid overloading the new figure, some of the data have been moved to supplementary figures, ensuring the main figure remains clear and focused.

(6) An in vivo study is anticipated to assess the drug's efficacy. 

Although AZD2858 was developed a few years ago, there is a limited amount of in vivo data available, which led us to consider potential issues related to the drug's biodistribution or its pharmacokinetics (PK). Despite these concerns, we proceeded with preliminary in vivo studies, testing various diluents and injection routes for AZD2858. However, we observed that the compound was not effective in vivo. Given the strong synergistic effects observed in vitro, we concluded that AZD2858 was likely not being distributed properly in the mice. As a result, we have decided to conduct a more detailed investigation into the pharmacokinetics (PK), pharmacodynamics (PD), and absorption, distribution, metabolism, and excretion (ADME) of AZD2858 to better understand its in vivo behavior and efficacy. Therefore, the in vivo evaluation of AZD2858 will be addressed in a separate study specifically focused on this aspect.

Reviewer #2 (Significance (Required)): 

Addressing the stated concerns would enhance clarity and further in vivo work may improve significance. 

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

Summary 

In 2021 (PMID: 33503405) and 2024 (PMID: 38578830) Constantinou and colleagues published two elegant papers in which they demonstrated that the Topbp1 checkpoint adaptor protein could assemble into mesoscale phase-separated condensates that were essential to amplify activation of the PIKK, ATR, and its downstream effector kinase, Chk1, during DNA damage signalling. A key tool that made these studies possible was the use of a chimeric Topbp1 protein bearing a cryptochrome domain, Cry2, which triggered condensation of the chimeric Topbp1 protein, and thus activation of ATR and Chk1, in response to irradiation with blue light without the myriad complications associated with actually exposing cells to DNA damage. 

In this current report Morano and co-workers utilise the same optogenetic Topbp1 system to investigate a different question, namely whether Topbp1 phase-condensation can be inhibited pharmacologically to manipulate downstream ATR-Chk1 signalling. This is of interest, as the therapeutic potential of the ATR-Chk1 pathway is an area of active investigation, albeit generally using more conventional kinase inhibitor approaches. 

The starting point is a high throughput screen of 4730 existing or candidate small molecule anticancer drugs for compounds capable of inhibiting the condensation of the Topbp1-Cry2mCherry reporter molecule in vivo. A surprisingly large number of putative hits (>300) were recorded, from which 131 of the most potent were selected for secondary screening using activation of Chk1 in response to DNA damage induced by SN-38, a topoisomerase inhibitor, as a surrogate marker for Topbp1 condensation. From this the 10 most potent compounds were tested for interactions with a clinically used combination of SN-38 and 5-FU (FOLFIRI) in terms of cytotoxicity in HCT116 cells. The compound that synergised most potently with FOLFIRI, the GSK3-beta inhibitor drug AZD2858, was selected for all subsequent experiments. 

AZD2858 is shown to suppress the formation of Topbp1 (endogenous) condensates in cells exposed to SN-38, and to inhibit activation of Chk1 without interfering with activation of ATM or other endpoints of damage signalling such as formation of gamma-H2AX or activation of Chk2 (generally considered to be downstream of ATM). AZD2858 therefore seems to selectively inhibit the Topbp1-ATR-Chk1 pathway without interfering with parallel branches of the DNA damage signalling system, consistent with Topbp1 condensation being the primary target. Importantly, neither siRNA depletion of GSK3-beta, or other GSK3-beta inhibitors were able to recapitulate this effect, suggesting it was a specific non-canonical effect of AZD2858 and not a consequence of GSK3-beta inhibition per se. 

To understand the basis for synergism between AZD2858 and SN-38 in terms of cell killing, the effect of AZD2858 on the replication checkpoint was assessed. This is a response, mediated via ATR-Chk1, that modulates replication origin firing and fork progression in S-phase cell under conditions of DNA damage or when replication is impeded. SN-38 treatment of HCT116 cells markedly suppresses DNA replication, however this was partially reversed by co-treatment with AZD2858, consistent with the failure to activate ATR-Chk1 conferring a defect in replication checkpoint function. 

Figures 4 and 5 demonstrate that AZD2858 can markedly enhance the cytotoxic and cytostatic effects of SN-38 and FOLFIRI through a combination of increased apoptosis and growth arrest according to dosage and treatment conditions. Figure 6 extends this analysis to cells cultured as spheroids, sometimes considered to better represent tumor responses compared to single cell cultures. 

Major comments 

Most of the data presented is of good technical quality and supports the conclusions drawn. There are however a small number of instances where this is not true; ie where the data are of insufficient technical quality, or where the description or interpretation of the results is at variance with the data which is presented. Some examples: 

(1) Fig.2E - the claim that "we observed an increase in RPA, Topb1 and Pol-epsilon levels when CPT and AZD2858 were added together" do not seem to be justified by the data provided. It is also unclear what the purpose/ significance of this experiment is. 

Thank you for pointing out the contradiction in Figure 2E. Upon review, we identified an error in the labeling of conditions (CPT and AZD2858 were inadvertently swapped). The corrected figure now clearly shows that, at the 60-minute timepoint after starting replication, the combination of

CPT and AZD2858 results in a greater accumulation of TopBP1, Pol ε, and RPA on chromatin compared to CPT alone. We have revised the sentence to: "Our data demonstrate that combining CPT and AZD2858 earlier enhances the accumulation of replication-related factors (RPA, TopBP1, and Pol ε) on chromatin compared to CPT treatment alone, particularly visible at the 60minute after starting replication."

The significance of this experiment lies in its connection to the earlier observation that AZD2858 restores BrdU incorporation when combined with SN-38, as shown in flow cytometry data (Figure 3A). At a molecular level, this was further supported by DNA fiber assays, which revealed that replication tracks (CldU tracts) were longer in the combination treatment compared to SN-38 alone (Figure 3B).

To strengthen and validate these findings, we chose to employ the Xenopus egg extract system for several reasons. This model provides a highly controlled environment where DNA replication occurs without confounding effects from transcription or translation. Moreover, replication is limited to a single round, offering a unique opportunity to specifically interrogate replication mechanisms. These attributes make the Xenopus model an ideal system to confirm that AZD2858 facilitates replication recovery in the presence of replication stress induced by agents like CPT. This will lead, in longer treatment, to accumulation of DNA damage and apoptosis (Figure 3D-E and Figure 4A-D)

(2) Figs. 3 A and C certainly show that the SN-38-mediated suppression of DNA synthesis is modified and partially alleviated by co-treatment with AZD2858. The statement however that "prolonged co-incubation with AZD2858 for 6 and 12 hours effectively abolished the SN-38 induced S-phase checkpoint" is clearly misleading. If this were true, then the BrdU incorporation profiles of the respective samples would be similar or identical to control, which clearly they are not. Clearly AZD2858 is affecting the imposition of the S-phase checkpoint in some way, but not "abolishing" it. 

We appreciate the reviewer’s detailed observations regarding Figures 3A and 3C and the phrasing in our manuscript. We agree that the term "abolished" is not precise in describing the effects of AZD2858 on the SN-38-induced S-phase checkpoint.

To clarify: our data indicate that co-treatment with AZD2858 modifies and partially alleviates the SN-38-induced suppression of DNA synthesis, as demonstrated by increased BrdU incorporation relative to SN-38 treatment alone. However, as the reviewer correctly points out, the BrdU incorporation profiles of the co-treated samples do not fully return to control non treated cells levels. This suggests that while AZD2858 significantly mitigates the S-phase checkpoint, it does not completely abolish it.

We have revised the statement in the manuscript to better reflect these findings, as follows: "Prolonged co-incubation with AZD2858 for 6 and 12 hours significantly alleviated the SN-38induced S-phase checkpoint, as evidenced by the partially increased BrdU incorporation. However, the population of co-treated cells is heterogeneous: some cells exhibit BrdU incorporation levels similar to those of untreated control cells, while others incorporate BrdU at levels comparable to cells treated with SN-38 alone. This indicates that AZD2858 does not fully restore DNA synthesis to control levels across the entire cell population."

This revised phrasing aligns with the data presented and acknowledges the partial recovery of DNA synthesis observed. Thank you for bringing this to our attention and helping us improve the accuracy of our conclusions.

(3) Fig. 3 E. The western blots of pDNA-PKcs (S2056) and total DNA-PKcs are really not interpretable. It is possible to sympathise that these reagents are probably extremely difficult to work with and obtain clear results, however uninterpretable results are not acceptable. 

We agree that the data presented in the Fig3E are difficult to interpret. As noted by Reviewer 1, we recognize the challenge of obtaining clear and reliable results with these specific reagents. Based on this feedback, and to ensure the robustness of our conclusions, we have decided to exclude these specifics blots from the revised manuscript.

We believe that this adjustment will enhance the clarity and reliability of the manuscript while focusing on the other, more interpretable data presented. Thank you for pointing this out, and we appreciate your understanding.

(4) Fig. 3D. This is a puzzling image. Described as a PFGE assay, it presumably depicts an agarose gel, with intact genomic DNA at the top and a discrete band below representing fragmented genomic DNA. This is a little surprising, as fragmented genomic DNA does not usually appear as a specific band but as a heterogenous population or "smear". Nevertheless, even if one accepts this premise, it is unclear what is meant by "DSBs remained elevated after the combined treatment" when the intensity of this band is equivalent for both SN-38 and SN-38 + AZD2858 treatments. 

We thank the reviewer for his insightful comments regarding the PFGE results in Figure 3D. We agree that the appearance of a discrete band, rather than a heterogeneous smear, is atypical for fragmented genomic DNA in this assay. However, by enhancing the signal intensity (as shown below), the expected smear becomes more appreciable.

Author response image 4.

Regarding the interpretation of the band intensities, we agree that the signals for SN-38 and SN38 + AZD2858 appear similar under these specific conditions. At the relatively high concentration of SN-38 used in this experiment (300 nM), it is indeed challenging to observe a more pronounced effect on DNA breaks. This is why we proposed the "DSBs remained elevated after the combined treatment" because the band intensity of SN-38 single agent treated cells or combined with AZD2858 is comparable. However, we note a slightly more intense γH2AX signal over time when AZD2858 is combined with SN-38 compared to SN-38 alone (Figure 3E). Furthermore, under lower, sub-optimal doses of SN-38 and over extended incubation treatment (48h), we observe a clearer increase in fragmented DNA bands, as demonstrated in Figure 4D.

Minor comments 

(1) Fig. 1. A surprisingly large number of compounds scored positive in the primary screen for inhibition of Topbp1 condensation (>300). Of the 131 of these selected for secondary screening using Chk1 activation (S345 phosphorylation) as a readout approximately 2/3 were negative, implying that a majority of the tested compounds inhibited Topbp1 condensation but not Chk1 activation. What could explain that?

Thank you for this thoughtful comment. The discrepancy between the large number of compounds scoring positive for TopBP1 condensation inhibition and the smaller number inhibiting Chk1 activation (S345 phosphorylation) could be attributed to several factors:

• Different cell lines and induction methods: The initial screen was conducted in HEK293 TrexFlpin cells overexpressing optoTopBP1, while the secondary screen used HCT116 cells. In addition, the methods used to induce the respective pathways were distinct: in the primary screen, we employed a blue light induction of opto-TopBP1 condensates, whereas in the secondary screen, we used an SN-38 treatment to induce DNA replication stress and activate the Chk1 pathway. These differences could account for the varying responses observed in the two screens.

• The compounds that inhibited TopBP1 condensation might not fully block Chk1 activation. While they disrupt TopBP1 condensation, they may still allow for partial activation of Chk1 or Chk1 activation through alternative mechanisms. For instance, Chk1 activation could be mediated by other signaling pathways or molecules, such as ETAA1, a known Chk1 activator (1). Thus, TopBP1 condensation inhibition does not necessarily translate to complete inhibition of Chk1 activation, especially if ETAA1 is employed by cells as a rescue activator.

• Some compounds may affect chromosome dynamics, potentially generating mechanical forces or torsional stress that could activate the ATR/Chk1 pathway independently of TopBP1

(2).

These factors suggest that while the compounds effectively disrupt TopBP1 condensation, they may not always fully inhibit the downstream Chk1 activation, pointing to the complexity of the DNA damage response pathways. 

(1) Bass, T. E. et al. ETAA1 acts at stalled replication forks to maintain genome integrity. Nat Cell Biol 18, 1185–1195 (2016).

(2) Kumar, A. et al. ATR Mediates a Checkpoint at the Nuclear Envelope in Response to Mechanical Stress. Cell 158, 633–646 (2014).

(2) Fig. 2D. The protein-protein interaction assay shown demonstrates that AZD2858 ablates the light-induced auto-interaction between exogenous opto-Topbp1 molecules and ATR plus or minus SN-38, but clearly endogenous Topbp1 molecules do not participate. Why is this? 

The biotin proximity labeling assay was conducted without exposing cells to light, using a TurboID module fused to TopBP1-mCherry-CRY2. Stable cell lines were then generated in HEK293 TrexFlpIn cells, where endogenous TopBP1 is still expressed. Upon adding doxycycline, the recombinant TurboID-TopBP1-mCherry-Cry2 (opto-TopBP1) is induced at levels comparable to endogenous TopBP1 (Fig 2D).

Since the opto-TopBP1 construct exhibits behavior similar to that of endogenous TopBP1 (1), we used it to investigate whether TopBP1 self-assembly and its interaction with ATR are influenced by AZD2858 alone or in combination with SN38. Our results show that treatment with SN38 increases the proximity between opto-TopBP1 and the endogenous TopBP1 (not fused to TurboID). However, AZD2858, either alone or in combination with SN38, disrupts the selfassembly of recombinant TopBP1 with itself as well as its interaction with endogenous TopBP1.

(1) Frattini C, Promonet A, Alghoul E, Vidal-Eychenie S, Lamarque M, Blanchard MP, et al. TopBP1 assembles nuclear condensates to switch on ATR signaling. Molecular Cell. 18 mars 2021;81(6):1231-1245.e8.

Reviewer #3 (Significance (Required)): 

Significance 

Liquid phase separation of protein complexes is increasingly recognised as a fundamental mechanism in signal transduction and other cellular processes. One recent and important example was that of Topbp1, whose condensation in response to DNA damage is required for efficient activation of the ATR-Chk1 pathway. The current study asks a related but distinct question; can protein condensation be targeted by drugs to manipulate signalling pathways which in the main rely on protein kinase cascades? 

Here, the authors identify an inhibitor of GSK3-beta as a novel inhibitor of DNA damage-induced Topbp1 condensation and thus of ATR-Chk1 signalling. 

This work will be of interest to researchers in the fields of DNA damage signalling, biophysics of protein condensation, and cancer chemotherapy.

Author response:

Public Reviews:

Reviewer #1 (Public review):

In this paper by Brickwedde et al., the authors observe an increase in posterior alpha when anticipating auditory as opposed to visual targets. The authors also observe an enhancement in both visual and auditory steady-state sensory evoked potentials in anticipation of auditory targets, in correlation with enhanced occipital alpha. The authors conclude that alpha does not reflect inhibition of early sensory processing, but rather orchestrates signal transmission to later stages of the sensory processing stream. However, there are several major concerns that need to be addressed in order to draw this conclusion.

First, I am not convinced that the frequency tagging method and the associated analyses are adequate for dissociating visual vs auditory steady-state sensory evoked potentials.

Second, if the authors want to propose a general revision for the function of alpha, it would be important to show that alpha effects in the visual cortex for visual perception are analogous to alpha effects in the auditory cortex for auditory perception.

Third, the authors propose an alternative function for alpha - that alpha orchestrates signal transmission to later stages of the sensory processing stream. However, the supporting evidence for this alternative function is lacking. I will elaborate on these major concerns below.

(1) Potential bleed-over across frequencies in the spectral domain is a major concern for all of the results in this paper. The fact that alpha power, 36Hz and 40Hz frequency-tagged amplitude and 4Hz intermodulation frequency power is generally correlated with one another amplifies this concern. The authors are attaching specific meaning to each of these frequencies, but perhaps there is simply a broadband increase in neural activity when anticipating an auditory target compared to a visual target?

We appreciate the reviewer’s insightful comment regarding the potential bleed-over across frequencies in the spectral domain. We fully acknowledge that the trade-off between temporal and frequency resolution is a challenge, particularly given the proximity of the frequencies we are examining.

To address this concern, we performed additional analyses to investigate whether there is indeed a broadband increase in neural activity when anticipating an auditory target as compared to a visual target, as opposed to distinct frequency-specific effects. Our results show that the bleed-over between frequencies is minimal and does not significantly affect our findings. Specifically, we repeated the analyses using the same filter and processing steps for the 44 Hz frequency. At this frequency, we did not observe any significant differences between conditions.

These findings suggest that the effects we report are indeed specific to the 40 Hz frequency band and not due to a general broadband increase in neural activity. We hope this addresses the reviewer’s concern and strengthens the validity of our frequency-specific results.

Author response image 1.

Illustration of bleeding over effects over a span of 4 Hz. A, 40 Hz frequency-tagging data over the significant cluster differing between when expecting an auditory versus a visual target (identical to Fig. 9 in the manuscript). B, 44 Hz signal over the same cluster chosen for A. The analysis was identical with the analysis performed in  A, apart from the frequency for the band-pass filter.

We do, however, not specifically argue against the possibility of a broadband increase when anticipating an auditory compared to a visual target. But even a broadband-increase would directly contradict the alpha inhibition hypothesis, which poses that an increase in alpha completely disengages the whole cortex. We will clarify this point in the revised manuscript.

(2) Moreover, 36Hz visual and 40Hz auditory signals are expected to be filtered in the neocortex. Applying standard filters and Hilbert transform to estimate sensory evoked potentials appears to rely on huge assumptions that are not fully substantiated in this paper. In Figure 4, 36Hz "visual" and 40Hz "auditory" signals seem largely indistinguishable from one another, suggesting that the analysis failed to fully demix these signals.

We appreciate the reviewer’s insightful concern regarding the filtering and demixing of the 36 Hz visual and 40 Hz auditory signals, and we share the same reservations about the reliance on standard filters and the Hilbert transform method.

To address this, we would like to draw attention to Author response image 1, which demonstrates that a 4 Hz difference is sufficient to effectively demix the signals using our chosen filtering and Hilbert transform approach. We believe that the reason the 36 Hz visual and 40 Hz auditory signals show similar topographies lies not in incomplete demixing but rather in the possibility that this condition difference reflects sensory integration, rather than signal contamination.

This interpretation is further supported by our findings with the intermodulation frequency at 4 Hz, which also suggests cross-modal integration. Furthermore, source localization analysis revealed that the strongest condition differences were observed in the precuneus, an area frequently associated with sensory integration processes. We will expand on this in the discussion section to better clarify this point.

(3) The asymmetric results in the visual and auditory modalities preclude a modality-general conclusion about the function of alpha. However, much of the language seems to generalize across sensory modalities (e.g., use of the term 'sensory' rather than 'visual').

We thank the reviewer for pointing this out and agree that in some cases we have not made a good enough distinction between visual and sensory. We will make sure, that when using ‘sensory’, we either describe overall theories, which are not visual-exclusive or refer to the possibility of a broad sensory increase. However, when directly discussing our results and the interpretation thereof, we will now use ‘visual’ in the revised manuscript.

(4) In this vein, some of the conclusions would be far more convincing if there was at least a trend towards symmetry in source-localized analyses of MEG signals. For example, how does alpha power in the primary auditory cortex (A1) compare when anticipating auditory vs visual target? What do the frequency-tagged visual and auditory responses look like when just looking at the primary visual cortex (V1) or A1?

We thank the reviewer for this important suggestion and have added a virtual channel analysis. We were however, not interested in alpha power in primary auditory cortex, as we were specifically interested in the posterior alpha, which is usually increased when expecting an auditory compared to a visual target (and used to be interpreted as a blanket inhibition of the visual cortex). We will improve upon the clarity concerning this point in the manuscript.

We have however, followed the reviewer’s suggestion of a virtual channel analysis, showing that the condition differences are not observable in primary visual cortex for the 36 Hz visual signal and in primary auditory cortex for the 40 Hz auditory signal. Our data clearly shows that there is an alpha condition difference in V1, while there no condition difference for 36 Hz in V1 and for 40 Hz in Heschl’s Gyrus (see Author response image 2).

Author response image 2.

Virtual channels for V1 and Helschl’s gyrus. A, alpha power for the virtual channel created in V1 (Calcerine_L and Calcerine_R from AAL atlas; Tzourio-Mazoyer et al., 2002, NeuroImage). A cluster permutation analysis over time (between -2 and 0) revealed a significant condition difference between ~ -2 and -1.7 s (p = 0.0449). B, 36 Hz frequency-tagging signal for the virtual channel created in V1 (equivalent to the procedure in A). The same cluster permutation as performed in A revealed no significant condition differences. C, 40 Hz frequency-tagging signal for the virtual channel created in Heschl’s gryrus (Heschl_L and Heschl_R from AAL atlas; Tzourio-Mazoyer et al., 2002, NeuroImage). The same cluster permutation as performed in A revealed no significant condition differences.

(5) Blinking would have a huge impact on the subject's ability to ignore the visual distractor. The best thing to do would be to exclude from analysis all trials where the subjects blinked during the cue-to-target interval. The authors mention that in the MEG experiment, "To remove blinks, trials with very large eye-movements (> 10 degrees of visual angle) were removed from the data (See supplement Fig. 5)." This sentence needs to be clarified since eye-movements cannot be measured during blinking. In addition, it seems possible to remove putative blink trials from EEG experiments as well, since blinks can be detected in the EEG signals.

We thank the reviewer for mentioning that we were making this point confusing. From the MEG-data, we removed eyeblinks using ICA. Alone for the supplementary Fig. 5 analysis, we used the eye-tracking data to confirm that participants were in fact fixating the centre of the screen. For this analysis, we removed trials with blinks (which can be seen in the eye-tracker as huge amplitude movements or as large eye-movements in degrees of visual angle; see Author response image 3 below to show a blink in the MEG data and the according eye-tracker data in degrees of visual angle). We will clarify this in the methods section.

As for the concern closed eyes to ignore visual distractors, in both experiments we can observe highly significant distractor cost in accuracy for visual distractors, which we hope will convince the reviewer that our visual distractors were working as intended.

Author response image 3.

Illustration of eye-tracker data for a trial without and a trial with a blink. All data points recorded during this trial are plottet. A, ICA component 1, which reflects blinks and its according data trace in a trial. No blink is visible. B, eye-tracker data transformed into degrees of visual angle for the trial depicted in A. C, ICA component 1, which reflects blinks and its according data trace in a trial. A clear blink is visible. D, eye-tracker data transformed into degrees of visual angle for the trial depicted in C.

(6) It would be interesting to examine the neutral cue trials in this task. For example, comparing auditory vs visual vs neutral cue conditions would be indicative of whether alpha was actively recruited or actively suppressed. In addition, comparing spectral activity during cue-to-target period on neutral-cue auditory correct vs incorrect trials should mimic the comparison of auditory-cue vs visual-cue trials. Likewise, neutral-cue visual correct vs incorrect trials should mimic the attention-related differences in visual-cue vs auditory-cue trials.

We thank the reviewer for this suggestion. We have analysed the neutral cue trials in the EEG dataset (see suppl. Fig. 1) and will expand this figure to show all conditions. There were no significant differences to auditory or visual cues, but descriptively alpha power was higher for neutral cues compared to visual cues and lower for neutral cues compared to auditory cues. While this may suggest that for visual trials alpha is actively suppressed and for auditory trials actively recruited, we do not feel comfortable to make this claim, as the neutral condition may not reflect a completely neutral state. The neutral task can still be difficult, especially because of the uncertainty of the target modality.

As for the analysis of incorrect versus correct trials, we love the idea, but unfortunately the accuracy rate was quite high so that the number of incorrect trials would not be sufficient to perform a reliable analysis.

(7) In the abstract, the authors state that "This implies that alpha modulation does not solely regulate 'gain control' in early sensory areas but rather orchestrates signal transmission to later stages of the processing stream." However, I don't see any supporting evidence for the latter claim, that alpha orchestrates signal transmission to later stages of the processing stream. If the authors are claiming an alternative function to alpha, this claim should be strongly substantiated.

We thank the reviewer for pointing out, that we have not sufficiently explained our case. The first point refers to gain control akin to the alpha inhibition hypothesis, which claims that increases in alpha disengage a whole cortical area. Since we have confirmed the alpha increase in our data to originate from primary visual cortex through source analysis, this should lead to decreased visual processing. The increase in 36 Hz visual processing therefore directly contradicts the alpha inhibition hypothesis. We propose an alternative explanation for the functionality of alpha activity in this task. Through pulsed inhibition, information packages of relevant visual information could be transmitted down the processing stream, thereby enhancing relevant visual signal transmission. We believe the fact that the enhanced visual 36 Hz signal we found correlated with visual alpha power on a trial-by-trial basis, and did not originate from primary visual cortex, but from areas known for sensory integration supports our claim.

We will make this point clearer in our revised manuscript.

Reviewer #2 (Public review):

Brickwedde et al. investigate the role of alpha oscillations in allocating intermodal attention. A first EEG study is followed up with a MEG study that largely replicates the pattern of results (with small to be expected differences). They conclude that a brief increase in the amplitude of auditory and visual stimulus-driven continuous (steady-state) brain responses prior to the presentation of an auditory - but not visual - target speaks to the modulating role of alpha that leads them to revise a prevalent model of gating-by-inhibition.

Overall, this is an interesting study on a timely question, conducted with methods and analysis that are state-of-the-art. I am particularly impressed by the author's decision to replicate the earlier EEG experiment in MEG following the reviewer's comments on the original submission. Evidently, great care was taken to accommodate the reviewer's suggestions.

We thank the reviewer for the positive feedback and expression of interest in the topic of our manuscript.

Nevertheless, I am struggling with the report for two main reasons: It is difficult to follow the rationale of the study, due to structural issues with the narrative and missing information or justifications for design and analysis decisions, and I am not convinced that the evidence is strong, or even relevant enough for revising the mentioned alpha inhibition theory. Both points are detailed further below.

We thank the reviewer for raising this important point. We will revise our introduction and results in line with the reviewer’s suggestions, hoping that our rationale will then be easier to follow and that our evidence will be more convincing.

Strength/relevance of evidence for model revision: The main argument rests on 1) a rather sustained alpha effect following the modality cue, 2) a rather transient effect on steady-state responses just before the expected presentation of a stimulus, and 3) a correlation between those two. Wouldn't the authors expect a sustained effect on sensory processing, as measured by steady-state amplitude irrespective of which of the scenarios described in Figure 1A (original vs revised alpha inhibition theory) applies? Also, doesn't this speak to the role of expectation effects due to consistent stimulus timing? An alternative explanation for the results may look like this: Modality-general increased steady-state responses prior to the expected audio stimulus onset are due to increased attention/vigilance. This effect may be exclusive (or more pronounced) in the attend-audio condition due to higher precision in temporal processing in the auditory sense or, vice versa, too smeared in time due to the inferior temporal resolution of visual processing for the attend-vision condition to be picked up consistently. As expectation effects will build up over the course of the experiment, i.e., while the participant is learning about the consistent stimulus timing, the correlation with alpha power may then be explained by a similar but potentially unrelated increase in alpha power over time.

We thank the reviewer for raising these insightful questions and suggestions.

It is true that our argument rests on a rather sustained alpha effect and a rather transient effect on steady-state responses and a correlation between the two. However, this connection would not be expected under the alpha inhibition hypothesis, which states that alpha activity would inhibit a whole cortical area (when irrelevant to the task), exerting “gain control”. This notion directly contradicts our results of the “irrelevant” visual information a) being transmitted at all and b) increasing.

However, it has been shown on many occasions that alpha activity exerts pulsed inhibition, so we proposed an alternative theory of an involvement in signal transmission. In this case, the cyclic inhibition would serve as an ordering system, which only allows for high-priority information to pass, resulting in higher signa-to-noise. We do not make a claim about how fast or when these signals are transmitted in relation to alpha power. For instance, it could be that alpha power increases as a preparatory state even before signal is actually transmitted.  Zhigalov (2020 Hum. Brain M.) has shown that in V1, frequency-tagging responses were up-and down regulated with attention – independent of alpha activity.

But we do believe that the fact that visual alpha power correlates on a trial-by-trial level with visual 36 Hz frequency-tagging increases and (a relationship which has not been found in V1, see Zhigalov 2020, Hum. Brain Mapp.) suggest a strong connection. Furthermore, the fact that the alpha modulation originates from early visual areas and occurs prior to any frequency-tagging changes, while the increase in frequency-tagging can be observed in areas which are later in the processing stream (such as the precuneus) is strongly indicative for an involvement of alpha power in the transmission of this signal. We cannot fully exclude alternative accounts and mechanisms which effect both alpha power and frequency-tagging responses. 

We do believe that the alternative account described by the reviewer does not contradict our theory, as we do believe that the alpha power modulation may reflect an expectation effect (and the idea that it could be related to the resolution of auditory versus visual processing is very interesting!). It is also possible that this expectation is, as the reviewer suggests, related to attention/vigilance and might result in a modality-general signal increase. And indeed, we can observe an increase in the frequency-tagging response in sensory integration areas. Accordingly, we believe that the alternative explanation provided by the reviewer contradicts the alpha inhibition hypothesis, but not necessarily our alternative theory.

We will revise the discussion, which we hope will make our case stronger and easier to follow. Additionally, we will mention the possibility for alternative explanations as well as the possibility, that alpha networks fulfil different roles in different locations/task environments.

Structural issues with the narrative and missing information: Here, I am mostly concerned with how this makes the research difficult to access for the reader. I list the major points below:

In the introduction the authors pit the original idea about alpha's role in gating against some recent contradictory results. If it's the aim of the study to provide evidence for either/or, predictions for the results from each perspective are missing. Also, it remains unclear how this relates to the distinction between original vs revised alpha inhibition theory (Fig. 1A). Relatedly if this revision is an outcome rather than a postulation for this study, it shouldn't be featured in the first figure.

We agree with the reviewer that we have not sufficiently clarified our goal as well as how different functionalities of alpha oscillations would lead to different outcomes. We will revise the introduction and restructure the results and hope that it will be easier to follow.

The analysis of the intermodulation frequency makes a surprise entrance at the end of the Results section without an introduction as to its relevance for the study. This is provided only in the discussion, but with reference to multisensory integration, whereas the main focus of the study is focussed attention on one sense. (Relatedly, the reference to "theta oscillations" in this sections seems unclear without a reference to the overlapping frequency range, and potentially more explanation.) Overall, if there's no immediate relevance to this analysis, I would suggest removing it.

We thank the reviewer for pointing this out and will add information about this frequency to the introduction part. We believe that the intermodulation frequency analysis is important, as it potentially supports the notion that condition differences in the visual-frequency tagging response are related to downstream processing rather than overall visual information processing in V1. We would therefore prefer to leave this analysis in the manuscript.

Reviewer #3 (Public review):

Brickwedde et al. attempt to clarify the role of alpha in sensory gain modulation by exploring the relationship between attention-related changes in alpha and attention-related changes in sensory-evoked responses, which surprisingly few studies have examined given the prevalence of the alpha inhibition hypothesis. The authors use robust methods and provide novel evidence that alpha likely exhibits inhibitory control over later processing, as opposed to early sensory processing, by providing source-localization data in a cross-modal attention task.

This paper seems very strong, particularly given that the follow-up MEG study both (a) clarifies the task design and separates the effect of distractor stimuli into other experimental blocks, and (b) provides source-localization data to more concretely address whether alpha inhibition is occurring at or after the level of sensory processing, and (c) replicates most of the EEG study's key findings.

We are very grateful to the reviewer for their positive feedback and evaluation of our work.

There are some points that would be helpful to address to bolster the paper. First, the introduction would benefit from a somewhat deeper review of the literature, not just reviewing when the effects of alpha seem to occur, but also addressing how the effect can change depending on task and stimulus design (see review by Morrow, Elias & Samaha (2023).

We thank the reviewer for this suggestion and agree. We will add a paragraph to the introduction which refers to missing correlation studies and the impact of task design.

Additionally, the discussion could benefit from more cautionary language around the revision of the alpha inhibition account. For example, it would be helpful to address some of the possible discrepancies between alpha and SSEP measures in terms of temporal specificity, SNR, etc. (see Peylo, Hilla, & Sauseng, 2021). The authors do a good job speculating as to why they found differing results from previous cross-modal attention studies, but I'm also curious whether the authors think that alpha inhibition/modulation of sensory signals would have been different had the distractors been within the same modality or whether the cues indicated target location, rather than just modality, as has been the case in so much prior work?

We thank the reviewer for suggesting these interesting discussion points and will include a paragraph in our discussion which goes deeper into these topics.

Overall, the analyses and discussion are quite comprehensive, and I believe this paper to be an excellent contribution to the alpha-inhibition literature.

Author Response

We thank the reviewers and editorial team for the positive reaction to our paper and for the constructive recommendations and comments on our work. Here we provide a brief provisional response to key points that were identified. We will give a detailed point-by-point response with highlighted changes in our manuscript when we upload the revised version of our paper.

Reviewer 1:

Statistical evaluation of the null

In Experiment 2, we inferred the existence of a null effect of image category on suppression depth based on frequentist statistics. At the reviewer’s suggestion we performed a statistical evaluation of the evidence in favour of the null effect using a Bayesian repeated measures ANOVA implemented in JASP. That analysis provides strong evidence for the null (BF01= 20.38) and will be included in the final version of the paper.

Likelihood of exceptional cases

We acknowledge that our selection of categories is only a sampling of possible categories to which our novel tCFS method can be applied for deriving suppression depth. Other possibilities that come to mind include objects that emerge from specific configurations of simple 'tokens' such as dots (such as actions defined by biological motion (Watson et al., 2004)) or different shaped tokens configured to generate pareidolia faces (Zhou et al., 2021). We will expand on the possibility of these exceptional cases impacting bCFS and reCFS thresholds in the discussion of our revised manuscript.

Reviewer 2:

In response to the claim “the paper overreaches by claiming breakthrough thresholds are insufficient for drawing certain conclusions about subconscious processing.”

We agree that breakthrough thresholds can provide useful information to draw conclusions about unconscious processing – as our procedure is predicated on breakthrough thresholds. Our key point is that breakthrough provides only half of the needed information and will amend our manuscript accordingly. In so doing, we will also shift our focus toward the influence of semantics and low-level factors, including discussion of the possibility that suppression depth and bCFS thresholds could be driven by statistically orthogonal factors.

Reviewer 3:

On the appropriateness of log-transformed contrast

Our motivation to quantify suppression depth after log-transform to decibel scale was two-fold. First, we recognised that the traditional use of a linear contrast ramp in bCFS is at odds with the well-characterised profile of contrast discrimination thresholds which obey a power law (Legge, 1981) and the observations that neural contrast response functions show the same compressive non-linearity in many different cortical processing areas (e.g.: V1, V2, V3, V4, MT, MST, FST, TEO. See Ekstrom et al., 2009). Increasing contrast in linear steps could thus lead to a rapid saturation of the response function, which may account for the overshoot that has been reported in many canonical bCFS studies. For example, in Jiang et al. (2007), target contrast reached 100% after 1 second, yet average suppression times for faces and inverted faces were 1.36 and 1.76 seconds respectively. As contrast response functions in visual neurons saturate at high contrast, the upper levels of a linear contrast ramp have less and less effect on the target's strength. This approach to response asymptote may have exaggerated small differences between stimulus conditions and may have inflated some previously reported differences. In sum, the use of a log-transformed contrast ramp allows finer increments in contrast to be explored before saturation, a simple manipulation which we hope will be adopted by our field.

Second, by quantifying suppression depth as a decibel change, we enable the comparison of suppression depth between experiments and laboratories, which inevitably differ in presentation environments. As a comparison, a reaction-time for bCFS of 1.36 s cannot easily be compared without access to near-identical stimulation and testing environments. In addition, once ramp contrast is log-transformed it effectively linearises the neural contrast response function. This means that different studies that use different contrast levels for masker or target can be directly compared because a given suppression depth (for example, 15 dB) is the same proportionate difference between bCFS and reCFS regardless of the contrasts used in the particular study.

We also acknowledge that different stimulus categories may engage neural and visual processing associated with different contrast gain values (e.g., magno- vs parvo-mediated processing). But the breaks and returns to suppression of a given stimulus category would be dependent on the same contrast gain function appropriate for that stimulus which thus permits their direct comparison. Indeed, this is why our novel approach offers a promising technique for comparing suppression depth associated with various stimulus categories (a point mentioned above). Viewed in this way, differences in actual durations of break times (such as we report in our paper) may tell us more about differences in gain control within neural mechanisms responsible for processing of those categories.

Consider that preferential processing could shift both bCFS and reCFS thresholds together

This is related to the point raised in the previous comment. A stimulus that is preferentially processed (such as a face) could have lower bCFS and reCFS thresholds than other stimuli such that it emerges into awareness at a lower contrast but also remains visible at lower contrasts. We plan to address this interpretation of our data in our revised discussion and highlight that this type of preferential processing could well occur, and yet could still produce the same uniform suppression depth.

Can the effect of contrast ramp be explained by slower RTs?

A 500 ms reaction time estimate would not account for the magnitude of the changes observed in Experiment 3. Suppression depths in our slow, medium, and fast contrast ramps were 9.64 dB, 14.64 dB and 18.97 dB, respectively (produced by step sizes of .035, .07 and .105 dB per video frame at 60 fps). At each rate, assuming a 500 ms reaction time for both thresholds (1 second total) would capture a change of 2.1 dB, 4.2 dB, 6.3 dB. This difference cannot account for the size of the effects observed between our different ramp speeds.

Non-zero switch rate probability affecting ramping

We agree that for a given ramp speed there is a variable probability of a switch in perceptual state for both bCFS and reCFS portions of the trial. To put it in other words, for a given ramp speed and a given observer the distribution of durations at which transitions occur will exhibit variance. We see that variance in our data (just as it’s present in conventional binocular rivalry duration histograms), as a non-zero probability of switches at very short durations (for example). One might surmise that slower ramp speeds would afford more opportunity for stochastic transitions to occur and that the measured suppression depths for slow ramps are underestimates of the suppression depth produced by contrast adaptation. Yet by the same token, the same underestimation would occur during fast ramp speeds, indicating that that difference may be even larger than we reported. In our revision we will spell this out in more detail, and indicate that a non-zero probability of switches at any time may lead to an underestimation of all recorded suppression depths.

In our data, we believe the contribution of these stochastic switches are minimal. Our current Supplementary Figure 1(d) indicates that there is a non-zero probability of responses early in each ramp (e.g. durations < 2 seconds), yet these are a small proportion of all percept durations. This small proportion is clear in the empirical cumulative density function of percept durations, which we include in Author response image 1, and will address in our detailed response. Notably, during slow-ramp conditions, average percept durations actually increased, implying a resistance to any effect of early stochastic switching. We plan to expand on our analysis of these reaction-time differences in our revised manuscript.

Author response image 1.

The specificity of the DHO fit

In our revised manuscript we will increase the justification for this model, and plan to include a comparison of model fits over time (as opposed to response number in the current manuscript).

References

Ekstrom, L. B., Roelfsema, P. R., Arsenault, J. T., Kolster, H., & Vanduffel, W. (2009). Modulation of the contrast response function by electrical microstimulation of the macaque frontal eye field. The Journal of Neuroscience: The Official Journal of the Society for Neuroscience, 29(34), 10683–10694.

Jiang, Y., Costello, P., & He, S. (2007). Processing of invisible stimuli: advantage of upright faces and recognizable words in overcoming interocular suppression. Psychological Science, 18(4), 349–355.

Legge, G. E. (1981). A power law for contrast discrimination. Vision Research, 21(4), 457–467.

Watson, T. L., Pearson, J., & Clifford, C. W. G. (2004). Perceptual grouping of biological motion promotes binocular rivalry. Current Biology: CB, 14(18), 1670–1674.

Zhou, L.-F., Wang, K., He, L., & Meng, M. (2021). Twofold advantages of face processing with or without visual awareness. Journal of Experimental Psychology. Human Perception and Performance, 47(6), 784–794.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This paper is an elegant, mostly observational work, detailing observations that polysome accumulation appears to drive nucleoid splitting and segregation. Overall I think this is an insightful work with solid observations.

Thank you for your appreciation and positive comments. In our view, an appealing aspect of this proposed biophysical mechanism for nucleoid segregation is its self-organizing nature and its ability to intrinsically couple nucleoid segregation to biomass growth, regardless of nutrient conditions.

Strengths:

The strengths of this paper are the careful and rigorous observational work that leads to their hypothesis. They find the accumulation of polysomes correlates with nucleoid splitting, and that the nucleoid segregation occurring right after splitting correlates with polysome segregation. These correlations are also backed up by other observations:

(1) Faster polysome accumulation and DNA segregation at faster growth rates.

(2) Polysome distribution negatively correlating with DNA positioning near asymmetric nucleoids.

(3) Polysomes form in regions inaccessible to similarly sized particles.

These above points are observational, I have no comments on these observations leading to their hypothesis.

Thank you!

Weaknesses:

It is hard to state weaknesses in any of the observational findings, and furthermore, their two tests of causality, while not being completely definitive, are likely the best one could do to examine this interesting phenomenon.

It is indeed difficult to prove causality in a definitive manner when the proposed coupling mechanism between nucleoid segregation and gene expression is self-organizing, i.e., does not involve a dedicated regulatory molecule (e.g., a protein, RNA, metabolite) that we could have depleted through genetic engineering to establish causality. We are grateful to the reviewer for recognizing that our two causality tests are the best that can be done in this context.

Points to consider / address:

Notably, demonstrating causality here is very difficult (given the coupling between transcription, growth, and many other processes) but an important part of the paper. They do two experiments toward demonstrating causality that help bolster - but not prove - their hypothesis. These experiments have minor caveats, my first two points.

(1) First, "Blocking transcription (with rifampicin) should instantly reduce the rate of polysome production to zero, causing an immediate arrest of nucleoid segregation". Here they show that adding rifampicin does indeed lead to polysome loss and an immediate halting of segregation - data that does fit their model. This is not definitive proof of causation, as rifampicin also (a) stops cell growth, and (b) stops the translation of secreted proteins. Neither of these two possibilities is ruled out fully.

That’s correct; cell growth also stops when gene expression is inhibited, which is consistent with our model in which gene expression within the nucleoid promotes nucleoid segregation and biomass growth (i.e., cell growth), inherently coupling these two processes. This said, we understand the reviewer’s point: the rifampicin experiment doesn’t exclude the possibility that protein secretion and cell growth drive nucleoid segregation. We are assuming that the reviewer is envisioning an alternative model in which sister nucleoids would move apart because they would be attached to the membrane through coupled transcription-translation-protein secretion (transertion) and the membrane would expand between the separating nucleoids, similar to the model proposed by Jacob et al in 1963 (doi:10.1101/SQB.1963.028.01.048). There are several observations arguing against this cell elongation/transertion model.

(1) For this alternative mechanism to work, membrane growth must be localized at the middle of the splitting nucleoids (i.e., midcell position for slow growth and ¼ and ¾ cell positions for fast growth) to create a directional motion. To our knowledge, there is no evidence of such localized membrane incorporation. Furthermore, even if membrane growth was localized at the right places, the fluidity of the cytoplasmic membrane (PMID: 6996724, 20159151, 24735432, 27705775) would be problematic. To circumvent the membrane fluidity issue, one could potentially evoke an additional connection to the rigid peptidoglycan, but then again, peptidoglycan growth would have to be localized at the middle of the splitting nucleoid. However, peptidoglycan growth is dispersed early in the cell division cycle when the nucleoid splitting happens in fast growing cells and only appears to be zonal after the onset of cell constriction (PMID: 35705811, 36097171, 2656655).

(2) Even if we ignore the aforementioned caveats, Paul Wiggins’s group ruled out the cell elongation/transertion model by showing that the rate of cell elongation is slower than the rate of chromosome segregation (PMID: 23775792). In the revised manuscript, we wil clarify this point and provide confirmatory data showing that the cell elongation rate is indeed slower than the nucleoid segregation rate, indicating that it cannot be the main driver.

(3) Furthermore, our correlation analysis comparing the rate of nucleoid segregation to the rate of either cell elongation or polysome accumulation argues that polysome accumulation plays a larger role than cell elongation in nucleoid segregation. These data were already shown in Figure 1H and Figure 1 – figure supplement 3 of the original manuscript but were not highlighted in this context. We will revise the text to clarify this point.

(4) The asymmetries in nucleoid compaction that we described in our paper are predicted by our model. We do not see how they could be explained by cell growth or protein secretion.

(5) We also show that polysome accumulation at ectopic sites (outside the nucleoid) results in correlated nucleoid dynamics, consistent with our proposed mechanism. These nucleoid dynamics cannot be explained by cell growth or protein secretion (transertion).

(1a) As rifampicin also stops all translation, it also stops translational insertion of membrane proteins, which in many old models has been put forward as a possible driver of nucleoid segregation, and perhaps independent of growth. This should at last be mentioned in the discussion, or if there are past experiments that rule this out it would be great to note them.

It is not clear to us how the attachment of the DNA to the cytoplasmic membrane could alone create a directional force to move the sister nucleoids. We agree that old models have proposed a role for cell elongation (providing the force) and transertion (providing the membrane tether).  Please see our response above for the evidence (from the literature and our work) against it. This was mentioned in the introduction and Results section, but we agree that this was not well explained. We will add experimental data and revise the text to clarify these points.

(1b) They address at great length in the discussion the possibility that growth may play a role in nucleoid segregation. However, this is testable - by stopping surface growth with antibiotics. Cells should still accumulate polysomes for some time, it would be easy to see if nucleoids are still segregated, and to what extent, thereby possibly decoupling growth and polysome production. If successful, this or similar experiments would further validate their model.

We reviewed the literature and could not find a drug that stops cell growth without stopping gene expression. Any drug that affects the membrane integrity or potential stops gene expression, which requires ATP.  However, our experiment in which we drive polysome accumulation at ectopic sites decouples polysome accumulation from cell growth. In this experiment, by redirecting most of chromosome gene expression to a single plasmid-encoded gene, we reduce the rate of cell growth but still create a large accumulation of polysomes at an ectopic location. This ectopic polysome accumulation is sufficient to affect nucleoid dynamics in a correlated fashion. In the revised manuscript, we will clarify this point and add model simulations to show that our experimental observations are predicted by our model.

(2) In the second experiment, they express excess TagBFP2 to delocalize polysomes from midcell. Here they again see the anticorrelation of the nucleoid and the polysomes, and in some cells, it appears similar to normal (polysomes separating the nucleoid) whereas in others the nucleoid has not separated. The one concern about this data - and the differences between the "separated" and "non-separated" nuclei - is that the over-expression of TagBFP2 has a huge impact on growth, which may also have an indirect effect on DNA replication and termination in some of these cells. Could the authors demonstrate these cells contain 2 fully replicated DNA molecules that are able to segregate?

We will perform the requested experiment.

(3) What is not clearly stated and is needed in this paper is to explain how polysomes do (or could) "exert force" in this system to segregate the nucleoid: what a "compaction force" is by definition, and what mechanisms causes this to arise (what causes the "force") as the "compaction force" arises from new polysomes being added into the gaps between them caused by thermal motions.

They state, "polysomes exert an effective force", and they note their model requires "steric effects (repulsion) between DNA and polysomes" for the polysomes to segregate, which makes sense. But this makes it unclear to the reader what is giving the force. As written, it is unclear if (a) these repulsions alone are making the force, or (b) is it the accumulation of new polysomes in the center by adding more "repulsive" material, the force causes the nucleoids to move. If polysomes are concentrated more between nucleoids, and the polysome concentration does not increase, the DNA will not be driven apart (as in the first case) However, in the second case (which seems to be their model), the addition of new material (new polysomes) into a sterically crowded space is not exerting force - it is filling in the gaps between the molecules in that region, space that needs to arise somehow (like via Brownian motion). In other words, if the polysome region is crowded with polysomes, space must be made between these polysomes for new polysomes to be inserted, and this space must be made by thermal (or ATP-driven) fluctuations of the molecules. Thus, if polysome accumulation drives the DNA segregation, it is not "exerting force", but rather the addition of new polysomes is iteratively rectifying gaps being made by Brownian motion.

We apologize for the understandable confusion. In our picture, the polysomes and DNA (conceptually considered as small plectonemic segments) basically behave as dissolved particles. If these particles were noninteracting, they would simply mix. However, both polysomes and DNA segments are large enough to interact sterically. So as density increases, steric avoidance implies a reduced conformational entropy and thus a higher free energy per particle. We argue (based on Miangolarra et al. PNAS 2021 PMID: 34675077 and Xiang et al. Cell 2021 PMID: 34186018) that the demixing of polysomes and DNA segments occurs because DNA segments pack better with each other than they do with polysomes. This raises the free energy cost associated with DNA-polysome interactions compared to DNA-DNA interactions.  We model this effect by introducing a term in the free energy χ_np, which refer to as a repulsion between DNA and polysomes, though as explained above it arises from entropic effects. At realistic cellular densities of DNA and polysomes this repulsive interaction is strong enough to cause the DNA and polysomes to phase separate.

This same density-dependent free energy that causes phase separation can also give rise to forces, just in the way that a higher pressure on one side of a wall can give rise to a net force on the wall. Indeed, the “compaction force” we refer to is fundamentally an osmotic pressure difference. At some stages during nucleoid segregation, the region of the cell between nucleoids has a higher polysome concentration, and therefore a higher osmotic pressure, than the regions near the poles. This results in a net poleward force on the sister nucleoids that drives their migration toward the poles. This migration continues until the osmotic pressure equilibrates. Therefore, both phase separation (due to the steric repulsion described above) and nonequilibrium polysome production and degradation (which creates the initial accumulation of polysomes around midcell) are essential ingredients for nucleoid segregation.

This will be clarified in the revised text, with the support of additional simulation results.

The authors use polysome accumulation and phase separation to describe what is driving nucleoid segregation. Both terms are accurate, but it might help the less physically inclined reader to have one term, or have what each of these means explicitly defined at the start. I say this most especially in terms of "phase separation", as the currently huge momentum toward liquid-liquid interactions in biology causes the phrase "phase separation" to often evoke a number of wider (and less defined) phenomena and ideas that may not apply here. Thus, a simple clear definition at the start might help some readers.

Phase separation means that the DNA-polysome steric repulsion is strong enough to drive their demixing, which creates a compact nucleoid. As mentioned in a previous point, this effect is captured in the free energy by the χ_np term, which is an effective repulsion between DNA and polysomes, though as explained above it arises from entropic effects.

In the revised manuscript, we will illustrate this with our theoretical model by initializing a cell with a diffuse nucleoid and low polysome concentration. For the sake of simplicity, we assume that the cell does not elongate. We observe that the DNA-polysome steric repulsion is sufficient to compact the nucleoid and place it at mid-cell.

(4) Line 478. "Altogether, these results support the notion that ectopic polysome accumulation drives nucleoid dynamics". Is this right? Should it not read "results support the notion that ectopic polysome accumulation inhibits/redirects nucleoid dynamics"?

We think that this is correct; the ectopic polysome accumulation drives nucleoid dynamics. In our theoretical model, we can introduce polysome production at fixed sources to mimic the experiments where ectopic polysome production is achieved by high plasmid expression (Fig. 6). The model is able to recapitulate the two main phenotypes observed in experiments. These new simulation results will be added to the revised manuscript.

(5) It would be helpful to clarify what happens as the RplA-GFP signal decreases at midcell in Figure 1- is the signal then increasing in the less "dense" parts of the cell? That is, (a) are the polysomes at midcell redistributing throughout the cell? (b) is the total concentration of polysomes in the entire cell increasing over time?

It is a redistribution—the RplA-GFP signal remains constant in concentration from cell birth to division (Figure 1 – Figure Supplement 1E). This will be clarified in the revised text.

(6) Line 154. "Cell constriction contributed to the apparent depletion of ribosomal signal from the mid-cell region at the end of the cell division cycle (Figure 1B-C and Movie S1)" - It would be helpful if when cell constriction began and ended was indicated in Figures 1B and C.

Good idea. We will add markers to indicate the start of cell constriction. We will also indicate that cell birth and division correspond to the first and last images/timepoint in Fig. 1B and C, respectively.

(7) In Figure 7 they demonstrate that radial confinement is needed for longitudinal nucleoid segregation. It should be noted (and cited) that past experiments of Bacillus l-forms in microfluidic channels showed a clear requirement role for rod shape (and a given width) in the positing and the spacing of the nucleoids.

Wu et al, Nature Communications, 2020 . "Geometric principles underlying the proliferation of a model cell system" https://dx.doi.org/10.1038/s41467-020-17988-7

Good point. We will add this reference. Thank you.

(8) "The correlated variability in polysome and nucleoid patterning across cells suggests that the size of the polysome-depleted spaces helps determine where the chromosomal DNA is most concentrated along the cell length. This patterning is likely reinforced through the displacement of the polysomes away from the DNA dense region"

It should be noted this likely functions not just in one direction (polysomes dictating DNA location), but also in the reverse - as the footprint of compacted DNA should also exclude (and thus affect) the location of polysomes

We agree that the effects could go both ways at this early stage of the story. We will revise the text accordingly.  

(9) Line 159. Rifampicin is a transcription inhibitor that causes polysome depletion over time. This indicates that all ribosomal enrichments consist of polysomes and therefore will be referred to as polysome accumulations hereafter". Here and throughout this paper they use the term polysome, but cells also have monosomes (and 2 somes, etc). Rifampicin stops the assembly of all of these, and thus the loss of localization could occur from both. Thus, is it accurate to state that all transcription events occur in polysomes? Or are they grouping all of the n-somes into one group?

In the discussion, we noted that our term “polysomes” also includes monosomes for simplicity, but we agree that the term should have been defined much earlier. This will be done in the revised manuscript.

Thank you for the valuable comments and suggestions!

Reviewer #2 (Public review):

Summary:

The authors perform a remarkably comprehensive, rigorous, and extensive investigation into the spatiotemporal dynamics between ribosomal accumulation, nucleoid segregation, and cell division. Using detailed experimental characterization and rigorous physical models, they offer a compelling argument that nucleoid segregation rates are determined at least in part by the accumulation of ribosomes in the center of the cell, exerting a steric force to drive nucleoid segregation prior to cell division. This evolutionarily ingenious mechanism means cells can rely on ribosomal biogenesis as the sole determinant for the growth rate and cell division rate, avoiding the need for two separate 'sensors,' which would require careful coupling.

Terrific summary! Thank you for your positive assessment.

Strengths:

In terms of strengths; the paper is very well written, the data are of extremely high quality, and the work is of fundamental importance to the field of cell growth and division. This is an important and innovative discovery enabled through a combination of rigorous experimental work and innovative conceptual, statistical, and physical modeling.

Thank you!

Weaknesses:

In terms of weaknesses, I have three specific thoughts.

Firstly, my biggest question (and this may or may not be a bona fide weakness) is how unambiguously the authors can be sure their ribosomal labeling is reporting on polysomes, specifically. My reading of the work is that the loss of spatial density upon rifampicin treatment is used to infer that spatial density corresponds to polysomes, yet this feels like a relatively indirect way to get at this question, given rifampicin targets RNA polymerase and not translation. It would be good if a more direct way to confirm polysome dependence were possible.

The heterogeneity of ribosome distribution inside E. coli cells has been attributed to polysomes by many labs (PMID: 25056965, 38678067, 22624875, 31150626, 34186018, 10675340).  The attribution is also consistent with single-molecule tracking experiments showing that slow-moving ribosomes (polysomes) are excluded by the nucleoid whereas fast-diffusing ribosomes (free ribosomal subunits) are distributed throughout the cytoplasm (PMID: 25056965, 22624875).

Furthermore, inhibition of translation initiation with kasugamycin treatment, which decreases the pool of polysomes, results in a homogenization of ribosomes and expansion of the nucleoid (see Author response image 1). This further supports the rifampicin experiments. Given that the attribution of ribosome heterogeneity to polysomes is well accepted in the field, we would prefer to not include these kasugamycin data in the revised manuscript because long-term exposure to this drug leads to nucleoid re-compaction (PMID: 25250841 and PMID: 34186018). This secondary effect may possibly be due to a dysregulated increase in synthesis of naked rRNAs (PMID: 14460744, PMID: 2114400, and PMID: 2448483) or ribosome aggregation, which we are currently investigating.

Author response image 1.

Effects of kasugamycin treatment on the intracellular distribution of ribosomes and nucleoids. Representative single cell (CJW7323) growing in M9gluCAAT.  Kasugamycin (3 mg/mL) was added at time = 0 min. Show is the early response (0-30 min) to the drug characterized by the homogenization of the ribosomal RplA-GFP fluorescence and the expansion of the HupA-mCherry-labeled nucleoids. For each segmented cell, the RplA-GFP and HupA-mCherry signals were normalized by the average fluorescence.

Second, the authors invoke a phase separation model to explain the data, yet it is unclear whether there is any particular evidence supporting such a model, whether they can exclude simpler models of entanglement/local diffusion (and/or perhaps this is what is meant by phase separation?) and it's not clear if claiming phase separation offers any additional insight/predictive power/utility. I am OK with this being proposed as a hypothesis/idea/working model, and I agree the model is consistent with the data, BUT I also feel other models are consistent with the data. I also very much do not think that this specific aspect of the paper has any bearing on the paper's impact and importance.

We appreciate the reviewer’s comment, but the output of our reaction-diffusion model is a bona fide phase separation (spinodal decomposition). So, we feel that we need to use the term when reporting the modeling results. Inside the cell, the situation is more complicated. As the reviewer points out, there likely are entanglements (not considered in our model) and other important factors (please see our discussion on the model limitations). This said, we will revise our text to clarify our terms and proposed mechanism.

Finally, the writing and the figures are of extremely high quality, but the sheer volume of data here is potentially overwhelming. I wonder if there is any way for the authors to consider stripping down the text/figures to streamline things a bit? I also think it would be useful to include visually consistent schematics of the question/hypothesis/idea each of the figures is addressing to help keep readers on the same page as to what is going on in each figure. Again, there was no figure or section I felt was particularly unclear, but the sheer volume of text/data made reading this quite the mental endurance sport! I am completely guilty of this myself, so I don't think I have any super strong suggestions for how to fix this, but just something to consider.

We agree that there is a lot to digest. We will add schematics and a didactic simulation. We will also try to streamline the text.

Reviewer #3 (Public review):

Summary:

Papagiannakis et al. present a detailed study exploring the relationship between DNA/polysome phase separation and nucleoid segregation in Escherichia coli. Using a combination of experiments and modelling, the authors aim to link physical principles with biological processes to better understand nucleoid organisation and segregation during cell growth.

Strengths:

The authors have conducted a large number of experiments under different growth conditions and physiological perturbations (using antibiotics) to analyse the biophysical factors underlying the spatial organisation of nucleoids within growing E. coli cells. A simple model of ribosome-nucleoid segregation has been developed to explain the observations.

Weaknesses:

While the study addresses an important topic, several aspects of the modelling, assumptions, and claims warrant further consideration.

Thank you for your feedback. Please see below for a response to each concern. 

Major Concerns:

Oversimplification of Modelling Assumptions:

The model simplifies nucleoid organisation by focusing on the axial (long-axis) dimension of the cell while neglecting the radial dimension (cell width). While this approach simplifies the model, it fails to explain key experimental observations, such as:

(1) Inconsistencies with Experimental Evidence:

The simplified model presented in this study predicts that translation-inhibiting drugs like chloramphenicol would maintain separated nucleoids due to increased polysome fractions. However, experimental evidence shows the opposite-separated nucleoids condense into a single lobe post-treatment (Bakshi et al 2014), indicating limitations in the model's assumptions/predictions. For the nucleoids to coalesce into a single lobe, polysomes must cross the nucleoid zones via the radial shells around the nucleoid lobes.

We do not think that the results from chloramphenicol-treated cells are inconsistent with our model. Our proposed mechanism predicts that nucleoids will condense in the presence of chloramphenicol, consistent with experiments. It also predicts that nucleoids that were still relatively close at the time of chloramphenicol treatment could fuse if they eventually touched through diffusion (thermal fluctuation) to reduce their interaction with the polysomes and minimize their conformational energy. Fusion is, however, not expected for well-separated nucleoids since their diffusion is slow in the crowded cytoplasm. This is consistent with our experimental observations: In the presence of a growth-inhibitory concentration of chloramphenicol (70 μg/mL), nucleoids in relatively close proximity can fuse, but well-separated nucleoids condense and do not fuse. Since the growth rate inhibition is not immediate upon chloramphenicol treatment, many cells with well-separated condensed nucleoids divide during the first hour. As a result, the non-fusion phenotype is more obvious in non-dividing cells, achieved by pre-treating cells with the cell division inhibitor cephalexin (50μg/mL). In these polyploid elongated cells, well-separated nucleoids condensed but did not fuse, not even after an hour in the presence of chloramphenicol (as illustrated in Author response image 2).

In Bakshi et al, 2014, nucleoid fusion was shown for a single cell in which the sister nucleoids were relatively close to each other at the time of chloramphenicol treatment. Population statistics were provided for the relative length and width of the nucleoids, but not for the fusion events. So, it is unclear whether the illustrated fusion was universal or not. Also, we note that Bakshi et al (2014) used a chloramphenicol concentration of 300 μg/mL, which is 20-fold higher than the minimal inhibitory concentration for growth, compared to 70 μg/mL in our experiments.

Author response image 2.

Effects of chloramphenicol treatment on the intracellular distribution of ribosomes and nucleoids in non-dividing cells. Exponentially growing cells (M9glyCAAT at 30°C) were pre-treated with cephalexin for one hour before being spotted on an 1% agarose pad for time-lapse imaging. The agarose pad contained M9glyCAAT, cephalexin, and chloramphenicol.  (A) Phase contrast, RplA-GFP fluorescence and HupA-mCherry fluorescence images of a representative single cell. Three timepoints are shown, including the first image after spotting on the agarose pad (at 0 min), 30 minutes and one hour of chloramphenicol treatment. (B) One-dimensional profiles of the ribosomal (RplA-GFP) and nucleoid (HupA-mCherry) fluorescence from the cells shown in panel A. These intensity profiles correspond to the average fluorescence along the medial axis of the cell considering a 6-pixel region (0.4 μm) centered on the central line of the cell. The fluorescence intensity is plotted along the relative cell length, scaled from 0 to 100% between the two poles, illustrating the relative nucleoid length (L_DNA/L_cell) that was plotted by Bakshi et al in 2014 (PMID: 25250841).

(2) The peripheral localisation of nucleoids observed after A22 treatment in this study and others (e.g., Japaridze et al., 2020; Wu et al., 2019), which conflicts with the model's assumptions and predictions. The assumption of radial confinement would predict nucleoids to fill up the volume or ribosomes to go near the cell wall, not the nucleoid, as seen in the data.

The reviewer makes a good point that DNA attachment to the membrane through transertion likely contributes to the nucleoid being peripherally localized in A22 cells. We will revise the text to add this point. However, we do not think that this contradicts the proposed nucleoid segregation mechanism based on phase separation and out-of-equilibrium dynamics described in our model. On the contrary, by attaching the nucleoid to the cytoplasmic membrane along the cell width, transertion might help reduce the diffusion and thus exchange of polysomes across nucleoids. We will revise the text to discuss transertion over radial confinement.

(3) The radial compaction of the nucleoid upon rifampicin or chloramphenicol treatment, as reported by Bakshi et al. (2014) and Spahn et al. (2023), also contradicts the model's predictions. This is not expected if the nucleoid is already radially confined.

We originally evoked radial confinement to explain the observation that polysome accumulations do not equilibrate between DNA-free regions. We agree that transertion is an alternative explanation. Thank you for bringing it to our attention. However, please note that this does not contradict the model. In our view, it actually supports the 1D model by providing a reasonable explanation for the slow exchange of polysomes across DNA-free regions. The attachment of the nucleoid to the membrane along the cell width may act as diffusion barrier. We will revise the text and the title of the manuscript accordingly.

(4) Radial Distribution of Nucleoid and Ribosomal Shell:

The study does not account for well-documented features such as the membrane attachment of chromosomes and the ribosomal shell surrounding the nucleoid, observed in super-resolution studies (Bakshi et al., 2012; Sanamrad et al., 2014). These features are critical for understanding nucleoid dynamics, particularly under conditions of transcription-translation coupling or drug-induced detachment. Work by Yongren et al. (2014) has also shown that the radial organisation of the nucleoid is highly sensitive to growth and the multifork nature of DNA replication in bacteria.

We will discuss the membrane attachment. Please see the previous response.

The omission of organisation in the radial dimension and the entropic effects it entails, such as ribosome localisation near the membrane and nucleoid centralisation in expanded cells, undermines the model's explanatory power and predictive ability. Some observations have been previously explained by the membrane attachment of nucleoids (a hypothesis proposed by Rabinovitch et al., 2003, and supported by experiments from Bakshi et al., 2014, and recent super-resolution measurements by Spahn et al.).

We agree—we will add a discussion about membrane attachment in the radial dimension. See previous responses.

Ignoring the radial dimension and membrane attachment of nucleoid (which might coordinate cell growth with nucleoid expansion and segregation) presents a simplistic but potentially misleading picture of the underlying factors.

As mentioned above, we will discuss membrane attachment in the revised manuscript.

This reviewer suggests that the authors consider an alternative mechanism, supported by strong experimental evidence, as a potential explanation for the observed phenomena:

Nucleoids may transiently attach to the cell membrane, possibly through transertion, allowing for coordinated increases in nucleoid volume and length alongside cell growth and DNA replication. Polysomes likely occupy cellular spaces devoid of the nucleoid, contributing to nucleoid compaction due to mutual exclusion effects. After the nucleoids separate following ter separation, axial expansion of the cell membrane could lead to their spatial separation.

This “membrane attachment/cell elongation” model is reminiscent to the hypothesis proposed by Jacob et al in 1963 (doi:10.1101/SQB.1963.028.01.048). There are several lines of evidence arguing against it as the major driver of nucleoid segregation:

(Below is a slightly modified version of our response to a comment from Reviewer 1—see page 3)

(1) For this alternative model to work, axial membrane expansion (i.e., cell elongation) would have to be localized at the middle of the splitting nucleoids (i.e., midcell position for slow growth and ¼ and ¾ cell positions for fast growth) to create a directional motion. To our knowledge, there is no evidence of such localized membrane incorporation.  Furthermore, even if membrane growth was localized at the right places, the fluidity of the cytoplasmic membrane (PMID: 6996724, 20159151, 24735432, 27705775) would be problematic. To go around this fluidity issue, one could potentially evoke a potential connection to the rigid peptidoglycan, but then again, peptidoglycan growth would have to be localized at the middle of the splitting nucleoid to “push” the sister nucleoid apart from each other. However, peptidoglycan growth is dispersed prior to cell constriction (PMID: 35705811, 36097171, 2656655).

(2) Even if we ignore the aforementioned caveats, Paul Wiggins’s group ruled out the cell elongation/transertion model by showing that the rate of cell elongation is slower than the rate of chromosome segregation (PMID: 23775792). In the revised manuscript, we will provide additional data showing that the cell elongation rate is indeed slower than the nucleoid segregation rate.

(3) Furthermore, our correlation analysis comparing the rate of nucleoid segregation to the rate of either cell elongation or polysome accumulation argues that polysome accumulation plays a larger role than cell elongation in nucleoid segregation. These data were already shown in the original manuscript (Figure 1I and Figure 1 – figure supplement 3) but were not highlighted in this context. We will revise the text to clarify this point.

(4) The membrane attachment/cell elongation model does not explain the nucleoid asymmetries described in our paper (Figure 3), whereas they can be recapitulated by our model.

(5) The cell elongation/transertion model cannot predict the aberrant nucleoid dynamics observed when chromosomal expression is largely redirected to plasmid expression. In the revised manuscript, we will add simulation results showing that these nucleoid dynamics are predicted by our model.

In line of these arguments, we do not believe that a mechanism based on membrane attachment and cell elongation is the major driver of nucleoid segregations. However, we do believe that it may play a complementary role (see “Nucleoid segregation likely involves multiple factors” in the Discussion). We will revise this section to clarify our thoughts and mention the potential role of transertion.

Incorporating this perspective into the discussion or future iterations of the model may provide a more comprehensive framework that aligns with the experimental observations in this study and previous work.

As noted above, we will revise the text to mention about transertion.

Simplification of Ribosome States:

Combining monomeric and translating ribosomes into a single 'polysome' category may overlook spatial variations in these states, particularly during ribosome accumulation at the mid-cell. Without validating uniform mRNA distribution or conducting experimental controls such as FRAP or single-molecule measurements to estimate the proportions of ribosome states based on diffusion, this assumption remains speculative.

Indeed, for simplicity, we adopt an average description of all polysomes with an average diffusion coefficient and interaction parameters, which is sufficient for capturing the fundamental mechanism underlying nucleoid segregation. To illustrate that considering multiple polysome species does not change the physical picture, we consider an extension of our model, which contains three polysome species, each with a different diffusion coefficient (D<SUB>P</SUB> = 0.018, 0.023, or 0.028 μm²/s), reflecting that polysomes with more ribosomes will have a lower diffusion coefficient. Simulation of this model reveals that the different polysome species have essentially the same concentration distribution, suggesting that the average description in our minimal model is sufficient for our purposes. We will present these new simulation results in the revised manuscript.

Author Response

Reviewer #1 (Public Review):

Summary:

Alonso-Calleja and colleagues explore the role of TGR5 in adult hematopoiesis at both steady state and post-transplantation. The authors utilize two different mouse models including a TGR5-GFP reporter mouse to analyze the expression of TGR5 in various hematopoietic cell subsets. Using germline Tgr5-/- mice it's reported that loss of Tgr5 has no significant impact on steady-state hematopoiesis, with a small decrease in trabecular bone fraction, associated with a reduction in proximal tibia adipose tissue, and an increase in marrow phenotypic adipocytic precursors. The authors further explored the role of stroma TGR5 expression in the hematopoietic recovery upon bone marrow transplantation of wild-type cells, although the studies supporting this claim are weak. Overall, while most of the hematopoietic phenotypes have negative results or small effects, the role of TGR5 in adipose tissue regulation is interesting to the field.

We thank Reviewer 1 for having identified some strengths and weaknesses of our study. As summarized below, we will work to consolidate the weaknesses of our study.

Strengths:

• This is the first time the role of TGR5 has been examined in the bone marrow.

• This paper supports further exploration of the role of bile acids in bone marrow transplantation and possible therapeutic strategies.

Weaknesses:

• The authors fail to describe whether niche stroma cells or adipocyte progenitor cells (APCs) express TGR5.

We are currently working to address this question using our reporter model and expect to be able to provide the data in the next version of the reviewed preprint.

• Although the authors note a significant reduction in bone marrow adipose tissue in Tgr5-/- mice, they do not address whether this is white or brown adipose tissue especially since BA-TGR5 signaling has been shown to play a role in beiging.

The nature of BMAT and how it relates to brown, white or brown/beige adipose tissue has been a persistent question in the field. Our understanding is that BMAT is currently considered a distinct adipose depot that is neither white nor brown/beige. BMAT does not express UCP1 to an appreciable extent, with reports showing its expressing possibly detecting contamination by tissues surrounding bone (Craft et al., 2019). Beyond this consideration, as the regulated BMAT in TGR5-/- mice is almost absent, determination of the brown/beige vs white nature of the regulated BMAT remains technically challenging.

In Figure 1, the authors explore different progenitor subsets but stop short of describing whether TGR5 is expressed in hematopoietic stem cells (HSCs).

Figure 1 of the originally submitted manuscript described TGR5 expression in committed myeloid progenitors (CMP, GMP and MEP). Below we provide the requested data (expression in MPPs and HSCs in Author response image 1) and we have further expanded our data with the expression in megakaryocyte progenitors (MkProg - Lin-cKit+Sca1-CD41+CD150+) as shown in Author response image 2.

Author response image 1.

Frequencies of GFP+ cells in MPPs and HSCs in the BM of 8-12-week-old male TGR5:GFP mice and their controls (n=9 for Wild-type control mice, n=11 for TGR5:GFP mice). Results represent the mean ± s.e.m., n represents biologically independent replicates. Two-tailed Student’s t-test was used for statistical analysis. p-values (exact value) are indicated.

Author response image 2.

A, representative flow cytometry gating strategy used to identify megakaryocyte progenitors (MkProg) and GFP positivity in TGR5:GFP mice and their wild-type controls. B, frequencies of GFP+ cells in MkProg population in the BM of 8-12-week-old male TGR5:GFP mice and their controls (n=3 for Wild-type control mice, n=4 for TGR5:GFP mice). Results represent the mean ± s.e.m., n represents biologically independent replicates. Two-tailed Student’s t-test (B) was used for statistical analysis. p-values (exact value) are indicated.

• Are there more CD45+ cells in the BM because hematopoietic cells are proliferating more due to a direct effect of the loss of Tgr5 or is it because there is just more space due to less trabecular bone?

While we do not have direct evidence to address this question, we see approximately an average 20% increase in CD45+ cell counts in the baseline Tgr5-/- mice. The absolute volume of bone and BMAT lost in these animals does not account for 20% of the total volume of the medullary cavity, so we speculate that the increase in CD45+ counts is not due exclusively to an increase in available volume.

• In Figure 4 no absolute cell counts are provided to support the increase in immunophenotypic APCs (CD45-Ter119-CD31-Sca1+CD24-) in the stroma of Tgr5-/- mice. Accordingly, the absolute number of total stromal cells and other stroma niche cells such as MSCs, ECs are missing.

We initially chose not to report the total number of cells per leg, as the processing of the bones for stroma isolation is less homogenous than that of the HSPC populations (which we do by crushing whole bones with a mortar and pestle). Regardless of these considerations, the data for absolute counts of APCs (left panel), the stroma-enriched fraction (CD45-Ter119-CD31- - middle panel) and endothelial cells (CD45-Ter119-CD31+ - right panel) is provided in Author response image 3. Note that the number of cells plated for CFU-F and BMSC in vitro differentiation is constant between the genotypes, thus confirming the importance of ther elative abundance data shown in the submitted version of the manuscript. In conclusion, we have prioritized the data showing the relative overrepresentation of APC progenitors in the BM stroma as measured by flow cytometry in a per cell basis, which is in line with the functional in vitro data. Further studies could address the specific question through 3D wholemount studies once APC in situ markers are firmly characterized.

Author response image 3.

Left panel: absolute number of adipocyte progenitor cells (APCs) in the CD45-Ter119-CD31- BM stromal gate for bothTgr5+/+ and Tgr5−/− (n=5). Middle panel: absolute number of cells isolated from the stroma-enriched BM fraction (CD45-Ter119-CD31-) in the same mice. Right panel: absolute number of endothelial cells, defined as CD45-Ter119-CD31+, in the same BM isolates.

• There are issues with the reciprocal transplantation design in Fig 4. Why did the authors choose such a low dose (250 000) of BM cells to transplant? If the effect is true and relevant, the early recovery would be observed independently of the setup and a more robust engraftment dataset would be observed without having lethality post-transplant. On the same note, it's surprising that the authors report ~70% lethality post-transplant from wild-type control mice (Fig 4E), according to the literature 200 000 BM cells should ensure the survival of the recipient post-TBI. Overall, the results even in such a stringent setup still show minimal differences and the study lacks further in-depth analyses to support the main claim.

We thank the reviewer for this comment. On the one hand, we disagree on the relevance of the effect size, as Tgr5-/- mice recover from low levels of platelets significantly faster than the Tgr5+/+ controls. Underlining the relevance, in a clinical setting, G-CSF is administered to patients routinely even if the acceleration of recovery is of 1-2 days (Trivedi et al., 2009).

From the point of view of the mortality, we agree that it is higher than expected. We have suffered from cases of swollen muzzles syndrome in our facilities that have greatly hampered our ability to perform myeloablation experiments (Garrett et al., 2019), as even sublethal doses have resulted in the appearance of severe side effects that are reasons for euthanasia under Swiss legislation. For example, a strong reduction in mobility requires immediate euthanasia. All experiments were performed blinded to genotype allocation, so we can reasonably exclude experimenter bias. Finally, it could be argued that mice with more marked symptomatology leading to euthanasia are more likely to have hematopoietic deficits, which in our case was mostly seen for Tgr5+/+animals. We have therefore chosen to report mortality together with the longitudinal assessment of peripheral blood counts.

• Mechanistically, how does the loss of Tgr5 impact hematopoietic regeneration following sublethal irradiation?

The question of a non-lethal hematopoietic stress is a very relevant one. Unfortunately, and as delineated in the previous point, we have been seriously conditioned by cases of swollen muzzles syndrome (Garrett et al., 2019) that have stopped us from proceeding with more irradiation studies. We will profit from the change of animal facility that will consolidate during the upcoming year Labora(tory of Regenerative Hematopoiesis) to address this point in follow-up studies.

• Only male mice were used throughout this study. It would be beneficial to know whether female mice show similar results.

We agree with this comment, and we expect to include the characterization of BM microenvironment (Figure 3 of the current manuscript) in females in the reviewed version of the manuscript when a suitable cohort becomes available.

Reviewer #2 (Public Review):

Summary: In this manuscript, the authors examined the role of the bile acid receptor TGR5 in the bone marrow under steady-state and stress hematopoiesis. They initially showed the expression of TGR5 in hematopoietic compartments and that loss of TGR5 doesn't impair steady-state hematopoiesis. They further demonstrated that TGR5 knockout significantly decreases BMAT, increases the APC population, and accelerates the recovery upon bone marrow transplantation.

Strengths: The manuscript is well-structured and well-written.

We thank Reviewer #2 for this comment.

Weaknesses: The mechanism is not clear, and additional studies need to be performed to support the authors' conclusion.

We agree with Reviewer #2 that more studies are needed to understand what the role of TGR5 in the hematopoietic system is. We have been hampered in our studies of stress hematopoiesis because of frequent cases of swollen muzzles syndrome (Garrett et al., 2019), which has made difficult to continue with experiments involving myelosuppression (see response to Reviewer #1 as well). Further studies are planned or ongoing, including determining the role of the microbiome on the observed TGR5 bone and hematopoiesis stress phenotypes, but will be the focus of a separate study.

References

Craft, C.S., Robles, H., Lorenz, M.R., Hilker, E.D., Magee, K.L., Andersen, T.L., Cawthorn, W.P., MacDougald, O.A., Harris, C.A., Scheller, E.L., 2019. Bone marrow adipose tissue does not express UCP1 during development or adrenergic-induced remodeling. Sci Rep 9, 17427. https://doi.org/10.1038/s41598-019-54036-x

Garrett, J., Sampson, C.H., Plett, P.A., Crisler, R., Parker, J., Venezia, R., Chua, H.L., Hickman, D.L., Booth, C., MacVittie, T., Orschell, C.M., Dynlacht, J.R., 2019. Characterization and Etiology of Swollen Muzzles in Irradiated Mice. Radiat Res 191, 31–42. https://doi.org/10.1667/RR14724.1

Trivedi, M., Martinez, S., Corringham, S., Medley, K., Ball, E.D., 2009. Optimal use of G-CSF administration after hematopoietic SCT. Bone Marrow Transplant 43, 895–908. https://doi.org/10.1038/bmt.2009.75

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study by McKim et al seeks to provide a comprehensive description of the connectivity of neurosecretory cells (NSCs) using a high-resolution electron microscopy dataset of the fly brain and several single-cell RNA seq transcriptomic datasets from the brain and peripheral tissues of the fly. They use connectomic analyses to identify discrete functional subgroups of NSCs and describe both the broad architecture of the synaptic inputs to these subgroups as well as some of the specific inputs including from chemosensory pathways. They then demonstrate that NSCs have very few traditional presynapses consistent with their known function as providing paracrine release of neuropeptides. Acknowledging that EM datasets can't account for paracrine release, the authors use several scRNAseq datasets to explore signaling between NSCs and characterize widespread patterns of neuropeptide receptor expression across the brain and several body tissues. The thoroughness of this study allows it to largely achieve it's goal and provides a useful resource for anyone studying neurohormonal signaling.

Strengths:

The strengths of this study are the thorough nature of the approach and the integration of several large-scale datasets to address short-comings of individual datasets. The study also acknowledges the limitations that are inherent to studying hormonal signaling and provides interpretations within the the context of these limitations.

Weaknesses:

Overall, the framing of this paper needs to be shifted from statements of what was done to what was found. Each subsection, and the narrative within each, is framed on topics such as "synaptic output pathways from NSC" when there are clear and impactful findings such as "NSCs have sparse synaptic output". Framing the manuscript in this way allows the reader to identify broad takeaways that are applicable to other model system. Otherwise, the manuscript risks being encyclopedic in nature. An overall synthesis of the results would help provide the larger context within which this study falls.

We agree with the reviewer and will replace all the subsection titles as suggested.

The cartoon schematic in Figure 5A (which is adapted from a 2020 review) has an error. This schematic depicts uniglomerular projection neurons of the antennal lobe projecting directly to the lateral horn (without synapsing in the mushroom bodies) and multiglomerular projection neurons projecting to the mushroom bodies and then lateral horn. This should be reversed (uniglomerular PNs synapse in the calyx and then further project to the LH and multiglomerular PNs project along the mlACT directly to the LH) and is nicely depicted in a Strutz et al 2014 publication in eLife.

We thank the reviewer for spotting this error. We will modify the schematic as suggested.

Reviewer #2 (Public review):

Summary:

The authors aim to provide a comprehensive description of the neurosecretory network in the adult Drosophila brain. They sought to assign and verify the types of 80 neurosecretory cells (NSCs) found in the publicly available FlyWire female brain connectome. They then describe the organization of synaptic inputs and outputs across NSC types and outline circuits by which olfaction may regulate NSCs, and by which Corazon-producing NSCs may regulate flight behavior. Leveraging existing transcriptomic data, they also describe the hormone and receptor expressions in the NSCs and suggest putative paracrine signaling between NSCs. Taken together, these analyses provide a framework for future experiments, which may demonstrate whether and how NSCs, and the circuits to which they belong, may shape physiological function or animal behavior.

Strengths:

This study uses the FlyWire female brain connectome (Dorkenwald et al. 2023) to assign putative cell types to the 80 neurosecretory cells (NSCs) based on clustering of synaptic connectivity and morphological features. The authors then verify type assignments for selected populations by matching cluster sizes to anatomical localization and cell counts using immunohistochemistry of neuropeptide expression and markers with known co-expression.

The authors compare their findings to previous work describing the synaptic connectivity of the neurosecretory network in larval Drosophila (Huckesfeld et al., 2021), finding that there are some differences between these developmental stages. Direct comparisons between adults and larvae are made possible through direct comparison in Table 1, as well as the authors' choice to adopt similar (or equivalent) analyses and data visualizations in the present paper's figures.

The authors extract core themes in NSC synaptic connectivity that speak to their function: different NSC types are downstream of shared presynaptic outputs, suggesting the possibility of joint or coordinated activation, depending on upstream activity. NSCs receive some but not all modalities of sensory input. NSCs have more synaptic inputs than outputs, suggesting they predominantly influence neuronal and whole-body physiology through paracrine and endocrine signaling.

The authors outline synaptic pathways by which olfactory inputs may influence NSC activity and by which Corazon-releasing NSCs may regulate flight. These analyses provide a basis for future experiments, which may demonstrate whether and how such circuits shape physiological function or animal behavior.

The authors extract expression patterns of neuropeptides and receptors across NSC cell types from existing transcriptomic data (Davie et al., 2018) and present the hypothesis that NSCs could be interconnected via paracrine signaling. The authors also catalog hormone receptor expression across tissues, drawing from the Fly Cell Atlas (Li et al., 2022).

Weaknesses:

The clustering of NSCs by their presynaptic inputs and morphological features, along with corroboration with their anatomical locations, distinguished some, but not all cell types. The authors attempt to distinguish cell types using additional methodologies: immunohistochemistry (Figure 2), retrograde trans-synaptic labeling, and characterization of dense core vesicle characteristics in the FlyWire dataset (Figure 1, Supplement 1). However, these corroborating experiments often lacked experimental replicates, were not rigorously quantified, and/or were presented as singular images from individual animals or even individual cells of interest. The assignments of DH44 and DMS types remain particularly unconvincing.

We thank the reviewer for this comment. We would like to clarify that the images presented in Figure 2 and Figure 1 Supplement 1 are representative images based on at least 5 independent samples. We will clarify this in the figure caption and methods. The electron micrographs showing dense core vesicle (DCV) characteristics (Figure 1 Supplement E-G) are also representative images based on examination of multiple neurons. However, we agree with the reviewer that a rigorous quantification would be useful to showcase the differences between DCVs from NSC subtypes. Therefore, we have now performed a quantitative analysis of the DCVs in putative m-NSC^DH44 (n=6), putative m-NSC^DMS (n=6) and descending neurons (n=4) known to express DMS. For consistency, we examined the cross section of each cell where the diameter of nuclei was the largest. We quantified the mean gray value of at least 50 DCV per cell. Our analysis shows that mean gray values of putative m-NSC^DMS and DMS descending neurons are not significantly different, whereas the mean gray values of m-NSC^DH44 are significantly larger. This analysis is in agreement with our initial conclusion.

Author response image 1.

The authors present connectivity diagrams for visualization of putative paracrine signaling between NSCs based on their peptide and receptor expression patterns. These transcriptomic data alone are inadequate for drawing these conclusions, and these connectivity diagrams are untested hypotheses rather than results. The authors do discuss this in the Discussion section.

We fully agree with the reviewer and will further elaborate on the limitations of our approach in the revised manuscript. However, there is a very high-likelihood that a given NSC subtype can signal to another NSC subtype using a neuropeptide if its receptor is expressed in the target NSC. This is due to the fact that all NSC axons are part of the same nerve bundle (nervi corpora cardiaca) which exits the brain. The axons of different NSCs form release sites that are extremely close to each other. Neuropeptides from these release sites can easily diffuse via the hemolymph to peripheral tissues that (e.g. fat body and ovaries) that are much further away from the release sites on neighboring NSCs. We believe that neuropeptide receptors are expressed in NSCs near these release sites where they can receive inputs not just from the adjacent NSCs but also from other sources such as the gut enteroendocrine cells. Hence, neuropeptide diffusion is not a limiting factor preventing paracrine signaling between NSCs and receptor expression is a good indicator for putative paracrine signaling.

Reviewer #3 (Public review):

Summary:

The manuscript presents an ambitious and comprehensive synaptic connectome of neurosecretory cells (NSC) in the Drosophila brain, which highlights the neural circuits underlying hormonal regulation of physiology and behaviour. The authors use EM-based connectomics, retrograde tracing, and previously characterised single-cell transcriptomic data. The goal was to map the inputs to and outputs from NSCs, revealing novel interactions between sensory, motor, and neurosecretory systems. The results are of great value for the field of neuroendocrinology, with implications for understanding how hormonal signals integrate with brain function to coordinate physiology.

The manuscript is well-written and provides novel insights into the neurosecretory connectome in the adult Drosophila brain. Some, additional behavioural experiments will significantly strengthen the conclusions.

Strengths:

(1) Rigorous anatomical analysis

(2) Novel insights on the wiring logic of the neurosecretory cells.

Weaknesses:

(1) Functional validation of findings would greatly improve the manuscript.

We agree with this reviewer that assessing the functional output from NSCs would improve the manuscript. Given that we currently lack genetic tools to measure hormone levels and that behaviors and physiology are modulated by NSCs on slow timescales, it is difficult to assess the immediate functional impact of the sensory inputs to NSC using approaches such as optogenetics. However, since l-NSC^CRZ are the only known cell type that provide output to descending neurons, we will functionally test this output pathway using different behavioral assays recommended by this reviewer.

Author Response

Public Reviews

We thank both reviewers for taking the time and effort to think critically about our paper and point out areas where it can be improved. In this document, we do our best to clarify any misunderstandings with the hope that further consideration about the strengths and weaknesses of our approach will be possible. Our responses are in bold.

Reviewer #1 (Public Review):

Summary:

In their manuscript, Schmidlin, Apodaca, et al try to answer fundamental questions about the evolution of new phenotypes and the trade-offs associated with this process. As a model, they use yeast resistance to two drugs, fluconazole and radicicol. They use barcoded libraries of isogenic yeasts to evolve thousands of strains in 12 different environments. They then measure the fitness of evolved strains in all environments and use these measurements to examine patterns in fitness trade-offs. They identify only six major clusters corresponding to different trade-off profiles, suggesting the vast genotypic landscape of evolved mutants translates to a highly constrained phenotypic space. They sequence over a hundred evolved strains and find that mutations in the same gene can result in different phenotypic profiles.

Overall, the authors deploy innovative methods to scale up experimental evolution experiments, and in many aspects of their approach tried to minimize experimental variation.

We thank the reviewer for this positive assessment of our work. We are happy that the reviewer noted what we feel is a unique strength of our approach: we scaled up experimental evolution by using DNA barcodes and by exploring 12 related selection pressures. Despite this scaling up, we still see phenotypic convergence among the 744 adaptive mutants we study.

The environments we study represent 12 different concentrations or combinations of two drugs, radicicol and fluconazole. Our hope is that this large dataset (774 mutants x 12 environments) will be useful, both to scientists who are generally interested in the genetic and phenotypic underpinnings of adaptation, and to scientists specifically interested in the evolution of drug resistance.

Weaknesses:

(1) One of the objectives of the authors is to characterize the extent of phenotypic diversity in terms of resistance trade-offs between fluconazole and radicicol. To minimize noise in the measurement of relative fitness, the authors only included strains with at least 500 barcode counts across all time points in all 12 experimental conditions, resulting in a set of 774 lineages passing this threshold. This corresponds to a very small fraction of the starting set of ~21 000 lineages that were combined after experimental evolution for fitness measurements.

This is a misunderstanding that we will work to clarify in the revision. Our starting set did not include 21,000 adaptive lineages. The total number of unique adaptive lineages in this starting set is much lower than 21,000 for two reasons.

First, ~21,000 represents the number of single colonies we isolated in total from our evolution experiments. Many of these isolates possess the same barcode, meaning they are duplicates. Second, and more importantly, most evolved lineages do not acquire adaptive mutations, meaning that many of the 21,000 isolates are genetically identical to their ancestor. In our revised manuscript, we will explicitly state that these 21,000 isolated lineages do not all represent unique, adaptive lineages. In figure 2 and all associated text, we will change the word “lineages” to “isolates,” where relevant.

More broadly speaking, several previous studies have demonstrated that diverse genetic mutations converge at the level of phenotype, and have suggested that this convergence makes adaptation more predictable (PMID33263280, PMID37437111, PMID22282810, PMID25806684). Our study captures mutants that are overlooked in previous studies, such as those that emerge across subtly different selection pressures (e.g., 4 𝜇g/ml vs. 8 𝜇g/ml flu) and those that are undetectable in evolutions lacking DNA barcodes. Thus, while our experimental design misses some mutants (see next comment), it captures many others. Note that 774 adaptive lineages is more than most previous studies. Thus, we feel that “our work – showing that 774 mutants fall into a much smaller number of groups” is important because it “contributes to growing literature suggesting that the phenotypic basis of adaptation is not as diverse as the genetic basis (lines 161 - 162).”

As the authors briefly remark, this will bias their datasets for lineages with high fitness in all 12 environments, as all these strains must be fit enough to maintain a high abundance.

The word “briefly” feels a bit unfair because we discuss this bias on 3 separate occasions (on lines 146 - 147, 260 - 264, and in more detail on 706 - 714). We even walk through an example of a class of mutants that our study misses. We say, “our study is underpowered to detect adaptive lineages that have low fitness in any of the 12 environments. This is bound to exclude large numbers of adaptive mutants. For example, previous work has shown some FLU resistant mutants have strong tradeoffs in RAD (Cowen and Lindquist 2005). Perhaps we are unable to detect these mutants because their barcodes are at too low a frequency in RAD environments, thus they are excluded from our collection of 774.”

In our revised version, we will add more text to the first mention of these missing mutants (lines 146 - 147) so that the implications are more immediately made apparent.

While we “miss” some classes of mutants, we “catch” other classes that may have been missed in previous studies of convergence. For example, we observe a unique class of FLU-resistant mutants that primarily emerged in evolution experiments that lack FLU (Figure 3). Thus, we think that the unique design of our study, surveying 12 environments, allows us to make a novel contribution to the study of phenotypic convergence.

One of the main observations of the authors is phenotypic space is constrained to a few clusters of roughly similar relative fitness patterns, giving hope that such clusters could be enumerated and considered to design antimicrobial treatment strategies. However, by excluding all lineages that fit in only one or a few environments, they conceal much of the diversity that might exist in terms of trade-offs and set up an inclusion threshold that might present only a small fraction of phenotypic space with characteristics consistent with generalist resistance mechanisms or broadly increased fitness. This has important implications regarding the general conclusions of the authors regarding the evolution of trade-offs.

We discussed these implications in some detail in the 16 lines mentioned above (146 - 147, 260 - 264, 706 - 714). To add to this discussion, we will also add the following sentence to the end of the paragraph on lines 697 - 714: “This could complicate (or even make impossible) endeavors to design antimicrobial treatment strategies that thwart resistance”.

We will also add a new paragraph that discusses these implications earlier in our manuscript. This paragraph will highlight the strengths of our method (e.g., that we “catch” classes of mutants that are often overlooked) while being transparent about the weaknesses of our approach (e.g., that we “miss” mutants with strong tradeoffs).

(2) Most large-scale pooled competition assays using barcodes are usually stopped after ~25 to avoid noise due to the emergence of secondary mutations.

The rate at which new mutations enter a population is driven by various factors such as the mutation rate and population size, so choosing an arbitrary threshold like 25 generations is difficult.

We conducted our fitness competition following previous work using the Levy/Blundell yeast barcode system, in which the number of generations reported varies from 32 to 40 (PMID33263280, PMID27594428, PMID37861305, see PMID27594428 for detailed calculation of the fraction of lineages biased by secondary mutations in this system).

The authors measure fitness across ~40 generations, which is almost the same number of generations as in the evolution experiment. This raises the possibility of secondary mutations biasing abundance values, which would not have been detected by the whole genome sequencing as it was performed before the competition assay.

We understand how the reviewer came to this misunderstanding and will adjust our revised manuscript accordingly. Previous work has demonstrated that, in this particular evolution platform, most of the mutations actually occur during the transformation that introduces the DNA barcodes (PMID25731169). In other words, these mutations do not accumulate during the 40 generations of evolution, they are already there. So the observation that we collect a genetically diverse pool of adaptive mutants after 40 generations of evolution is not evidence that 40 generations is enough time for secondary mutations to bias abundance values.

(3) The approach used by the authors to identify and visualize clusters of phenotypes among lineages does not seem to consider the uncertainty in the measurement of their relative fitness. As can be seen from Figure S4, the inter-replicate difference in measured fitness can often be quite large. From these graphs, it is also possible to see that some of the fitness measurements do not correlate linearly (ex.: Med Flu, Hi Rad Low Flu), meaning that taking the average of both replicates might not be the best approach.

This concern, and all subsequent concerns, seem to be driven by either (a) general concerns about the noisiness of fitness measurements obtained from large-scale barcode fitness assays or (b) general concerns about whether the clusters obtained from our dimensional reduction approach capture this noise as opposed to biologically meaningful differences.

We will respond to each concern point-by-point, but want to start by generally stating that (a) our particular large-scale barcode fitness assay has several features that diminish noise, and (b) we devote 4 figures and 200 lines of text to demonstrating that these clusters capture biologically meaningful differences between mutants (and not noise).

In terms of this specific concern, we performed an analysis of noise in the submitted manuscript: Our noisiest fitness measurements correspond to barcodes that are the least abundant and thus suffer the most from stochastic sampling noise. These are also the barcodes that introduce the nonlinearity the reviewer mentions. We removed these from our dataset by increasing our coverage threshold from 500 reads to 5,000 reads. The clusters did not collapse, which suggests that they were not capturing noise (Figure S7 panel B). But we agree with the reviewer that this analysis alone is not sufficient to conclude that the clusters distinguish groups of mutants with unique fitness tradeoffs.

Because the clustering approach used does not seem to take this variability into account, it becomes difficult to evaluate the strength of the clustering, especially because the UMAP projection does not include any representation of uncertainty around the position of lineages.

To evaluate the strength of the clustering, we performed numerous analyses including whole genome sequencing, growth experiments, reclustering, and tracing the evolutionary origins of each cluster (Figures 5 - 8). All of these analyses suggested that our clusters capture groups of mutants that have different fitness tradeoffs. We will adjust our revised manuscript to make clear that we do not rely on the results of a clustering algorithm alone to draw conclusions about phenotypic convergence.

We are also grateful to the reviewer for helping us realize that, as written, our manuscript is not clear with regard to how we perform clustering. We are not using UMAP to decide which mutant belongs to which cluster. Recent work highlights the importance of using an independent clustering method (PMID37590228). Although this recent work addresses the challenge of clustering much higher dimensional data than we survey here, we did indeed use an independent clustering method (gaussian mixture model). In other words, we use UMAP for visualization but not clustering. We also confirm our clustering results using a second independent method (hierarchical clustering; Figure S8). And in our revised manuscript, will confirm with a third method (PCA, see below). We will adjust the main text and the methods section to make these choices clearer.

This might paint a misleading picture where clusters appear well separate and well defined but are in fact much fuzzier, which would impact the conclusion that the phenotypic space is constricted.

The salient question is whether the clusters are so “fuzzy” that they are not meaningful. That interpretation seems unreasonable. Our clusters group mutants with similar genotypes, evolutionary histories, and fitness tradeoffs (Figures 5 - 8). Clustering mutants with similar behaviors is important and useful. It improves phenotypic prediction by revealing which mutants are likely to have at least some phenotypic effects in common. And it also suggests that the phenotypic space is constrained, at least to some degree, which previous work suggests is helpful in predicting evolution (PMID33263280, PMID37437111, PMID22282810, PMID25806684).

(4) The authors make the decision to use UMAP and a gaussian mixed model to cluster and represent the different fitness landscapes of their lineages of interest. Their approach has many caveats. First, compared to PCA, the axis does not provide any information about the actual dissimilarities between clusters. Using PCA would have allowed a better understanding of the amount of variance explained by components that separate clusters, as well as more interpretable components.

The components derived from PCA are often not interpretable. It’s not obvious that each one, or even the first one, will represent some intuitive phenotype, like resistance to fluconazole.

Moreover, we see many non-linearities in our data. For example, fitness in a double drug environment is not predicted by adding up fitness in the relevant single drug environments. Also, there are mutants that have high fitness when fluconazole is absent or abundant, but low fitness when mild concentrations are present. These types of nonlinearities can make the axes in PCA very difficult to interpret, plus these nonlinearities can be missed by PCA, thus we prefer other clustering methods.

We will adjust our revised manuscript to explain these reasons why we chose UMAP and GMM over PCA.

Also, we will include PCA in the supplement of our revised manuscript. Please find below PC1 vs PC2, with points colored according to the cluster assignment in figure 4 (i.e. using a gaussian mixture model). It appears the clusters are largely preserved.

Author response image 1.

Second, the advantages of dimensional reduction are not clear. In the competition experiment, 11/12 conditions (all but the no drug, no DMSO conditions) can be mapped to only three dimensions: concentration of fluconazole, concentration of radicicol, and relative fitness. Each lineage would have its own fitness landscape as defined by the plane formed by relative fitness values in this space, which can then be examined and compared between lineages.

We worry that the idea stems from apriori notions of what the important dimensions should be. It also seems like this would miss important nonlinearities such as our observation that low fluconazole behaves more like a novel selection pressure than a dialed down version of high fluconazole.

Also, we believe the reviewer meant “fitness profile” and not “fitness landscape”. A fitness landscape imagines a walk where every “step” is a mutation. Most lineages in barcoded evolution experiments possess only a single adaptive mutation. A single-step walk is not enough to build a landscape, though others are expanding barcoded evolution experiments beyond the first step (PMID34465770, PMID31723263), so maybe one day this will be possible.

Third, the choice of 7 clusters as the cutoff for the multiple Gaussian model is not well explained. Based on Figure S6A, BIC starts leveling off at 6 clusters, not 7, and going to 8 clusters would provide the same reduction as going from 6 to 7. This choice also appears arbitrary in Figure S6B, where BIC levels off at 9 clusters when only highly abundant lineages are considered.

We agree. We did not rely on the results of BIC alone to make final decisions about how many clusters to include. We thank the reviewer for pointing out this gap in our writing. We will adjust our revised manuscript to explain that we ultimately chose to describe 6 clusters that we were able to validate with follow-up experiments. In figures 5, 6, 7, and 8, we use external information to validate the clusters that we report in figure 4. And in lines 697 – 714, we explain that there are may be additional clusters beyond those we tease apart in this study.

This directly contradicts the statement in the main text that clusters are robust to noise, as more a stringent inclusion threshold appears to increase and not decrease the optimal number of clusters. Additional criteria to BIC could have been used to help choose the optimal number of clusters or even if mixed Gaussian modeling is appropriate for this dataset.

We are under the following impression: If our clustering method was overfitting, i.e. capturing noise, the optimal number of clusters should decrease when we eliminate noise. It increased. In other words, the observation that our clusters did not collapse (i.e. merge) when we removed noise suggests these clusters were not capturing noise.

More generally, our validation experiments, described below, provide additional evidence that our clusters capture meaningful differences between mutants (and not noise).

(5) Large-scale barcode sequencing assays can often be noisy and are generally validated using growth curves or competition assays.

Some types of bar-seq methods, in particular those that look at fold change across two time points, are noisier than others that look at how frequency changes across multiple timepoints (PMID30391162). Here, we use the less noisy method. We also reduce noise by using a stricter coverage threshold than previous work (e.g., PMID33263280), and by excluding batch effects by performing all experiments simultaneously (PMID37237236).

The main assay we use to measure fitness has been previously validated (PMID27594428). No subsequent study using this assay validates using the methods suggested by the reviewer (see PMID37861305, PMID33263280, PMID31611676, PMID29429618, PMID37192196, PMID34465770, PMID33493203).

More to the point, bar-seq has been used, without the reviewer’s suggested validation, to demonstrate that the way some mutant’s fitness changes across environments is different from other mutants (PMID33263280, PMID37861305, PMID31611676, PMID33493203, PMID34596043). This is the same thing that we use bar-seq to demonstrate.

For all of these reasons, we are hesitant to confirm bar-seq itself as a valid way to infer fitness. It seems this is already accepted as a standard in our field.

Having these types of results would help support the accuracy of the main assay in the manuscript and thus better support the claims of the authors.

We don’t agree that fitness measurements obtained from this bar-seq assay generally require validation. But we do agree that it is important to validate whether the mutants in each of our 6 clusters indeed are different from one another in meaningful ways, in particular, in that they have different fitness tradeoffs. We have four figures (5 - 8) and 200 lines of text dedicated to validating whether our clusters capture reproducible and biologically meaningful differences between mutants. Happily, one of these figures (Fig 7) includes growth curves, which are exactly the type of validation experiment asked for by the reviewer.

Below, we walk through the different types of validation experiments that are present in our original manuscript, and additional validation experiments that we plan to include in the revised version. We are hopeful that these validation experiments are sufficient, or at the very least, that this list empowers reviewers to point out where more work is needed.

(1) Mutants from different clusters have different growth curves: In our original manuscript, we measured growth curves corresponding to a fitness tradeoff that we thought was surprising. Mutants in clusters 4 and 5 both have fitness advantages in single drug conditions. While mutants from cluster 4 also are advantageous in the double drug conditions, mutants from cluster 5 are not! We validated these different behaviors by studying growth curves for a mutant from each cluster (Figures 7 and S10).

(2) Mutants from different clusters have different evolutionary origins: In our original manuscript, we came up with a novel way to ask whether the clusters capture different types of adaptive mutants. We asked whether the mutants in each cluster originate from different evolution experiments. Indeed they often do (see pie charts in Figures 6, 7, 8). This method also provides evidence supporting each cluster’s differing fitness tradeoffs.

For example, mutants in cluster 5 appear to have a tradeoff in a double drug condition (described above). They rarely originate from that evolution condition, unlike mutants in nearby cluster 4 (see Figure 7).

(3) Mutants from each cluster often fall into different genes: In our original manuscript, we sequenced many of these mutants and show that mutants in the same gene are often found in the same cluster. For example, all 3 IRA1 mutants are in cluster 6 (Fig 8), both GPB2 mutants are in cluster 4 (Figs 7 & 8), and 35/36 PDR mutants are in either cluster 2 or 3 (Figs 5 & 6).

(4) Mutants from each cluster have behaviors previously observed in the literature: In our original manuscript, we compared our sequencing results to the literature and found congruence. For example, PDR mutants are known to provide a fitness benefit in fluconazole and are found in clusters that have high fitness in fluconazole (lines 457 - 462). Previous work suggests that some mutations to PDR have different tradeoffs than others, which is what we see (lines 540 - 542). IRA1 mutants were previously observed to have high fitness in our “no drug” condition, and are found in the cluster that has the highest fitness in the “no drug” condition (lines 642 - 646). Previous work even confirms the unusual fitness tradeoff we observe where IRA1 and other cluster 6 mutants have low fitness only in low concentrations of fluconazole (lines 652 - 657).

(5) Mutants largely remain in their clusters when we use alternate clustering methods: In our original manuscript, we performed various different reclustering and/or normalization approaches on our data (Fig 6, S5, S7, S8, S9). The clusters of mutants that we observe in figure 4 do not change substantially when we recluster the data. We will add PCA (see above) to these analyses in our revised manuscript.

(6) We will include additional data showing that mutants in different clusters have different evolutionary origins: Cluster 1 is defined by high fitness in low fluconazole that declines with increasing fluconazole (see Fig 4E and Fig 5C). In our revised manuscript, we will show that cluster 1 lineages were overwhelmingly sampled from evolutions conducted in our lowest concentration of fluconazole (see figure panel A below). No other cluster’s evolutionary history shows this pattern (figures 6, 7, and 8).

(7) We will include additional data showing that mutants in different clusters have different growth curves: Cluster 1 lineages are unique in that their fitness advantage is specific to low flu and trades off in higher concentrations of fluconazole. We obtained growth curves for three cluster 1 mutants (2 SUR1 mutants and 1 UPC2 mutant). We compared them to growth curves for three PDR mutants (from clusters 2 and 3). Cluster 1 mutants appear to have the highest growth rates and reach the higher carrying capacity in low fluconazole (see red and green lines in Author response image 2 panel B below). But the cluster 1 mutants are negatively affected by higher concentrations of fluconazole, much more so than the mutants from clusters 2 and 3 (see Author response image 2 panel C below). This is consistent with the different fitness tradeoffs we observe for each cluster (figures 4 and 5). We will include a more detailed version of this analysis and the figures below in our revised manuscript.

Author response image 2.

Validation experiments demonstrate that cluster 1 mutants have uniquely high fitness in only the lowest concentration of fluconazole. (A) The mutant lineages in cluster 1 were largely sampled from evolution experiments performed in low flu. This is not true of other clusters (see pie charts in main manuscript). (B) In low flu (4 𝜇g/ml), Cluster 1 lineages (red/UPC2 and green/SUR1) grow faster and achieve higher density than lineages from clusters 2 and 3 (blue/PDR). This is consistent with barseq measurements demonstrating that cluster 1 mutants have the highest fitness in low flu. (C) Cluster 1 lineages are sensitive to increasing flu concentrations (SUR1 and UPC2 mutants, middle and rightmost graphs). This is apparent in that the gray (8 𝜇g/ml flu) and light blue (32 𝜇g/ml flu) growth curves rise more slowly and reach lower density than the dark blue curves (4 𝜇g/ml flu). But this is not the case for the PDR mutants from clusters 2 and 3 (leftmost graph). These observations are consistent with the bar-seq fitness data presented in the main manuscript (Fig 4E).

With all of these validation efforts combined, we are hopeful that the reviewer is now more convinced that our clusters capture groups of mutants with different fitness tradeoffs (as opposed to noise). We want to conclude by saying that we are grateful to the reviewer for making us think deeply about areas where we can include additional validation efforts as well as areas where we can make our manuscript clearer.

Reviewer #2 (Public Review):

Summary:

Schmidlin & Apodaca et al. aim to distinguish mutants that resist drugs via different mechanisms by examining fitness tradeoffs across hundreds of fluconazole-resistant yeast strains. They barcoded a collection of fluconazole-resistant isolates and evolved them in different environments with a view to having relevance for evolutionary theory, medicine, and genotypephenotype mapping.

Strengths:

There are multiple strengths to this paper, the first of which is pointing out how much work has gone into it; the quality of the experiments (the thought process, the data, the figures) is excellent. Here, the authors seek to induce mutations in multiple environments, which is a really large-scale task. I particularly like the attention paid to isolates with are resistant to low concentrations of FLU. So often these are overlooked in favour of those conferring MIC values >64/128 etc. What was seen is different genotype and fitness profiles. I think there's a wealth of information here that will actually be of interest to more than just the fields mentioned (evolutionary medicine/theory).

We are very grateful for this positive review. This was indeed a lot of work! We are happy that the reviewer noted what we feel is a unique strength of our manuscript: that we survey adaptive isolates across multiple environments, including low drug concentrations.

Weaknesses:

Not picking up low fitness lineages - which the authors discuss and provide a rationale as to why. I can completely see how this has occurred during this research, and whilst it is a shame I do not think this takes away from the findings of this paper. Maybe in the next one!

We thank the reviewer for these words of encouragement and will work towards catching more low fitness lineages in our next project.

In the abstract the authors focus on 'tradeoffs' yet in the discussion they say the purpose of the study is to see how many different mechanisms of FLU resistance may exist (lines 679-680), followed up by "We distinguish mutants that likely act via different mechanisms by identifying those with different fitness tradeoffs across 12 environments". Whilst I do see their point, and this is entirely feasible, I would like a bit more explanation around this (perhaps in the intro) to help lay-readers make this jump. The remainder of my comments on 'weaknesses' are relatively fixable, I think:

We think that phrasing the “jump” as a question might help lay readers get from point A to point B. So, in the introduction of our revised manuscript, we will add a paragraph roughly similar to this one: “If two groups of drug-resistant mutants have different fitness tradeoffs, does it mean that they provide resistance through different underlying mechanisms? Alternatively, it could mean that both provide drug resistance via the same mechanism, but some mutations come with a cost that others don’t pay. However, another way to phrase this alternative is to say that both groups of mutants affect fitness through different suites of mechanisms that are only partially overlapping. And so, by identifying groups of mutants with different fitness tradeoffs, we argue that we will be uncovering sets of mutations that impact fitness through different underlying mechanisms. The ability to do so would be useful for genotype-phenotype mapping endeavors.”

In the introduction I struggle to see how this body of research fits in with the current literature, as the literature cited is a hodge-podge of bacterial and fungal evolution studies, which are very different! So example, the authors state "previous work suggests that mutants with different fitness tradeoffs may affect fitness through different molecular mechanisms" (lines 129-131) and then cite three papers, only one of which is a fungal research output. However, the next sentence focuses solely on literature from fungal research. Citing bacterial work as a foundation is fine, but as you're using yeast for this I think tailoring the introduction more to what is and isn't known in fungi would be more appropriate. It would also be great to then circle back around and mention monotherapy vs combination drug therapy for fungal infections as a rationale for this study. The study seems to be focused on FLU-resistant mutants, which is the first-line drug of choice, but many (yeast) infections have acquired resistance to this and combination therapy is the norm.

In our revised manuscript, we will carefully review all citations. The issue may stem from our attempt to reach two different groups of scientists. We ourselves are broadly interested in the structure of the genotype-phenotype-fitness map (PMID33263280, PMID32804946). Though the 3 papers the reviewer mentions on lines 132 - 133 all pertain to yeast, we cite them because they are studies about the complexity of this map. Their conclusions, in theory, should apply broadly, beyond yeast. Similarly, the reason we cite papers from yeast, as well as bacteria and cancer, is that we believe general conclusions about the genotype-phenotype-fitness map should apply broadly. For example, the sentence the reviewer highlights, “previous work suggests that mutants with different fitness tradeoffs may affect fitness through different molecular mechanisms” is a general observation about the way genotype maps to fitness. So we cited papers from across the tree of life to support this sentence.

On the other hand, because we study drug resistant mutations, we also hope that our work is of use to scientists studying the evolution of resistance. We agree with the reviewer that in this regard, some of our findings may be especially pertinent to the evolution of resistance to antifungal drugs. We will consider this when reviewing the citations in our revised manuscript and add some text to clarify these points.

Methods: Line 769 - which yeast? I haven't even seen mention of which species is being used in this study; different yeast employ different mechanisms of adaptation for resistance, so could greatly impact the results seen. This could help with some background context if the species is mentioned (although I assume S. cerevisiae).

In the revised manuscript, we will make clear that we study S. cerevisiae.

In which case, should aneuploidy be considered as a mechanism? This is mentioned briefly on line 556, but with all the sequencing data acquired this could be checked quickly?

We like this idea and we are working on it, but it is not straightforward. The reviewer is correct in that we can use the sequencing data that we already have. But calling aneuploidy with certainty is tough because its signal can be masked by noise. In other words, some regions of the genome may be sequenced more than others by chance. Given this is not straightforward, at least not for us, this analysis will likely have to wait for a subsequent paper.

I think the authors could be bolder and try and link this to other (pathogenic) yeasts. What are the implications of this work on say, Candida infections?

Perhaps because our background lies in general study of the genotype-phenotype map, we did not want to make bold assertions about how our work might apply to pathogenic yeasts. But we see how this could be helpful and will add some discussion points about this. Specifically, we will discuss which of the genes and mutants we observe are also found in Candida. We will also investigate whether our observation that low fluconazole represents a seemingly unique challenge, not just a milder version of high fluconazole, has any corollary in the Candida literature.

Author response:

We thank the reviewers for their thorough reading and thoughtful feedback. Below, we provisionally address each of the concerns raised in the public reviews, and outline our planned revision that aims to further clarify and strengthen the manuscript.

In our response, we clarify our conceptualization of elasticity as a dimension of controllability, formalizing it within an information-theoretic framework, and demonstrating that controllability and its elasticity are partially dissociable. Furthermore, we provide clarifications and additional modeling results showing that our experimental design and modeling approach are well-suited to dissociating elasticity inference from more general learning processes, and are not inherently biased to find overestimates of elasticity. Finally, we clarify the advantages and disadvantages of our canonical correlation analysis (CCA) approach for identifying latent relationships between multidimensional data sets, and provide additional analyses that strengthen the link between elasticity estimation biases and a specific psychopathology profile.

Reviewer 1:

This research takes a novel theoretical and methodological approach to understanding how people estimate the level of control they have over their environment, and how they adjust their actions accordingly. The task is innovative and both it and the findings are well-described (with excellent visuals). They also offer thorough validation for the particular model they develop. The research has the potential to theoretically inform the understanding of control across domains, which is a topic of great importance.

We thank the reviewer for their favorable appraisal and valuable suggestions, which have helped clarify and strengthen the study’s conclusion. 

An overarching concern is that this paper is framed as addressing resource investments across domains that include time, money, and effort, and the introductory examples focus heavily on effort-based resources (e.g., exercising, studying, practicing). The experiments, though, focus entirely on the equivalent of monetary resources - participants make discrete actions based on the number of points they want to use on a given turn. While the same ideas might generalize to decisions about other kinds of resources (e.g., if participants were having to invest the effort to reach a goal), this seems like the kind of speculation that would be better reserved for the Discussion section rather than using effort investment as a means of introducing a new concept (elasticity of control) that the paper will go on to test.

We thank the reviewer for pointing out a lack of clarity regarding the kinds of resources tested in the present experiment. Investing additional resources in the form of extra tickets did not only require participants to pay more money. It also required them to invest additional time – since each additional ticket meant making another attempt to board the vehicle, extending the duration of the trial, and attentional effort – since every attempt required precisely timing a spacebar press as the vehicle crossed the screen. Given this involvement of money, time, and effort resources, we believe it would be imprecise to present the study as concerning monetary resources in particular. That said, we agree with the Reviewer that results might differ depending on the resource type that the experiment or the participant considers most. Thus, in our revision of the manuscript, we will make sure to clarify the kinds of resources the experiment involved, and highlight the open question of whether inferences concerning the elasticity of control generalize across different resource domains.

Setting aside the framing of the core concepts, my understanding of the task is that it effectively captures people's estimates of the likelihood of achieving their goal (Pr(success)) conditional on a given investment of resources. The ground truth across the different environments varies such that this function is sometimes flat (low controllability), sometimes increases linearly (elastic controllability), and sometimes increases as a step function (inelastic controllability). If this is accurate, then it raises two questions.

First, on the modeling front, I wonder if a suitable alternative to the current model would be to assume that the participants are simply considering different continuous functions like these and, within a Bayesian framework, evaluating the probabilistic evidence for each function based on each trial's outcome. This would give participants an estimate of the marginal increase in Pr(success) for each ticket, and they could then weigh the expected value of that ticket choice (Pr(success)*150 points) against the marginal increase in point cost for each ticket. This should yield similar predictions for optimal performance (e.g., opt-out for lower controllability environments, i.e., flatter functions), and the continuous nature of this form of function approximation also has the benefit of enabling tests of generalization to predict changes in behavior if there was, for instance, changes in available tickets for purchase (e.g., up to 4 or 5) or changes in ticket prices. Such a model would of course also maintain a critical role for priors based on one's experience within the task as well as over longer timescales, and could be meaningfully interpreted as such (e.g., priors related to the likelihood of success/failure and whether one's actions influence these). It could also potentially reduce the complexity of the model by replacing controllability-specific parameters with multiple candidate functions (presumably learned through past experience, and/or tuned by experience in this task environment), each of which is being updated simultaneously.

Second, if the reframing above is apt (regardless of the best model for implementing it), it seems like the taxonomy being offered by the authors risks a form of "jangle fallacy," in particular by positing distinct constructs (controllability and elasticity) for processes that ultimately comprise aspects of the same process (estimation of the relationship between investment and outcome likelihood). Which of these two frames is used doesn't bear on the rigor of the approach or the strength of the findings, but it does bear on how readers will digest and draw inferences from this work. It is ultimately up to the authors which of these they choose to favor, but I think the paper would benefit from some discussion of a common-process alternative, at least to prevent too strong of inferences about separate processes/modes that may not exist. I personally think the approach and findings in this paper would also be easier to digest under a common-construct approach rather than forcing new terminology but, again, I defer to the authors on this.

We thank the reviewer for suggesting this interesting alternative modeling approach. We agree that a Bayesian framework evaluating different continuous functions could offer advantages, particularly in its ability to generalize to other ticket quantities and prices. We will attempt to implement this as an alternative model and compare it with the current model.  

We also acknowledge the importance of avoiding a potential "jangle fallacy". We entirely agree with the Reviewer that elasticity and controllability inferences are not distinct processes. Specifically, we view resource elasticity as a dimension of controllability, hence the name of our ‘elastic controllability’ model. In response to this and other Reviewers’ comments, we now offer a formal definition of elasticity as the reduction in uncertainty about controllability due to knowing the amount of resources the agent is able and willing to invest (see further details in response to Reviewer 3 below).  

With respect to how this conceptualization is expressed in the modelling, we note that the representation in our model of maximum controllability and its elasticity via different variables is analogous to how a distribution may be represented by separate mean and variance parameters. Ultimately, even in the model suggested by the Reviewer, there would need to be a dedicated variable representing elasticity, such as the probability of sloped controllability functions. A single-process account thus allows that different aspects of this process would be differently biased (e.g., one can have an accurate estimate of the mean of a distribution but overestimate its variance). Therefore, our characterization of distinct elasticity and controllability biases (or to put it more accurately, ‘elasticity of controllability bias’ and ‘maximum controllability bias’) is consistent with a common construct account. 

That said, given the Reviewer’s comments, we believe that some of the terminology we used may have been misleading. In our planned revision, we will modify the text to clarify that we view elasticity as a dimension of controllability that can only be estimated in conjunction with controllability. 

Reviewer 2:

This research investigates how people might value different factors that contribute to controllability in a creative and thorough way. The authors use computational modeling to try to dissociate "elasticity" from "overall controllability," and find some differential associations with psychopathology. This was a convincing justification for using modeling above and beyond behavioral output and yielded interesting results. Interestingly, the authors conclude that these findings suggest that biased elasticity could distort agency beliefs via maladaptive resource allocation. Overall, this paper reveals some important findings about how people consider components of controllability.

We appreciate the Reviewer's positive assessment of our findings and computational approach to dissociating elasticity and overall controllability.

The primary weakness of this research is that it is not entirely clear what is meant by "elastic" and "inelastic" and how these constructs differ from existing considerations of various factors/calculations that contribute to perceptions of and decisions about controllability. I think this weakness is primarily an issue of framing, where it's not clear whether elasticity is, in fact, theoretically dissociable from controllability. Instead, it seems that the elements that make up "elasticity" are simply some of the many calculations that contribute to controllability. In other words, an "elastic" environment is inherently more controllable than an "inelastic" one, since both environments might have the same level of predictability, but in an "elastic" environment, one can also partake in additional actions to have additional control overachieving the goal (i.e., expend effort, money, time).

We thank the reviewer for highlighting the lack of clarity in our concept of elasticity. We first clarify that elasticity cannot be entirely dissociated from controllability because it is a dimension of controllability. If no controllability is afforded, then there cannot be elasticity or inelasticity. This is why in describing the experimental environments, we only label high-controllability, but not low-controllability, environments as ‘elastic’ or ‘inelastic’. For further details on this conceptualization of elasticity, and a planned revision of the text, see our response above to Reviewer 1. 

Second, we now clarify that controllability can also be computed without knowing the amount of resources the agent is able and willing to invest, for instance by assuming infinite resources available or a particular distribution of resource availabilities. However, knowing the agent’s available resources often reduces uncertainty concerning controllability. This reduction in uncertainty is what we define as elasticity. Since any action requires some resources, this means that no controllable environment is entirely inelastic if we also consider agents that do not have enough resources to commit any action. However, even in this case environments can differ in the degree to which they are elastic. For further details on this formal definition, see our response to Reviewer 3 below. We will make these necessary clarifications in the revised manuscript. 

Importantly, whether an environment is more or less elastic does not determine whether it is more or less controllable. In particular, environments can be more controllable yet less elastic. This is true even if we allow that investing different levels of resources (i.e., purchasing 0, 1, 2, or 3 tickets) constitute different actions, in conjunction with participants’ vehicle choices. Below, we show this using two existing definitions of controllability. 

Definition 1, reward-based controllability¹: If control is defined as the fraction of available reward that is controllably achievable, and we assume all participants are in principle willing and able to invest 3 tickets, controllability can be computed in the present task as:

where P(S' \= goal ∣ 𝑆, 𝐴, 𝐶 ) is the probability of reaching the treasure from present state 𝑆 when taking action A and investing C resources in executing the action. In any of the task environments, the probability of reaching the goal is maximized by purchasing 3 tickets (𝐶 = 3) and choosing the vehicle that leads to the goal (𝐴 = correct vehicle). Conversely, the probability of reaching the goal is minimized by purchasing 3 tickets (𝐶 = 3) and choosing the vehicle that does not lead to the goal (𝐴 = wrong vehicle). This calculation is thus entirely independent of elasticity, since it only considers what would be achieved by maximal resource investment, whereas elasticity consists of the reduction in controllability that would arise if the maximal available 𝐶 is reduced. Consequently, any environment where the maximum available control is higher yet varies less with resource investment would be more controllable and less elastic. 

Note that if we also account for ticket costs in calculating reward, this will only reduce the fraction of achievable reward and thus the calculated control in elastic environments.   

Definition 2, information-theoretic controllability²: Here controllability is defined as the reduction in outcome entropy due to knowing which action is taken:

I(S'; A, C | S) = H(S'|S) - H(S'|S, A, C)

where H(S'|S) is the conditional entropy of the distribution of outcomes S' given the present state 𝑆, and H(S'|S, A, C) is the conditional entropy of the outcome given the present state, action, and resource investment. 

To compare controllability, we consider two environments with the same maximum control:

• Inelastic environment: If the correct vehicle is chosen, there is a 100% chance of reaching the goal state with 1, 2, or 3 tickets. Thus, out of 7 possible action-resource investment combinations, three deterministically lead to the goal state (≥1 tickets and correct vehicle choice), three never lead to it (≥1 tickets and wrong vehicle choice), and one (0 tickets) leads to it 20% of the time (since walking leads to the treasure on 20% of trials).

• Elastic Environment: If the correct vehicle is chosen, the probability of boarding it is 0% with 1 ticket, 50% with 2 tickets, and 100% with 3 tickets. Thus, out of 7 possible actionresource investment combinations, one deterministically leads to the goal state (3 tickets and correct vehicle choice), one never leads to it (3 tickets and wrong vehicle choice), one leads to it 60% of the time (2 tickets and correct vehicle choice: 50% boarding + 50% × 20% when failing to board), one leads to it 10% of time (2 ticket and wrong vehicle choice), and three lead to it 20% of time (0-1 tickets).

Here we assume a uniform prior over actions, which renders the information-theoretic definition of controllability equal to another definition termed ‘instrumental divergence’3,4. We note that changing the uniform prior assumption would change the results for the two environments, but that would not change the general conclusion that there can be environments that are more controllable yet less elastic. 

Step 1: Calculating H(S'|S)

For the inelastic environment:

P(goal) = (3 × 100% + 3 × 0% + 1 × 20%)/7 = .46, P(non-goal) = .54  H(S'|S) = – [.46 × log₂(.46) + .54 × log₂(.54)] \= 1 bit

For the elastic environment:

P(goal) \= (1 × 100% + 1 × 0% + 1 × 60% + 1 × 10% + 3 × 20%)/7 \= .33, P(non-goal) \= .67  H(S'|S) = – [.33 × log₂(.33) + .67 × log₂(.67)] \= .91 bits

Step 2: Calculating H(S'|S, A, C)

Inelastic environment: Six action-resource investment combinations have deterministic outcomes entailing zero entropy, whereas investing 0 tickets has a probabilistic outcome (20%). The entropy for 0 tickets is: H(S'|C \= 0) \= -[.2 × log₂(.2) + 0.8 × log₂ (.8)] = .72 bits. Since this actionresource investment combination is chosen with probability 1/7, the total conditional entropy is approximately .10 bits

Elastic environment: 2 actions have deterministic outcomes (3 tickets with correct/wrong vehicle), whereas the other 5 actions have probabilistic outcomes:

2 tickets and correct vehicle (60% success): 

H(S'|A = correct, C = 2) = – [.6 × log₂(.6) + .4 × log₂(.4)] \= .97 bits 2 tickets and wrong vehicle (10% success): 

H(S'|A = wrong, C = 2) = – [.1 × ₂(.1) + .9 × ₂(.9)] \= .47 bits 0-1 tickets (20% success):

H(S'|C = 0-1) = – [.2 × ₂(.2) + .8 × ₂ .8)] \= .72 bits

Thus the total conditional entropy of the elastic environment is: H(S'|S, A, C) = (1/7) × .97 + (1/7) × .47 + (3/7) × .72 \= .52 bits

Step 3: Calculating I(S' | A, S)  

Inelastic environment: I(S'; A, C | S) = H(S'|S) – H(S'|S, A, C) = 1 – 0.1 = .9 bits 

Elastic environment: I(S'; A, C | S) = H(S'|S) – H(S'|S, A, C) = .91 – .52 = .39 bits

Thus, the inelastic environment offers higher information-theoretic controllability (.9 bits) compared to the elastic environment (.39 bits). 

Of note, even if each combination of cost and goal reaching is defined as a distinct outcome, then information-theoretic controllability is higher for the inelastic (2.81 bits) than for the elastic (2.30 bits) environment. 

In sum, for both definitions of controllability, we see that environments can be more elastic yet less controllable. We will amend the manuscript to clarify this distinction between controllability and its elasticity.

Reviewer 3:

A bias in how people infer the amount of control they have over their environment is widely believed to be a key component of several mental illnesses including depression, anxiety, and addiction. Accordingly, this bias has been a major focus in computational models of those disorders. However, all of these models treat control as a unidimensional property, roughly, how strongly outcomes depend on action. This paper proposes---correctly, I think---that the intuitive notion of "control" captures multiple dimensions in the relationship between action and outcome is multi-dimensional. In particular, the authors propose that the degree to which outcome depends on how much *effort* we exert, calling this dimension the "elasticity of control". They additionally propose that this dimension (rather than the more holistic notion of controllability) may be specifically impaired in certain types of psychopathology. This idea thus has the potential to change how we think about mental disorders in a substantial way, and could even help us better understand how healthy people navigate challenging decision-making problems.

Unfortunately, my view is that neither the theoretical nor empirical aspects of the paper really deliver on that promise. In particular, most (perhaps all) of the interesting claims in the paper have weak empirical support.

We appreciate the Reviewer's thoughtful engagement with our research and recognition of the potential significance of distinguishing between different dimensions of control in understanding psychopathology. We believe that all the Reviewer’s comments can be addressed with clarifications or additional analyses, as detailed below.  

Starting with theory, the elasticity idea does not truly "extend" the standard control model in the way the authors suggest. The reason is that effort is simply one dimension of action. Thus, the proposed model ultimately grounds out in how strongly our outcomes depend on our actions (as in the standard model). Contrary to the authors' claims, the elasticity of control is still a fixed property of the environment. Consistent with this, the computational model proposed here is a learning model of this fixed environmental property. The idea is still valuable, however, because it identifies a key dimension of action (namely, effort) that is particularly relevant to the notion of perceived control. Expressing the elasticity idea in this way might support a more general theoretical formulation of the idea that could be applied in other contexts. See Huys & Dayan (2009), Zorowitz, Momennejad, & Daw (2018), and Gagne & Dayan (2022) for examples of generalizable formulations of perceived control.

We thank the Reviewer for the suggestion that we formalize our concept of elasticity to resource investment, which we agree is a dimension of action. We first note that we have not argued against the claim that elasticity is a fixed property of the environment. We surmise the Reviewer might have misread our statement that “controllability is not a fixed property of the environment”. The latter statement is motivated by the observation that controllability is often higher for agents that can invest more resources (e.g., a richer person can buy more things). We will clarify this in our revision of the manuscript.

To formalize elasticity, we build on Huys & Dayan’s definition of controllability(1) as the fraction of reward that is controllably achievable, 𝜒 (though using information-theoretic definitions(2,3) would work as well). To the extent that this fraction depends on the amount of resources the agent is able and willing to invest (max 𝐶), this formulation can be probabilistically computed without information about the particular agent involved, specifically, by assuming a certain distribution of agents with different amounts of available resources. This would result in a probability distribution over 𝜒. Elasticity can thus be defined as the amount of information obtained about controllability due to knowing the amount of resources available to the agent: I(𝜒; max 𝐶). We will add this formal definition to the manuscript.  

Turning to experiment, the authors make two key claims: (1) people infer the elasticity of control, and (2) individual differences in how people make this inference are importantly related to psychopathology. Starting with claim 1, there are three sub-claims here; implicitly, the authors make all three. (1A) People's behavior is sensitive to differences in elasticity, (1B) people actually represent/track something like elasticity, and (1C) people do so naturally as they go about their daily lives. The results clearly support 1A. However, 1B and 1C are not supported. Starting with 1B, the experiment cannot support the claim that people represent or track elasticity because the effort is the only dimension over which participants can engage in any meaningful decision-making (the other dimension, selecting which destination to visit, simply amounts to selecting the location where you were just told the treasure lies). Thus, any adaptive behavior will necessarily come out in a sensitivity to how outcomes depend on effort. More concretely, any model that captures the fact that you are more likely to succeed in two attempts than one will produce the observed behavior. The null models do not make this basic assumption and thus do not provide a useful comparison.

We appreciate the reviewer's critical analysis of our claims regarding elasticity inference, which as detailed below, has led to an important new analysis that strengthens the study’s conclusions. However, we respectfully disagree with two of the Reviewer’s arguments. First, resource investment was not the only meaningful decision dimension in our task, since participant also needed to choose the correct vehicle to get to the right destination. That this was not trivial is evidenced by our exclusion of over 8% of participants who made incorrect vehicle choices more than 10% of the time. Included participants also occasionally erred in this choice (mean error rate = 3%, range [0-10%]). 

Second, the experimental task cannot be solved well by a model that simply tracks how outcomes depend on effort because 20% of the time participants reached the treasure despite failing to board their vehicle of choice. In such cases, reward outcomes and control were decoupled. Participants could identify when this was the case by observing the starting location, which was revealed together with the outcome (since depending on the starting location, the treasure location was automatically reached by walking). To determine whether participants distinguished between control-related and non-control-related reward, we have now fitted a variant of our model to the data that allows learning from each of these kinds of outcomes by means of a different free parameter. The results show that participants learned considerably more from control-related outcomes. They were thus not merely tracking outcomes, but specifically inferred when outcomes can be attributed to control. We will include this new analysis in the revised manuscript.

Controllability inference by itself, however, still does not suffice to explain the observed behavior. This is shown by our ‘controllability’ model, which learns to invest more resources to improve control, yet still fails to capture key features of participants’ behavior, as detailed in the manuscript. This means that explaining participants’ behavior requires a model that not only infers controllability—beyond merely outcome probability—but also assumes a priori that increased effort could enhance control. Building these a priori assumption into the model amounts to embedding within it an understanding of elasticity – the idea that control over the environment may be increased by greater resource investment. 

That being said, we acknowledge the value in considering alternative computational formulations of adaptation to elasticity. Thus, in our revision of the manuscript, we will add a discussion concerning possible alternative models.  

For 1C, the claim that people infer elasticity outside of the experimental task cannot be supported because the authors explicitly tell people about the two notions of control as part of the training phase: "To reinforce participants' understanding of how elasticity and controllability were manifested in each planet, [participants] were informed of the planet type they had visited after every 15 trips." (line 384).

We thank the reviewer for highlighting this point. We agree that our experimental design does not test whether people infer elasticity spontaneously. Our research question was whether people can distinguish between elastic and inelastic controllability. The results strongly support that they can, and this does have potential implications for behavior outside of the experimental task. Specifically, to the extent that people are aware that in some contexts additional resource investment improve control, whereas in other contexts it does not, then our results indicate that they would be able to distinguish between these two kinds of contexts through trial-and-error learning. That said, we agree that investigating whether and how people spontaneously infer elasticity is an interesting direction for future work. We will clarify the scope of the present conclusions in the revised manuscript.

Finally, I turn to claim 2, that individual differences in how people infer elasticity are importantly related to psychopathology. There is much to say about the decision to treat psychopathology as a unidimensional construct. However, I will keep it concrete and simply note that CCA (by design) obscures the relationship between any two variables. Thus, as suggestive as Figure 6B is, we cannot conclude that there is a strong relationship between Sense of Agency and the elasticity bias---this result is consistent with any possible relationship (even a negative one). The fact that the direct relationship between these two variables is not shown or reported leads me to infer that they do not have a significant or strong relationship in the data.

We agree that CCA is not designed to reveal the relationship between any two variables. However, the advantage of this analysis is that it pulls together information from multiple variables. Doing so does not treat psychopathology as unidimensional. Rather, it seeks a particular dimension that most strongly correlates with different aspects of task performance. This is especially useful for multidimensional psychopathology data because such data are often dominated by strong correlations between dimensions, whereas the research seeks to explain the distinctions between the dimensions. Similar considerations hold for the multidimensional task parameters, which although less correlated, may still jointly predict the relevant psychopathological profile better than each parameter does in isolation. Thus, the CCA enabled us to identify a general relationship between task performance and psychopathology that accounts for different symptom measures and aspects of controllability inference. 

Using CCA can thus reveal relationships that do not readily show up in two-variable analyses. Indeed, the direct correlation between Sense of Agency (SOA) and elasticity bias was not significant – a result that, for completeness, we will now report in the supplementary materials along with all other direct correlations. We note, however, that the CCA analysis was preregistered and its results were replicated. Furthermore, an auxiliary analysis specifically confirmed the contributions of both elasticity bias (Figure 6D, bottom plot) and, although not reported in the original paper, of the Sense of Agency score (SOA; p\=.03 permutation test) to the observed canonical correlation. Participants scoring higher on the psychopathology profile also overinvested resources in inelastic environments but did not futilely invest in uncontrollable environments (Figure 6A), providing external validation to the conclusion that the CCA captured meaningful variance specific to elasticity inference. The results thus enable us to safely conclude that differences in elasticity inferences are significantly associated with a profile of controlrelated psychopathology to which SOA contributed significantly.  

Finally, whereas interpretation of individual CCA loadings that were not specifically tested remains speculative, we note that the pattern of loadings largely replicated across the initial and replication studies (see Figure 6B), and aligns with prior findings. For instance, the positive loadings of SOA and OCD match prior suggestions that a lower sense of control leads to greater compensatory effort(7), whereas the negative loading for depression scores matches prior work showing reduced resource investment in depression(5-6).

We will revise the text to better clarify the advantageous and disadvantageous of our analytical approach, and the conclusions that can and cannot be drawn from it.

There is also a feature of the task that limits our ability to draw strong conclusions about individual differences in elasticity inference. As the authors clearly acknowledge, the task was designed "to be especially sensitive to overestimation of elasticity" (line 287). A straightforward consequence of this is that the resulting *empirical* estimate of estimation bias (i.e., the gamma_elasticity parameter) is itself biased. This immediately undermines any claim that references the directionality of the elasticity bias (e.g. in the abstract). Concretely, an undirected deficit such as slower learning of elasticity would appear as a directed overestimation bias. When we further consider that elasticity inference is the only meaningful learning/decisionmaking problem in the task (argued above), the situation becomes much worse. Many general deficits in learning or decision-making would be captured by the elasticity bias parameter. Thus, a conservative interpretation of the results is simply that psychopathology is associated with impaired learning and decision-making.

We apologize for our imprecise statement that the task was ‘especially sensitive to overestimation of elasticity’, which justifiably led to Reviewer’s concern that slower elasticity learning can be mistaken for elasticity bias. To make sure this was not the case, we made use of the fact that our computational model explicitly separates bias direction (λ) from the rate of learning through two distinct parameters, which initialize the prior concentration and mean of the model’s initial beliefs concerning elasticity (see Methods pg. 22). The higher the concentration of the initial beliefs (𝜖), the slower the learning. Parameter recovery tests confirmed that our task enables acceptable recovery of both the bias λ_elasticity (r=.81) and the concentration 𝝐_elasticity (r=.59) parameters. And importantly, the level of confusion between the parameters was low (confusion of 0.15 for 𝝐_elasticity→ λ_elasticity and 0.04 for λ_elasticity→ 𝝐_elasticity). This result confirms that our task enables dissociating elasticity biases from the rate of elasticity learning. 

Moreover, to validate that the minimal level of confusion existing between bias and the rate of learning did not drive our psychopathology results, we re-ran the CCA while separating concentration from bias parameters. The results (Author response image 1) demonstrate that differences in learning rate (𝜖) had virtually no contribution to our CCA results, whereas the contribution of the pure bias (𝜆) was preserved. 

We will incorporate these clarifications and additional analysis in our revised manuscript.

Author response image 1.

Showing that a model parameter correlates with the data it was fit to does not provide any new information, and cannot support claims like "a prior assumption that control is likely available was reflected in a futile investment of resources in uncontrollable environments." To make that claim, one must collect independent measures of the assumption and the investment.

We apologize if this and related statements seemed to be describing independent findings. They were merely meant to describe the relationship between model parameters and modelindependent measures of task performance. It is inaccurate, though, to say that they provide no new information, since results could have been otherwise. For instance, instead of a higher controllability bias primarily associating with futile investment of resources in uncontrollable environments, it could have been primarily associated with more proper investment of resources in high-controllability environments. Additionally, we believe these analyses are of value to readers who seek to understand the role of different parameters in the model. In our planned revision, we will clarify that the relevant analyses are merely descriptive. 

Did participants always make two attempts when purchasing tickets? This seems to violate the intuitive model, in which you would sometimes succeed on the first jump. If so, why was this choice made? Relatedly, it is not clear to me after a close reading how the outcome of each trial was actually determined.

We thank the reviewer for highlighting the need to clarify these aspects of the task in the revised manuscript. 

When participants purchased two extra tickets, they attempted both jumps, and were never informed about whether either of them succeeded. Instead, after choosing a vehicle and attempting both jumps, participants were notified where they arrived at. This outcome was determined based on the cumulative probability of either of the two jumps succeeding. Success meant that participants arrived at where their chosen vehicle goes, whereas failure meant they walked to the nearest location (as determined by where they started from). 

Though it is unintuitive to attempt a second jump before seeing whether the first succeed, this design choice ensured two key objectives. First, that participants would consistently need to invest not only more money but also more effort and time in planets with high elastic controllability. Second, that the task could potentially generalize to the many real-world situations where the amount of invested effort has to be determined prior to seeing any outcome, for instance, preparing for an exam or a job interview. 

It should be noted that the model is heuristically defined and does not reflect Bayesian updating. In particular, it overestimates control by not using losses with less than 3 tickets (intuitively, the inference here depends on your beliefs about elasticity). I wonder if the forced three-ticket trials in the task might be historically related to this modeling choice.

We apologize for not making this clear, but in fact losing with less than 3 tickets does reduce the model’s estimate of available control. It does so by increasing the elasticity estimates

(a_elastic≥1, a_elastic2 parameters), signifying that more tickets are needed to obtain the maximum available level of control, thereby reducing the average controllability estimate across ticket investment options. 

It would be interesting to further develop the model such that losing with less than 3 tickets would also impact inferences concerning the maximum available control, depending on present beliefs concerning elasticity, but the forced three-ticket purchases already expose participants to the maximum available control, and thus, the present data may not be best suited to test such a model. These trials were implemented to minimize individual differences concerning inferences of maximum available control, thereby focusing differences on elasticity inferences. We will discuss the Reviewer’s suggestion for a potentially more accurate model in the revised manuscript. 

References

(1) Huys, Q. J. M., & Dayan, P. (2009). A Bayesian formulation of behavioral control. Cognition, 113(3), 314– 328.

(2) Ligneul, R. (2021). Prediction or causation? Towards a redefinition of task controllability. Trends in Cognitive Sciences, 25(6), 431–433.

(3) Mistry, P., & Liljeholm, M. (2016). Instrumental divergence and the value of control. Scientific Reports, 6, 36295.

(4) Lin, J. (1991). Divergence measures based on the Shannon entropy. IEEE Transactions on Information Theory, 37(1), 145–151

(5) Cohen RM, Weingartner H, Smallberg SA, Pickar D, Murphy DL. Effort and cognition in depression. Arch Gen Psychiatry. 1982 May;39(5):593-7. doi: 10.1001/archpsyc.1982.04290050061012. PMID: 7092490.

(6) Bi R, Dong W, Zheng Z, Li S, Zhang D. Altered motivation of effortful decision-making for self and others in subthreshold depression. Depress Anxiety. 2022 Aug;39(8-9):633-645. doi: 10.1002/da.23267. Epub 2022 Jun 3. PMID: 35657301; PMCID: PMC9543190.

(7) Tapal, A., Oren, E., Dar, R., & Eitam, B. (2017). The Sense of Agency Scale: A measure of consciously perceived control over one's mind, body, and the immediate environment. Frontiers in Psychology, 8, 1552

Author response:

Reviewer 1:

There are no significant weaknesses to signal in the manuscript. However, in order to fully conclude that there is no obvious advantage for the linguistic dimension in neonates, it would have been most useful to test a third condition in which the two dimensions were pitted against each other, that is, in which they provide conflicting information as to the boundaries of the words comprised in the artificial language. This last condition would have allowed us to determine whether statistical learning weighs linguistic and non-linguistic features equally, or whether phonetic content is preferentially processed.

We appreciate the reviewers' suggestion that a stream with conflicting information would provide valuable insights. In the present study, we started with a simpler case involving two orthogonal features (i.e., phonemes and voices), with one feature being informative and the other uninformative, and we found similar learning capacities for both. Future work should explore whether infants—and humans more broadly—can simultaneously track regularities in multiple speech features. However, creating a stream with two conflicting statistical structures is challenging. To use neural entrainment, the two features must lead to segmentation at different chunk sizes so that their effects lead to changes in power/PLV at different frequencies—for instance, using duplets for the voice dimension and triplets for the linguistic dimension  (or vice versa). Consequently, the two dimensions would not be directly comparable within the same participant in terms of the number of distinguishable syllables/voices, memory demand, or SNR given the 1/F decrease in amplitude of background EEG activity. This would involve comparisons between two distinct groups counter-balancing chunk size and linguistic non-linguistic dimension. Considering the test phase, words for one dimension would have been part-words for the other dimension. As we are measuring differences and not preferences, interpreting the results would also have been difficult. Additionally, it may be difficult to find a sufficient number of clearly discriminable voices for such a design (triplets imply 12 voices). Therefore, an entirely different experimental paradigm would need to be developed.

If such a design were tested, one possibility is that the regularities for the two dimensions are calculated in parallel, in line with the idea that the calculation of statistical regularities is a ubiquitous implicit mechanism (see Benjamin et al., 2024, for a proposed neural mechanism). Yet, similar to our present study, possibly only phonetic features would be used as word candidates. Another possibility is that only one informative feature would be explicitly processed at a time due to the serial nature of perceptual awareness, which may prioritise one feature over the other.

Note: The reviewer’s summary contains a typo: syllabic rate (4 Hz) –not 2 Hz, and word rate (2 Hz) –not 4 Hz.

Reviewer 2:

N400: I am skeptical regarding the interpretation of the phoneme-specific ERP effect as a precursor of the N400 and would suggest toning it down. While the authors are correct in that infant ERP components are typically slower and more posterior compared to adult components, and the observed pattern is hence consistent with an adult N400, at the same time, it could also be a lot of other things. On a functional level, I can't follow the author's argument as to why a violation in phoneme regularity should elicit an N400, since there is no evidence for any semantic processing involved. In sum, I think there is just not enough evidence from the present paradigm to confidently call it an N400.

The reviewer is correct that we cannot definitively determine the type of processing reflected by the ERP component that appears when neonates hear a triplet after exposure to a stream with phonetic regularities. We interpreted this component as a precursor to the N400, based on prior findings in speech segmentation tasks without semantic content, where a ~400 ms component emerged when adult participants recognised pseudowords (Sander et al., 2002) or during structured streams of syllables (Cunillera et al., 2006, 2009). Additionally, the component we observed had a similar topography and timing to those labelled as N400 in infant studies, where semantic processing was involved (Parise et al., 2010; Friedrich & Friederici, 2011).

Given our experimental design, the difference we observed must be related to the type of regularity during familiarisation (either phonemes or voices). Thus, we interpreted this component as reflecting lexical search— a process which could be triggered by a linguistic structure but which would not be relevant to a non-linguistic regularity such as voices. However, we are open to alternative interpretations. In any case, this difference between the two streams reveals that computing regularities based on phonemes versus voices does not lead to the same processes. We will revise and tone down the corresponding part of the discussion to clarify that it is just a possible interpretation of the results.  

Female and male voices: Why did the authors choose to include male and female voices? While using both female and male stimuli of course leads to a higher generalizability, it also introduces a second dimension for one feature that is not present for this other (i.e., phoneme for Experiment 1 and voice identity plus gender for Experiment 2). Hence, couldn't it also be that the infants extracted the regularity with which one gender voice followed the other? For instance, in List B, in the words, one gender is always followed by the other (M-F or F-M), while in 2/3 of the part-words, the gender is repeated (F-F and M-M). Wouldn't you expect the same pattern of results if infants learned regularities based on gender rather than identity?

We used three female and three male voices to maximise acoustic variability. The streams were synthesised using MBROLA, which provides a limited set of artificial voices. Indeed, there were not enough French voices of acceptable quality, so we also used two Italian voices (the phonemes used existed in both Italian and French).

Voices differ in timbre, and female voices tend to be higher pitched. However, it is sometimes difficult to categorise low-pitched female voices and high-pitched male voices. Given that gender may be an important factor in infants' speech perception (newborns, for instance, prefer female voices at birth), we conducted tests to assess whether this dimension could have influenced our results.  

We first quantified the transitional probabilities matrices during the structured stream of Experiment 2, considering that there are only two types of voices: Female and Male.  

For List A, all transition probabilities are equal to 0.5 (P(M|F), P(F|M), P(M|M), P(F|F)), resulting in flat TPs throughout the stream (see Author response image 1, top). Therefore, we would not expect neural entrainment at the word rate (2 Hz), nor would we anticipate ERP differences between the presented duplets in the test phase.

For List B, P(M|F)=P(F|M)=0.66 while P(M|M)=P(F|F)=0.33. However, this does not produce a regular pattern of TP drops throughout the stream (see Author response image 1, bottom). As a result, strong neural entrainment at 2 Hz was unlikely, although some degree of entrainment might have occasionally occurred due to some drops occurring at a 2 Hz frequency. Regarding the test phase, all three Words and only one Part-word presented alternating patterns (TP=0.6). Therefore, the difference in the ERPs between Words and Partwords in List B might be attributed to gender alternation.  

However, it seems unlikely that gender alternation alone explains the entire pattern of results, as the effect is inconsistent and appears in only one of the lists. To rule out this possibility, we analysed the effects in each list separately.

Author response image 1.

Transition probabilities (TPs) across the structured stream in Experiment 2, considering voices processed by gender (Female or Male). Top: List A. Bottom: List B.

We computed the mean activation within the time windows and electrodes of interest and compared the effects of word type and list using a two-way ANOVA. For the difference between Words and Part-words over the positive cluster, we observed a main effect of word type (F(1,31) = 5.902, p = 0.021), with no effects of list or interactions (p > 0.1). Over the negative cluster, we again observed a main effect of word type (F(1,31) = 10.916, p = 0.0016), with no effects of list or interactions (p > 0.1). See Author response image 2.  

Author response image 2.

Difference in ERP voltage (Words – Part-words) for the two lists (A and B); W=Words; P=Part-Words, 

We conducted a similar analysis for neural entrainment during the structured stream on voices. A comparison of entrainment at 2 Hz between participants who completed List A and List B showed no significant differences (t(30) = -0.27, p = 0.79). A test against zero for each list indicated significant entrainment in both cases (List A: t(17) = 4.44, p = 0.00036; List B: t(13) = 3.16, p = 0.0075). See Author response image 3.

Author response image 3.

Neural entrainment at 2Hz during the structured stream of Experiment 2 for Lists A and B.

Words entrainment over occipital electrodes: Do you have any idea why the duplet entrainment effect occurs over the electrodes it does, in particular over the occipital electrodes (which seems a bit unintuitive given that this is a purely auditory experiment with sleeping neonates).

Neural entrainment might be considered as a succession of evoked response induced by the stream. After applying an average reference in high-density EEG recordings, the auditory ERP in neonates typically consists of a central positivity and a posterior negativity with a source located at the electrical zero in a single-dipole model (i.e. approximately in the superior temporal region (Dehaene-Lambertz & Dehaene, 1994). In adults, because of the average reference (i.e. the sum of voltages is equal to zero at each time point) and because the electrodes cannot capture the negative pole of the auditory response, the negativity is distributed around the head. In infants, however, the brain is higher within the skull, allowing for a more accurate recording of the negative pole of the auditory ERP (see Author response image 4 for the location of electrodes in an infant head model).  

Besides the posterior electrodes, we can see some entrainment on more anterior electrodes that probably corresponds to the positive pole of the auditory ERP.

Author response image 4.

International 10–20 sensors' location on the skull of an infant template, with the underlying 3-D reconstruction of the grey-white matter interface and projection of each electrode to the cortex. Computed across 16 infants (from Kabdebon et al, Neuroimage, 2014). The O1, O2, T5, and T6 electrodes project lower than in adults.

Reviewer 3:

(1) While it's true that voice is not essential for language (i.e., sign languages are implemented over gestures; the use of voices to produce non-linguistic sounds, like laughter), it is a feature of spoken languages. Thus I'm not sure if we can really consider this study as a comparison between linguistic and non-linguistic dimensions. In turn, I'm not sure that these results show that statistical learning at birth operates on non-linguistic features, being voices a linguistic dimension at least in spoken languages. I'd like to hear the authors' opinions on this.

On one hand, it has been shown that statistical learning (SL) operates across multiple modalities and domains in human adults and animals. On the other hand, SL is considered essential for infants to begin parsing speech. Therefore, we aimed to investigate whether SL capacities at birth are more effective on linguistic dimensions of speech, potentially as a way to promote language learning.

We agree with the reviewer that voices play an important role in communication (e.g., for identifying who is speaking); however, they do not contribute to language structure or meaning, and listeners are expected to normalize across voices to accurately perceive phonemes and words. Thus, voices are speech features but not linguistic features. Additionally, in natural speech, there are no abrupt voice changes within a word as in our experiment; instead, voice changes typically occur on a longer timescale and involve only a limited number of voices, such as in a dialogue. Therefore, computing regularities based on voice changes would not be useful in real-life language learning. We considered that contrasting syllables and voices was an elegant way to test SL beyond its linguistic dimension, as the experimental paradigm is identical in both experiments.  

Along the same line, in the Discussion section, the present results are interpreted within a theoretical framework showing statistical learning in auditory non-linguistic (string of tones, music) and visual domains as well as visual and other animal species. I'm not sure if that theoretical framework is the right fit for the present results.

(2) I'm not sure whether the fact that we see parallel and independent tracking of statistics in the two dimensions of speech at birth indicates that newborns would be able to do so in all the other dimensions of the speech. If so, what other dimensions are the authors referring to?

The reviewer is correct that demonstrating the universality of SL requires testing additional modalities and acoustic dimensions. However, we postulate that SL is grounded in a basic mechanism of long-term associative learning, as proposed in Benjamin et al. (2024), which relies on a slow decay in the representation of a given event. This simple mechanism, capable of operating on any representational output, accounts for many types of sequence learning reported in the literature (Benjamin et al., in preparation). We will revise the discussion section to clarify this theoretical framework.

(3) Lines 341-345: Statistical learning is an evolutionary ancient learning mechanism but I do not think that the present results are showing it. This is a study on human neonates and adults, there are no other animal species involved therefore I do not see a connection with the evolutionary history of statistical learning. It would be much more interesting to make claims on the ontogeny (rather than philogeny) of statistical learning, and what regularities newborns are able to detect right after birth. I believe that this is one of the strengths of this work.

We did not intend to make claims about the phylogeny of SL. Since SL appears to be a learning mechanism shared across species, we use it as a framework to suggest that SL may arise from general operational principles applicable to diverse neural networks. Thus, while it is highly useful for language acquisition, it is not specific to it. We will revise this section to tone down our claims.  

(4) The description of the stimuli in Lines 110-113 is a bit confusing. In Experiment 1, e.g., "pe" and "tu" are both uttered by the same voice, correct? ("random voice each time" is confusing). Whereas in Experiment 2, e.g., "pe" and "tu" are uttered by different voices, for example, "pe" by yellow voice and "tu" by red voice. If this is correct, then I recommend the authors to rephrase this section to make it more clear.

To clarify, in Experiment 1, the voices were randomly assigned to each syllable, with the constraint that no voice was repeated consecutively. This means that syllables within the same word were spoken by different voices, and each syllable was heard with various voices throughout the stream. As a result, neonates had to retrieve the words based solely on syllabic patterns, without relying on consistent voice associations or specific voice relationships.

In Experiment 2, the design was orthogonal: while the syllables were presented in a random order, the voices followed a structured pattern. Similar to Experiment 1, each syllable (e.g., “pe” and “tu”) was spoken by different voices. The key difference is that in Experiment 2, the structured regularities were applied to the voices rather than the syllables. In other words, the “green” voice was always followed by the “red” voice for example but uttered different syllables.

We will revise the methods section to clarify these important points.

(5) Line 114: the sentence "they should compute a 36 x 36 TPs matrix relating each acoustic signal, with TPs alternating between 1/6 within words and 1/12 between words" is confusing as it seems like there are different acoustic signals. Can the authors clarify this point?

Thank you for highlighting this point. To clarify, our suggestion is that neonates might not track regularities between phonemes and voices as separate features. Instead, they may treat each syllable-voice combination as a distinct item—for example, "pe" spoken by the "yellow" voice is one item, while "pe" spoken by the "red" voice is another. Under this scenario, there would be a total of 36 unique items (6 syllables × 6 voices), and infants would need to track regularities between these 36 combinations.

We will rephrase this sentence in the manuscript to make it clearer.

Author response:

Public Reviews:

Reviewer #1 (Public review):

We thank the reviewer for his valuable input and careful assessment, which have significantly improved the clarity and rigor of our manuscript.

Summary:

Mazer & Yovel 2025 dissect the inverse problem of how echolocators in groups manage to navigate their surroundings despite intense jamming using computational simulations.

The authors show that despite the 'noisy' sensory environments that echolocating groups present, agents can still access some amount of echo-related information and use it to navigate their local environment. It is known that echolocating bats have strong small and large-scale spatial memory that plays an important role for individuals. The results from this paper also point to the potential importance of an even lower-level, short-term role of memory in the form of echo 'integration' across multiple calls, despite the unpredictability of echo detection in groups. The paper generates a useful basis to think about the mechanisms in echolocating groups for experimental investigations too.

Strengths:

(1) The paper builds on biologically well-motivated and parametrised 2D acoustics and sensory simulation setup to investigate the various key parameters of interest

(2) The 'null-model' of echolocators not being able to tell apart objects & conspecifics while echolocating still shows agents successfully emerge from groups - even though the probability of emergence drops severely in comparison to cognitively more 'capable' agents. This is nonetheless an important result showing the direction-of-arrival of a sound itself is the 'minimum' set of ingredients needed for echolocators navigating their environment.

(3) The results generate an important basis in unraveling how agents may navigate in sensorially noisy environments with a lot of irrelevant and very few relevant cues.

(4) The 2D simulation framework is simple and computationally tractable enough to perform multiple runs to investigate many variables - while also remaining true to the aim of the investigation.

Weaknesses:

There are a few places in the paper that can be misunderstood or don't provide complete details. Here is a selection:

(1) Line 61: '... studies have focused on movement algorithms while overlooking the sensory challenges involved' : This statement does not match the recent state of the literature. While the previous models may have had the assumption that all neighbours can be detected, there are models that specifically study the role of limited interaction arising from a potential inability to track all neighbours due to occlusion, and the effect of responding to only one/few neighbours at a time e.g. Bode et al. 2011 R. Soc. Interface, Rosenthal et al. 2015 PNAS, Jhawar et al. 2020 Nature Physics.

We appreciate the reviewer's comment and the relevant references. We have revised the manuscript accordingly to clarify the distinction between studies that incorporate limited interactions and those that explicitly analyze sensory constraints and interference. We have refined our statement to acknowledge these contributions while maintaining our focus on sensory challenges beyond limited neighbor detection, such as signal degradation, occlusion effects, and multimodal sensory integration (see lines 61-64):

While collective movement has been extensively studied in various species, including insect swarming, fish schooling, and bird murmuration (Pitcher, Partridge and Wardle, 1976; Partridge, 1982; Strandburg-Peshkin et al., 2013; Pearce et al., 2014; Rosenthal, Twomey, Hartnett, Wu, Couzin, et al., 2015; Bastien and Romanczuk, 2020; Davidson et al., 2021; Aidan, Bleichman and Ayali, 2024), as well as in swarm robotics agents performing tasks such as coordinated navigation and maze-solving (Faria Dias et al., 2021; Youssefi and Rouhani, 2021; Cheraghi, Shahzad and Graffi, 2022), most studies have focused on movement algorithms , often assuming full detection of neighbors (Parrish and Edelstein-Keshet, 1999; Couzin et al., 2002, 2005; Sumpter et al., 2008; Nagy et al., 2010; Bialek et al., 2012; Gautrais et al., 2012; Attanasi et al., 2014). Some models have incorporated limited interaction rules where individuals respond to one or a few neighbors due to sensory constraints (Bode, Franks and Wood, 2011; Jhawar et al., 2020). However, fewer studies explicitly examine how sensory interference, occlusion, and noise shape decision-making in collective systems (Rosenthal et al., 2015).

(2) The word 'interference' is used loosely places (Line 89: '...took all interference signals...', Line 319: 'spatial interference') - this is confusing as it is not clear whether the authors refer to interference in the physics/acoustics sense, or broadly speaking as a synonym for reflections and/or jamming.

To improve clarity, we have revised the manuscript to distinguish between different types of interference:

· Acoustic interference (jamming): Overlapping calls that completely obscure echo detection, preventing bats from perceiving necessary environmental cues.

· Acoustic interference (masking): Partial reduction in signal clarity due to competing calls.

· Spatial interference: Physical obstruction by conspecifics affecting movement and navigation.

We have updated the manuscript to use these terms consistently and explicitly define them in relevant sections (see lines 87-94 and 329-330). This distinction ensures that the reader can differentiate between interference as an acoustic phenomenon and its broader implications in navigation.

(3) The paper discusses original results without reference to how they were obtained or what was done. The lack of detail here must be considered while interpreting the Discussion e.g. Line 302 ('our model suggests...increasing the call-rate..' - no clear mention of how/where call-rate was varied) & Line 323 '..no benefit beyond a certain level..' - also no clear mention of how/where call-level was manipulated in the simulations.

All tested parameters, including call rate dynamics and call intensity variations, are detailed in the Methods section and Tables 1 and 2. Specifically:

· Call Rate Variation: The Inter-Pulse Interval (IPI) was modeled based on documented echolocation behavior, decreasing from 100 msec during the search phase to 35 msec (~28 calls per second) at the end of the approach phase, and to 5 msec (200 calls per second) during the final buzz (see Table 2). This natural variation in call rate was not manually manipulated in the model but emerged from the simulated bat behavior.

· Call Intensity Variation: The tested call intensity levels (100, 110, 120, 130 dB SPL) are presented in Table 1 under the “Call Level” parameter. The effect of increasing call intensity was analyzed in relation to exit probability, jamming probability, and collision rate. This is now explicitly referenced in the Discussion.

We have revised the manuscript to explicitly reference these aspects in the Results and Discussion sections.

Reviewer #2 (Public review):

We are grateful for the reviewer’s insightful feedback, which has helped us clarify key aspects of our research and strengthen our conclusions.

This manuscript describes a detailed model of bats flying together through a fixed geometry. The model considers elements that are faithful to both bat biosonar production and reception and the acoustics governing how sound moves in the air and interacts with obstacles. The model also incorporates behavioral patterns observed in bats, like one-dimensional feature following and temporal integration of cognitive maps. From a simulation study of the model and comparison of the results with the literature, the authors gain insight into how often bats may experience destructive interference of their acoustic signals and those of their peers, and how much such interference may actually negatively affect the groups' ability to navigate effectively. The authors use generalized linear models to test the significance of the effects they observe.

In terms of its strengths, the work relies on a thoughtful and detailed model that faithfully incorporates salient features, such as acoustic elements like the filter for a biological receiver and temporal aggregation as a kind of memory in the system. At the same time, the authors' abstract features are complicating without being expected to give additional insights, as can be seen in the choice of a two-dimensional rather than three-dimensional system. I thought that the level of abstraction in the model was perfect, enough to demonstrate their results without needless details. The results are compelling and interesting, and the authors do a great job discussing them in the context of the biological literature.

The most notable weakness I found in this work was that some aspects of the model were not entirely clear to me.

For example, the directionality of the bat's sonar call in relation to its velocity. Are these the same?

For simplicity, in our model, the head is aligned with the body, therefore the direction of the echolocation beam is the same as the direction of the flight.

Moreover, call directionality (directivity) is not directly influenced by velocity. Instead, directionality is estimated using the piston model, as described in the Methods section. The directionality is based on the emission frequency and is thus primarily linked to the behavioral phases of the bat, with frequency shifts occurring as the bat transitions from search to approach to buzz phases. During the approach phase, the bat emits calls with higher frequencies, resulting in increased directionality. This is supported by the literature (Jakobsen and Surlykke, 2010; Jakobsen, Brinkløv and Surlykke, 2013). This phase is also associated with a natural reduction in flight speed, which is a well-documented behavioral adaptation in echolocating bats (Jakobsen et al., 2024).

To clarify this in the manuscript, we have updated the text to explicitly state that directionality follows phase-dependent frequency changes rather than being a direct function of velocity, see lines 460-465.

If so, what is the difference between phi_target and phi_tx in the model equations?

represents the angle between the bat and the reflected object (target).

the angle [rad], between the masking bat and target (from the transmitter’s perspective)

refers to the angle between the transmitting conspecific and the receiving focal bat, from the transmitter’s point of view.

represents the angle between the receiving bat and the transmitting bat, from the receiver’s point of view.

These definitions have been explicitly stated in the revised manuscript to prevent any ambiguity (lines 467-468). Additionally, a Supplementary figure demonstrating the geometrical relations has been added to the manuscript.

Author response image 1.

What is a bat's response to colliding with a conspecific (rather than a wall)?

In nature, minor collisions between bats are common and typically do not result in significant disruptions to flight (Boerma et al., 2019; Roy et al., 2019; Goldstein et al., 2024).Given this, our model does not explicitly simulate the physical impact of a collision event. Instead, during the collision event the bat keeps decreasing its velocity and changing its flight direction until the distance between bats is above the threshold (0.4 m). We assume that the primary cost of such interactions arises from the effort required to avoid collisions, rather than from the collision itself. This assumption aligns with observations of bat behavior in dense flight environments, where individuals prioritize collision avoidance rather than modeling post-collision dynamics.

From the statistical side, it was not clear if replicate simulations were performed. If they were, which I believe is the right way due to stochasticity in the model, how many replicates were used, and are the standard errors referred to throughout the paper between individuals in the same simulation or between independent simulations, or both?

The number of repetitions for each scenario is detailed in Table 1, but we included it in a more prominent location in the text for clarity. Specifically, we now state (Lines 274-275):

"The number of repetitions for each scenario was as follows: 1 bat: 240; 2 bats: 120; 5 bats: 48; 10 bats: 24; 20 bats: 12; 40 bats: 12; 100 bats: 6."

Regarding the reported standard errors, they are calculated across all individuals within each scenario, without distinguishing between different simulation trials.

We clarified in the revised text (Lines 534-535 in Statistical Analysis)

Overall, I found these weaknesses to be superficial and easily remedied by the authors. The authors presented well-reasoned arguments that were supported by their results, and which were used to demonstrate how call interference impacts the collective's roost exit as measured by several variables. As the authors highlight, I think this work is valuable to individuals interested in bat biology and behavior, as well as to applications in engineered multi-agent systems like robotic swarms.

Reviewer #3 (Public review):

We sincerely appreciate the reviewer’s thoughtful comments and the time invested in evaluating our work, which have greatly contributed to refining our study.

We would like to note that in general, our model often simplifies some of the bats’ abilities, under the assumption that if the simulated bats manage to perform this difficult task with simpler mechanisms, real better adapted bats will probably perform even better. This thought strategy will be repeated in several of the answers below.

Summary:

The authors describe a model to mimic bat echolocation behavior and flight under high-density conditions and conclude that the problem of acoustic jamming is less severe than previously thought, conflating the success of their simulations (as described in the manuscript) with hard evidence for what real bats are actually doing. The authors base their model on two species of bats that fly at "high densities" (defined by the authors as colony sizes from tens to tens of thousands of individuals and densities of up to 33.3 bats/m2), Pipistrellus kuhli and Rhinopoma microphyllum. This work fits into the broader discussion of bat sensorimotor strategies during collective flight, and simulations are important to try to understand bat behavior, especially given a lack of empirical data. However, I have major concerns about the assumptions of the parameters used for the simulation, which significantly impact both the results of the simulation and the conclusions that can be made from the data. These details are elaborated upon below, along with key recommendations the authors should consider to guide the refinement of the model.

Strengths:

This paper carries out a simulation of bat behavior in dense swarms as a way to explain how jamming does not pose a problem in dense groups. Simulations are important when we lack empirical data. The simulation aims to model two different species with different echolocation signals, which is very important when trying to model echolocation behavior. The analyses are fairly systematic in testing all ranges of parameters used and discussing the differential results.

Weaknesses:

The justification for how the different foraging phase call types were chosen for different object detection distances in the simulation is unclear. Do these distances match those recorded from empirical studies, and if so, are they identical for both species used in the simulation?

The distances at which bats transition between echolocation phases are identical for both species in our model (see Table 2). These distances are based on well-documented empirical studies of bat hunting and obstacle avoidance behavior (Griffin, Webster and Michael, 1958; Simmons and Kick, 1983; Schnitzler et al., 1987; Kalko, 1995; Hiryu et al., 2008; Vanderelst and Peremans, 2018). These references provide extensive evidence that insectivorous bats systematically adjust their echolocation calls in response to object proximity, following the characteristic phases of search, approach, and buzz.

To improve clarity, we have updated the text to explicitly state that the phase transition distances are empirically grounded and apply equally to both modeled species (lines 430-447).

What reasoning do the authors have for a bat using the same call characteristics to detect a cave wall as they would for detecting a small insect?

In echolocating bats, call parameters are primarily shaped by the target distance and echo strength. Accordingly, there is little difference in call structure between prey capture and obstacles-related maneuvers, aside from intensity adjustments based on target strength (Hagino et al., 2007; Hiryu et al., 2008; Surlykke, Ghose and Moss, 2009; Kothari et al., 2014). In our study, due to the dense cave environment, the bats are found to operate in the approach phase nearly all the time, which is consistent with natural cave emergence, where they are navigating through a cluttered environment rather than engaging in open-space search. For one of the species (Rhinopoma M.), we also have empirical recordings of individuals flying under similar conditions (Goldstein et al., 2024). Our model was designed to remain as simple as possible while relying on conservative assumptions that may underestimate bat performance. If, in reality, bats fine-tune their echolocation calls even earlier or more precisely during navigation than assumed, our model would still conservatively reflect their actual capabilities.

We actually used logarithmically frequency modulated (FM) chirps, generated using the MATLAB built-in function chirp(t, f0, t1, f1, 'logarithmic'). This method aligns with the nonlinear FM characteristics of Pipistrellus kuhlii (PK) and Rhinopoma microphyllum (RM) and provides a realistic approximation of their echolocation signals. We acknowledge that this was not sufficiently emphasized in the original text, and we have now explicitly highlighted this in the revised version to ensure clarity (sell Lines 447-449 in Methods).

The two species modeled have different calls. In particular, the bandwidth varies by a factor of 10, meaning the species' sonars will have different spatial resolutions. Range resolution is about 10x better for PK compared to RM, but the authors appear to use the same thresholds for "correct detection" for both, which doesn't seem appropriate.

The detection process in our model is based on Saillant’s method using a filter bank, as detailed in the paper (Saillant et al., 1993; Neretti et al., 2003; Sanderson et al., 2003). This approach inherently incorporates the advantages of a wider bandwidth, meaning that the differences in range resolution between the species are already accounted for within the signal-processing framework. Thus, there is no need to explicitly adjust the model parameters for bandwidth variations, as these effects emerge from the applied method.

Also, the authors did not mention incorporating/correcting for/exploiting Doppler, which leads me to assume they did not model it.

The reviewer is correct. To maintain model simplicity, we did not incorporate the Doppler effect or its impact on echolocation. The exclusion of Doppler effects was based on the assumption that while Doppler shifts can influence frequency perception, their impact on jamming and overall navigation performance is minor within the modelled context.

The maximal Doppler shifts expected for the bats in this scenario are of ~ 1kHz. These shifts would be applied variably across signals due to the semi-random relative velocities between bats, leading to a mixed effect on frequency changes. This variability would likely result in an overall reduction in jamming rather than exacerbating it, aligning with our previous statement that our model may overestimate the severity of acoustic interference. Such Doppler shifts would result in errors of 2-4 cm in localization (i.e., 200-400 micro-seconds) (Boonman, Parsons and Jones, 2003). 

We have now explicitly highlighted this in the revised version (see Lines 468-470).

The success of the simulation may very well be due to variation in the calls of the bats, which ironically enough demonstrates the importance of a jamming avoidance response in dense flight. This explains why the performance of the simulation falls when bats are not able to distinguish their own echoes from other signals. For example, in Figure C2, there are calls that are labeled as conspecific calls and have markedly shorter durations and wider bandwidths than others. These three phases for call types used by the authors may be responsible for some (or most) of the performance of the model since the correlation between different call types is unlikely to exceed the detection threshold. But it turns out this variation in and of itself is what a jamming avoidance response may consist of. So, in essence, the authors are incorporating a jamming avoidance response into their simulation.

We fully agree that the natural variations in call design between the phases contribute significantly to interference reduction (see our discussion in a previous paper in Mazar & Yovel, 2020). However, we emphasize that this cannot be classified as a Jamming Avoidance Response (JAR). In our model, bats respond only to the physical presence of objects and not to the acoustic environment or interference itself. There is no active or adaptive adjustment of call design to minimize jamming beyond the natural phase-dependent variations in call structure. Therefore, while variation in call types does inherently reduce interference, this effect emerges passively from the modeled behavior rather than as an intentional strategy to avoid jamming.

The authors claim that integration over multiple pings (though I was not able to determine the specifics of this integration algorithm) reduces the masking problem. Indeed, it should: if you have two chances at detection, you've effectively increased your SNR by 3dB.

The reviewer is correct. Indeed, integration over multiple calls improves signal-to-noise ratio (SNR), effectively increasing it by approximately 3 dB per doubling of observations. The specifics of the integration algorithm are detailed in the Methods section, where we describe how sensory information is aggregated across multiple time steps to enhance detection reliability.

They also claim - although it is almost an afterthought - that integration dramatically reduces the degradation caused by false echoes. This also makes sense: from one ping to the next, the bat's own echo delays will correlate extremely well with the bat's flight path. Echo delays due to conspecifics will jump around kind of randomly. However, the main concern is regarding the time interval and number of pings of the integration, especially in the context of the bat's flight speed. The authors say that a 1s integration interval (5-10 pings) dramatically reduces jamming probability and echo confusion. This number of pings isn't very high, and it occurs over a time interval during which the bat has moved 5-10m. This distance is large compared to the 0.4m distance-to-obstacle that triggers an evasive maneuver from the bat, so integration should produce a latency in navigation that significantly hinders the ability to avoid obstacles. Can the authors provide statistics that describe this latency, and discussion about why it doesn't seem to be a problem?

As described in the Methods section, the bat’s collision avoidance response does not solely rely on the integration process. Instead, the model incorporates real-time echoes from the last calls, which are used independently of the integration process for immediate obstacle avoidance maneuvers. This ensures that bats can react to nearby obstacles without being hindered by the integration latency. The slower integration on the other hand is used for clustering, outlier removal and estimation wall directions to support the pathfinding process, as illustrated in Supplementary Figure 1.

Additionally, our model assumes that bats store the physical positions of echoes in an allocentric coordinate system (x-y). The integration occurs after transforming these detections from a local relative reference frame to a global spatial representation. This allows for stable environmental mapping while maintaining responsiveness to immediate changes in the bat’s surroundings.

See lines 518-523 in the revied version.

The authors are using a 2D simulation, but this very much simplifies the challenge of a 3D navigation task, and there is an explanation as to why this is appropriate. Bat densities and bat behavior are discussed per unit area when realistically it should be per unit volume. In fact, the authors reference studies to justify the densities used in the simulation, but these studies were done in a 3D world. If the authors have justification for why it is realistic to model a 3D world in a 2D simulation, I encourage them to provide references justifying this approach.

We acknowledge that this is a simplification; however, from an echolocation perspective, a 2D framework represents a worst-case scenario in terms of bat densities and maneuverability:

· Higher Effective Density: A 2D model forces all bats into a single plane rather than distributing them through a 3D volume, increasing the likelihood of overlap in calls and echoes and making jamming more severe. As described in the text: the average distance to the nearest bat in our simulation is 0.27m (with 100 bats), whereas reported distances in very dense colonies are 0.5m, as observed in Myotis grisescens and Tadarida brasiliensis (Fujioka et al., 2021; Sabol and Hudson, 1995; Betke et al., 2008; Gillam et al, 2010)

· Reduced Maneuverability: In 3D space, bats can use vertical movement to avoid obstacles and conspecifics. A 2D constraint eliminates this degree of freedom, increasing collision risk and limiting escape options.

Thus, our 2D model provides a conservative difficult test case, ensuring that our findings are valid under conditions where jamming and collision risks are maximized. Additionally, the 2D framework is computationally efficient, allowing us to perform multiple simulation runs to explore a broad parameter space and systematically test the impact of different variables.

To address the reviewer’s concern, we have clarified this justification in the revised text and will provide supporting references where applicable: (see Methods lines 407-412)

The focus on "masking" (which appears to be just in-band noise), especially relative to the problem of misassigned echoes, is concerning. If the bat calls are all the same waveform (downsweep linear FM of some duration, I assume - it's not clear from the text), false echoes would be a major problem. Masking, as the authors define it, just reduces SNR. This reduction is something like sqrt(N), where N is the number of conspecifics whose echoes are audible to the bat, so this allows the detection threshold to be set lower, increasing the probability that a bat's echo will exceed a detection threshold. False echoes present a very different problem. They do not reduce SNR per se, but rather they cause spurious threshold excursions (N of them!) that the bat cannot help but interpret as obstacle detection. I would argue that in dense groups the mis-assignment problem is much more important than the SNR problem.

There is substantial literature supporting the assumption that bats can recognize their own echoes and distinguish them from conspecific signals (Schnitzler and Bioscience, 2001‏; Kazial, Burnett and Masters, 2001; Burnett and Masters, 2002; Kazial, Kenny and Burnett, 2008; Chili, Xian and Moss, 2009; Yovel et al., 2009; Beetz and Hechavarría, 2022). However, we acknowledge that false echoes may present a major challenge in dense groups. To address this, we explicitly tested the impact of the self-echo identification assumption in our study see Results Figure 4: The impact of confusion on performance, and lines 345-355 in the Discussion.

Furthermore, we examined a full confusion scenario, where all reflected echoes from conspecifics were misinterpreted as obstacle reflections (i.e., 100% confusion). Our results show that this significantly degrades navigation performance, supporting the argument that echo misassignment is a critical issue. However, we also explored a simple mitigation strategy based on temporal integration with outlier rejection, which provided some improvement in performance. This suggests that real bats may possess additional mechanisms to enhance self-echo identification and reduce false detections. See lines XX in the manuscript for further discussion.

The criteria set for flight behavior (lines 393-406) are not justified with any empirical evidence of the flight behavior of wild bats in collective flight. How did the authors determine the avoidance distances? Also, what is the justification for the time limit of 15 seconds to emerge from the opening? Instead of an exit probability, why not instead use a time criterion, similar to "How long does it take X% of bats to exit?"

While we acknowledge that wild bats may employ more complex behaviors for collision avoidance, we chose to implement a simplified decision-making rule in our model to maintain computational tractability.

The avoidance distances (1.5 m from walls and 0.4 m from other bats) were selected as internal parameters to ensure coherent flight trajectories while maintaining a reasonable collision rate. These distances provide a balance between maneuverability and stability, preventing erratic flight patterns while still enabling effective obstacle avoidance. In the revised paper, we have added supplementary figures illustrating the effect of model parameters on performance, specifically focusing on the avoidance distance.

The 15-second exit limit was determined as described in the text (Lines 403-404): “A 15-second window was chosen because it is approximately twice the average exit time for 40 bats and allows for a second corrective maneuver if needed.” In other words, it allowed each bat to circle the ‘cave’ twice to exit even in the most crowded environment. This threshold was set to keep simulation time reasonable while allowing sufficient time for most bats to exit successfully.

We acknowledge that the alternative approach suggested by the reviewer—measuring the time taken for a certain percentage of bats to exit—is also valid. However, in our model, some outlier bats fail to exit and continue flying for many minutes, Such simulations would lead to excessive simulation times making it difficult to generate repetitions and not teaching us much – they usually resulted from the bat slightly missing the opening (see video S1. Our chosen approach ensures practical runtime constraints while still capturing relevant performance metrics.

What is the empirical justification for the 1-10 calls used for integration?

The "average exit time for 40 bats" is also confusing and not well explained. Was this determined empirically? From the simulation? If the latter, what are the conditions? Does it include masking, no masking, or which species?

Previous studies have demonstrated that bats integrate acoustic information received sequentially over several echolocation calls (2-15), effectively constructing an auditory scene in complex environments (Ulanovsky and Moss, 2008; Chili, Xian and Moss, 2009; Moss and Surlykke, 2010; Yovel and Ulanovsky, 2017; Salles, Diebold and Moss, 2020). Additionally, bats are known to produce echolocation sound groups when spatiotemporal localization demands are high (Kothari et al., 2014). Studies have documented call sequences ranging from 2 to 15 grouped calls (Moss et al., 2010), and it has been hypothesized that grouping facilitates echo segregation.

We did not use a single integration window - we tested integration sizes between 1 and 10 calls and presented the results in Figure 3A. This range was chosen based on prior empirical findings and to explore how different levels of temporal aggregation impact navigation performance. Indeed, the results showed that the performance levels between 5-10 calls integration window (Figure 3A)

Regarding the average exit time for 40 bats, this value was determined from our simulations, where it represents the mean time for successful exits under standard conditions with masking.

We have revised the text to clarify these details see, lines 466.

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Author response:

eLife Assessment 

This valuable study investigates how the neural representation of individual finger movements changes during the early period of sequence learning. By combining a new method for extracting features from human magnetoencephalography data and decoding analyses, the authors provide incomplete evidence of an early, swift change in the brain regions correlated with sequence learning, including a set of previously unreported frontal cortical regions. The addition of more control analyses to rule out that head movement artefacts influence the findings, and to further explain the proposal of offline contextualization during short rest periods as the basis for improvement performance would strengthen the manuscript. 

We appreciate the Editorial assessment on our paper’s strengths and novelty.  We have implemented additional control analyses to show that neither task-related eye movements nor increasing overlap of finger movements during learning account for our findings, which are that contextualized neural representations in a network of bilateral frontoparietal brain regions actively contribute to skill learning.  Importantly, we carried out additional analyses showing that contextualization develops predominantly during rest intervals.

Public Reviews:

We thank the Reviewers for their comments and suggestions, prompting new analyses and additions that strengthened our report.

Reviewer #1 (Public review): 

Summary: 

This study addresses the issue of rapid skill learning and whether individual sequence elements (here: finger presses) are differentially represented in human MEG data. The authors use a decoding approach to classify individual finger elements and accomplish an accuracy of around 94%. A relevant finding is that the neural representations of individual finger elements dynamically change over the course of learning. This would be highly relevant for any attempts to develop better brain machine interfaces - one now can decode individual elements within a sequence with high precision, but these representations are not static but develop over the course of learning. 

Strengths: The work follows a large body of work from the same group on the behavioural and neural foundations of sequence learning. The behavioural task is well established and neatly designed to allow for tracking learning and how individual sequence elements contribute. The inclusion of short offline rest periods between learning epochs has been influential because it has revealed that a lot, if not most of the gains in behaviour (ie speed of finger movements) occur in these so-called micro-offline rest periods. The authors use a range of new decoding techniques, and exhaustively interrogate their data in different ways, using different decoding approaches. Regardless of the approach, impressively high decoding accuracies are observed, but when using a hybrid approach that combines the MEG data in different ways, the authors observe decoding accuracies of individual sequence elements from the MEG data of up to 94%. 

We have previously showed that neural replay of MEG activity representing the practiced skill correlated with micro-offline gains during rest intervals of early learning, 1 consistent with the recent report that hippocampal ripples during these offline periods predict human motor sequence learning2.  However, decoding accuracy in our earlier work1 needed improvement.  Here, we reported a strategy to improve decoding accuracy that could benefit future studies of neural replay or BCI using MEG.

Weaknesses: 

There are a few concerns which the authors may well be able to resolve. These are not weaknesses as such, but factors that would be helpful to address as these concern potential contributions to the results that one would like to rule out. Regarding the decoding results shown in Figure 2 etc, a concern is that within individual frequency bands, the highest accuracy seems to be within frequencies that match the rate of keypresses. This is a general concern when relating movement to brain activity, so is not specific to decoding as done here. As far as reported, there was no specific restraint to the arm or shoulder, and even then it is conceivable that small head movements would correlate highly with the vigor of individual finger movements. This concern is supported by the highest contribution in decoding accuracy being in middle frontal regions - midline structures that would be specifically sensitive to movement artefacts and don't seem to come to mind as key structures for very simple sequential keypress tasks such as this - and the overall pattern is remarkably symmetrical (despite being a unimanual finger task) and spatially broad. This issue may well be matching the time course of learning, as the vigor and speed of finger presses will also influence the degree to which the arm/shoulder and head move. This is not to say that useful information is contained within either of the frequencies or broadband data. But it raises the question of whether a lot is dominated by movement "artefacts" and one may get a more specific answer if removing any such contributions. 

Reviewer #1 expresses concern that the combination of the low-frequency narrow-band decoder results, and the bilateral middle frontal regions displaying the highest average intra-parcel decoding performance across subjects is suggestive that the decoding results could be driven by head movement or other artefacts.

Head movement artefacts are highly unlikely to contribute meaningfully to our results for the following reasons. First, in addition to ICA denoising, all “recordings were visually inspected and marked to denoise segments containing other large amplitude artifacts due to movements” (see Methods). Second, the response pad was positioned in a manner that minimized wrist, arm or more proximal body movements during the task. Third, while head position was not monitored online for this study, the head was restrained using an inflatable air bladder, and head position was assessed at the beginning and at the end of each recording. Head movement did not exceed 5mm between the beginning and end of each scan for all participants included in the study. Fourth, we agree that despite the steps taken above, it is possible that minor head movements could still contribute to some remaining variance in the MEG data in our study. The Reviewer states a concern that “it is conceivable that small head movements would correlate highly with the vigor of individual finger movements”. However, in order for any such correlations to meaningfully impact decoding performance, such head movements would need to: (A) be consistent and pervasive throughout the recording (which might not be the case if the head movements were related to movement vigor and vigor changed over time); and (B) systematically vary between different finger movements, and also between the same finger movement performed at different sequence locations (see 5-class decoding performance in Figure 4B). The possibility of any head movement artefacts meeting all these conditions is extremely unlikely.

Given the task design, a much more likely confound in our estimation would be the contribution of eye movement artefacts to the decoder performance (an issue appropriately raised by Reviewer #3 in the comments below). Remember from Figure 1A in the manuscript that an asterisk marks the current position in the sequence and is updated at each keypress. Since participants make very few performance errors, the position of the asterisk on the display is highly correlated with the keypress being made in the sequence. Thus, it is possible that if participants are attending to the visual feedback provided on the display, they may move their eyes in a way that is systematically related to the task.  Since we did record eye movements simultaneously with the MEG recordings (EyeLink 1000 Plus; Fs = 600 Hz), we were able to perform a control analysis to address this question. For each keypress event during trials in which no errors occurred (which is the same time-point that the asterisk position is updated), we extracted three features related to eye movements: 1) the gaze position at the time of asterisk position update (or keyDown event), 2) the gaze position 150ms later, and 3) the peak velocity of the eye movement between the two positions. We then constructed a classifier from these features with the aim of predicting the location of the asterisk (ordinal positions 1-5) on the display. As shown in the confusion matrix below (Author response image 1), the classifier failed to perform above chance levels (Overall cross-validated accuracy = 0.21817):

Author response image 1.

Confusion matrix showing that three eye movement features fail to predict asterisk position on the task display above chance levels (Fold 1 test accuracy = 0.21718; Fold 2 test accuracy = 0.22023; Fold 3 test accuracy = 0.21859; Fold 4 test accuracy = 0.22113; Fold 5 test accuracy = 0.21373; Overall cross-validated accuracy = 0.2181). Since the ordinal position of the asterisk on the display is highly correlated with the ordinal position of individual keypresses in the sequence, this analysis provides strong evidence that keypress decoding performance from MEG features is not explained by systematic relationships between finger movement behavior and eye movements (i.e. – behavioral artefacts).

In fact, inspection of the eye position data revealed that a majority of participants on most trials displayed random walk gaze patterns around a center fixation point, indicating that participants did not attend to the asterisk position on the display. This is consistent with intrinsic generation of the action sequence, and congruent with the fact that the display does not provide explicit feedback related to performance. A similar real-world example would be manually inputting a long password into a secure online application. In this case, one intrinsically generates the sequence from memory and receives similar feedback about the password sequence position (also provided as asterisks), which is typically ignored by the user. The minimal participant engagement with the visual task display observed in this study highlights another important point – that the behavior in explicit sequence learning motor tasks is highly generative in nature rather than reactive to stimulus cues as in the serial reaction time task (SRTT).  This is a crucial difference that must be carefully considered when designing investigations and comparing findings across studies.

We observed that initial keypress decoding accuracy was predominantly driven by contralateral primary sensorimotor cortex in the initial practice trials before transitioning to bilateral frontoparietal regions by trials 11 or 12 as performance gains plateaued.  The contribution of contralateral primary sensorimotor areas to early skill learning has been extensively reported in humans and non-human animals. 1,3-5  Similarly, the increased involvement of bilateral frontal and parietal regions to decoding during early skill learning in the non-dominant hand is well known.  Enhanced bilateral activation in both frontal and parietal cortex during skill learning has been extensively reported6-11, and appears to be even more prominent during early fine motor skill learning in the non-dominant hand12,13.  The frontal regions identified in these studies are known to play crucial roles in executive control14, motor planning15, and working memory6,8,16-18 processes, while the same parietal regions are known to integrate multimodal sensory feedback and support visuomotor transformations6,8,16-18, in addition to working memory19. Thus, it is not surprising that these regions increasingly contribute to decoding as subjects internalize the sequential task.  We now include a statement reflecting these considerations in the revised Discussion.

A somewhat related point is this: when combining voxel and parcel space, a concern is whether a degree of circularity may have contributed to the improved accuracy of the combined data, because it seems to use the same MEG signals twice - the voxels most contributing are also those contributing most to a parcel being identified as relevant, as parcels reflect the average of voxels within a boundary. In this context, I struggled to understand the explanation given, ie that the improved accuracy of the hybrid model may be due to "lower spatially resolved whole-brain and higher spatially resolved regional activity patterns".

We strongly disagree with the Reviewer’s assertion that the construction of the hybrid-space decoder is circular. To clarify, the base feature set for the hybrid-space decoder constructed for all participants includes whole-brain spatial patterns of MEG source activity averaged within parcels. As stated in the manuscript, these 148 inter-parcel features reflect “lower spatially resolved whole-brain activity patterns” or global brain dynamics. We then independently test how well spatial patterns of MEG source activity for all voxels distributed within individual parcels can decode keypress actions. Again, the testing of these intra-parcel spatial patterns, intended to capture “higher spatially resolved regional brain activity patterns”, is completely independent from one another and independent from the weighting of individual inter-parcel features. These intra-parcel features could, for example, provide additional information about muscle activation patterns or the task environment. These approximately 1150 intra-parcel voxels (on average, within the total number varying between subjects) are then combined with the 148 inter-parcel features to construct the final hybrid-space decoder. In fact, this varied spatial filter approach shares some similarities to the construction of convolutional neural networks (CNNs) used to perform object recognition in image classification applications. One could also view this hybrid-space decoding approach as a spatial analogue to common time-frequency based analyses such as theta-gamma phase amplitude coupling (PAC), which combine information from two or more narrow-band spectral features derived from the same time-series data.

We directly tested this hypothesis – that spatially overlapping intra- and inter-parcel features portray different information – by constructing an alternative hybrid-space decoder (HybridAlt) that excluded average inter-parcel features which spatially overlapped with intra-parcel voxel features, and comparing the performance to the decoder used in the manuscript (HybridOrig). The prediction was that if the overlapping parcel contained similar information to the more spatially resolved voxel patterns, then removing the parcel features (n=8) from the decoding analysis should not impact performance. In fact, despite making up less than 1% of the overall input feature space, removing those parcels resulted in a significant drop in overall performance greater than 2% (78.15% ± SD 7.03% for HybridOrig vs. 75.49% ± SD 7.17% for HybridAlt; Wilcoxon signed rank test, z = 3.7410, p = 1.8326e-04) (Author response image 2).

Author response image 2.

Comparison of decoding performances with two different hybrid approaches. HybridAlt: Intra-parcel voxel-space features of top ranked parcels and inter-parcel features of remaining parcels. HybridOrig:  Voxel-space features of top ranked parcels and whole-brain parcel-space features (i.e. – the version used in the manuscript). Dots represent decoding accuracy for individual subjects. Dashed lines indicate the trend in performance change across participants. Note, that HybridOrig (the approach used in our manuscript) significantly outperforms the HybridAlt approach, indicating that the excluded parcel features provide unique information compared to the spatially overlapping intra-parcel voxel patterns.

Firstly, there will be a relatively high degree of spatial contiguity among voxels because of the nature of the signal measured, i.e. nearby individual voxels are unlikely to be independent. Secondly, the voxel data gives a somewhat misleading sense of precision; the inversion can be set up to give an estimate for each voxel, but there will not just be dependence among adjacent voxels, but also substantial variation in the sensitivity and confidence with which activity can be projected to different parts of the brain. Midline and deeper structures come to mind, where the inversion will be more problematic than for regions along the dorsal convexity of the brain, and a concern is that in those midline structures, the highest decoding accuracy is seen. 

We definitely agree with the Reviewer that some inter-parcel features representing neighboring (or spatially contiguous) voxels are likely to be correlated. This has been well documented in the MEG literature20,21 and is a particularly important confound to address in functional or effective connectivity analyses (not performed in the present study). In the present analysis, any correlation between adjacent voxels presents a multi-collinearity problem, which effectively reduces the dimensionality of the input feature space. However, as long as there are multiple groups of correlated voxels within each parcel (i.e. - the effective dimensionality is still greater than 1), the intra-parcel spatial patterns could still meaningfully contribute to the decoder performance. Two specific results support this assertion.

First, we obtained higher decoding accuracy with voxel-space features [74.51% (± SD 7.34%)] compared to parcel space features [68.77% (± SD 7.6%)] (Figure 3B), indicating individual voxels carry more information in decoding the keypresses than the averaged voxel-space features or parcel-space features.  Second, Individual voxels within a parcel showed varying feature importance scores in decoding keypresses (Author response image 3). This finding supports the Reviewer’s assertion that neighboring voxels express similar information, but also shows that the correlated voxels form mini subclusters that are much smaller spatially than the parcel they reside in.

Author response image 3.

Feature importance score of individual voxels in decoding keypresses: MRMR was used to rank the individual voxel space features in decoding keypresses and the min-max normalized MRMR score was mapped to a structural brain surface. Note that individual voxels within a parcel showed different contribution to decoding.

Some of these concerns could be addressed by recording head movement (with enough precision) to regress out these contributions. The authors state that head movement was monitored with 3 fiducials, and their time courses ought to provide a way to deal with this issue. The ICA procedure may not have sufficiently dealt with removing movement-related problems, but one could eg relate individual components that were identified to the keypresses as another means for checking. An alternative could be to focus on frequency ranges above the movement frequencies. The accuracy for those still seems impressive and may provide a slightly more biologically plausible assessment. 

We have already addressed the issue of movement related artefacts in the first response above. With respect to a focus on frequency ranges above movement frequencies, the Reviewer states the “accuracy for those still seems impressive and may provide a slightly more biologically plausible assessment”. First, it is important to note that cortical delta-band oscillations measured with local field potentials (LFPs) in macaques is known to contain important information related to end-effector kinematics22,23 muscle activation patterns24 and temporal sequencing25 during skilled reaching and grasping actions. Thus, there is a substantial body of evidence that low-frequency neural oscillatory activity in this range contains important information about the skill learning behavior investigated in the present study. Second, our own data shows (which the Reviewer also points out) that significant information related to the skill learning behavior is also present in higher frequency bands (see Figure 2A and Figure 3—figure supplement 1). As we pointed out in our earlier response to questions about the hybrid space decoder architecture (see above), it is likely that different, yet complimentary, information is encoded across different temporal frequencies (just as it is encoded across different spatial frequencies). Again, this interpretation is supported by our data as the highest performing classifiers in all cases (when holding all parameters constant) were always constructed from broadband input MEG data (Figure 2A and Figure 3—figure supplement 1).  

One question concerns the interpretation of the results shown in Figure 4. They imply that during the course of learning, entirely different brain networks underpin the behaviour. Not only that, but they also include regions that would seem rather unexpected to be key nodes for learning and expressing relatively simple finger sequences, such as here. What then is the biological plausibility of these results? The authors seem to circumnavigate this issue by moving into a distance metric that captures the (neural network) changes over the course of learning, but the discussion seems detached from which regions are actually involved; or they offer a rather broad discussion of the anatomical regions identified here, eg in the context of LFOs, where they merely refer to "frontoparietal regions". 

The Reviewer notes the shift in brain networks driving keypress decoding performance between trials 1, 11 and 36 as shown in Figure 4A. The Reviewer questions whether these substantial shifts in brain network states underpinning the skill are biologically plausible, as well as the likelihood that bilateral superior and middle frontal and parietal cortex are important nodes within these networks.

First, previous fMRI work in humans performing a similar sequence learning task showed that flexibility in brain network composition (i.e. – changes in brain region members displaying coordinated activity) is up-regulated in novel learning environments and explains differences in learning rates across individuals26.  This work supports our interpretation of the present study data, that brain networks engaged in sequential motor skills rapidly reconfigure during early learning.

Second, frontoparietal network activity is known to support motor memory encoding during early learning27,28. For example, reactivation events in the posterior parietal29 and medial prefrontal30,31 cortex (MPFC) have been temporally linked to hippocampal replay, and are posited to support memory consolidation across several memory domains32, including motor sequence learning1,33,34.  Further, synchronized interactions between MPFC and hippocampus are more prominent during early learning as opposed to later stages27,35,36, perhaps reflecting “redistribution of hippocampal memories to MPFC” 27.  MPFC contributes to very early memory formation by learning association between contexts, locations, events and adaptive responses during rapid learning37. Consistently, coupling between hippocampus and MPFC has been shown during, and importantly immediately following (rest) initial memory encoding38,39.  Importantly, MPFC activity during initial memory encoding predicts subsequent recall40. Thus, the spatial map required to encode a motor sequence memory may be “built under the supervision of the prefrontal cortex” 28, also engaged in the development of an abstract representation of the sequence41.  In more abstract terms, the prefrontal, premotor and parietal cortices support novice performance “by deploying attentional and control processes” 42-44 required during early learning42-44. The dorsolateral prefrontal cortex DLPFC specifically is thought to engage in goal selection and sequence monitoring during early skill practice45, all consistent with the schema model of declarative memory in which prefrontal cortices play an important role in encoding46,47.  Thus, several prefrontal and frontoparietal regions contributing to long term learning 48 are also engaged in early stages of encoding. Altogether, there is strong biological support for the involvement of bilateral prefrontal and frontoparietal regions to decoding during early skill learning.  We now address this issue in the revised manuscript.

If I understand correctly, the offline neural representation analysis is in essence the comparison of the last keypress vs the first keypress of the next sequence. In that sense, the activity during offline rest periods is actually not considered. This makes the nomenclature somewhat confusing. While it matches the behavioural analysis, having only key presses one can't do it in any other way, but here the authors actually do have recordings of brain activity during offline rest. So at the very least calling it offline neural representation is misleading to this reviewer because what is compared is activity during the last and during the next keypress, not activity during offline periods. But it also seems a missed opportunity - the authors argue that most of the relevant learning occurs during offline rest periods, yet there is no attempt to actually test whether activity during this period can be useful for the questions at hand here. 

We agree with the Reviewer that our previous “offline neural representation” nomenclature could be misinterpreted. In the revised manuscript we refer to this difference as the “offline neural representational change”. Please, note that our previous work did link offline neural activity (i.e. – 16-22 Hz beta power and neural replay density during inter-practice rest periods) to observed micro-offline gains49.

Reviewer #2 (Public review): 

Summary 

Dash et al. asked whether and how the neural representation of individual finger movements is "contextualized" within a trained sequence during the very early period of sequential skill learning by using decoding of MEG signal. Specifically, they assessed whether/how the same finger presses (pressing index finger) embedded in the different ordinal positions of a practiced sequence (4-1-3-2-4; here, the numbers 1 through 4 correspond to the little through the index fingers of the non-dominant left hand) change their representation (MEG feature). They did this by computing either the decoding accuracy of the index finger at the ordinal positions 1 vs. 5 (index_OP1 vs index_OP5) or pattern distance between index_OP1 vs. index_OP5 at each training trial and found that both the decoding accuracy and the pattern distance progressively increase over the course of learning trials. More interestingly, they also computed the pattern distance for index_OP5 for the last execution of a practice trial vs. index_OP1 for the first execution in the next practice trial (i.e., across the rest period). This "off-line" distance was significantly larger than the "on-line" distance, which was computed within practice trials and predicted micro-offline skill gain. Based on these results, the authors conclude that the differentiation of representation for the identical movement embedded in different positions of a sequential skill ("contextualization") primarily occurs during early skill learning, especially during rest, consistent with the recent theory of the "micro-offline learning" proposed by the authors' group. I think this is an important and timely topic for the field of motor learning and beyond. <br /> Strengths 

The specific strengths of the current work are as follows. First, the use of temporally rich neural information (MEG signal) has a large advantage over previous studies testing sequential representations using fMRI. This allowed the authors to examine the earliest period (= the first few minutes of training) of skill learning with finer temporal resolution. Second, through the optimization of MEG feature extraction, the current study achieved extremely high decoding accuracy (approx. 94%) compared to previous works. As claimed by the authors, this is one of the strengths of the paper (but see my comments). Third, although some potential refinement might be needed, comparing "online" and "offline" pattern distance is a neat idea. 

Weaknesses 

Along with the strengths I raised above, the paper has some weaknesses. First, the pursuit of high decoding accuracy, especially the choice of time points and window length (i.e., 200 msec window starting from 0 msec from key press onset), casts a shadow on the interpretation of the main result. Currently, it is unclear whether the decoding results simply reflect behavioral change or true underlying neural change. As shown in the behavioral data, the key press speed reached 3~4 presses per second already at around the end of the early learning period (11th trial), which means inter-press intervals become as short as 250-330 msec. Thus, in almost more than 60% of training period data, the time window for MEG feature extraction (200 msec) spans around 60% of the inter-press intervals. Considering that the preparation/cueing of subsequent presses starts ahead of the actual press (e.g., Kornysheva et al., 2019) and/or potential online planning (e.g., Ariani and Diedrichsen, 2019), the decoder likely has captured these future press information as well as the signal related to the current key press, independent of the formation of genuine sequential representation (e.g., "contextualization" of individual press). This may also explain the gradual increase in decoding accuracy or pattern distance between index_OP1 vs. index_OP5 (Figure 4C and 5A), which co-occurred with performance improvement, as shorter inter-press intervals are more favorable for the dissociating the two index finger presses followed by different finger presses. The compromised decoding accuracies for the control sequences can be explained in similar logic. Therefore, more careful consideration and elaborated discussion seem necessary when trying to both achieve high-performance decoding and assess early skill learning, as it can impact all the subsequent analyses.

The Reviewer raises the possibility that (given the windowing parameters used in the present study) an increase in “contextualization” with learning could simply reflect faster typing speeds as opposed to an actual change in the underlying neural representation. The issue can essentially be framed as a mixing problem. As correct sequences are generated at higher and higher speeds over training, MEG activity patterns related to the planning, execution, evaluation and memory of individual keypresses overlap more in time. Thus, increased overlap between the “4” and “1” keypresses (at the start of the sequence) and “2” and “4” keypresses (at the end of the sequence) could artefactually increase contextualization distances even if the underlying neural representations for the individual keypresses remain unchanged (assuming this mixing of representations is used by the classifier to differentially tag each index finger press). If this were the case, it follows that such mixing effects reflecting the ordinal sequence structure would also be observable in the distribution of decoder misclassifications. For example, “4” keypresses would be more likely to be misclassified as “1” or “2” keypresses (or vice versa) than as “3” keypresses. The confusion matrices presented in Figures 3C and 4B and Figure 3—figure supplement 3A in the previously submitted manuscript do not show this trend in the distribution of misclassifications across the four fingers.

Moreover, if the representation distance is largely driven by this mixing effect, it’s also possible that the increased overlap between consecutive index finger keypresses during the 4-4 transition marking the end of one sequence and the beginning of the next one could actually mask contextualization-related changes to the underlying neural representations and make them harder to detect. In this case, a decoder tasked with separating individual index finger keypresses into two distinct classes based upon sequence position might show decreased performance with learning as adjacent keypresses overlapped in time with each other to an increasing extent. However, Figure 4C in our previously submitted manuscript does not support this possibility, as the 2-class hybrid classifier displays improved classification performance over early practice trials despite greater temporal overlap.

We also conducted a new multivariate regression analysis to directly assess whether the neural representation distance score could be predicted by the 4-1, 2-4 and 4-4 keypress transition times observed for each complete correct sequence (both predictor and response variables were z-score normalized within-subject). The results of this analysis affirmed that the possible alternative explanation put forward by the Reviewer is not supported by our data (Adjusted R2 = 0.00431; F = 5.62). We now include this new negative control analysis result in the revised manuscript.

Overall, we do strongly agree with the Reviewer that the naturalistic, self-paced, generative task employed in the present study results in overlapping brain processes related to planning, execution, evaluation and memory of the action sequence. We also agree that there are several tradeoffs to consider in the construction of the classifiers depending on the study aim. Given our aim of optimizing keypress decoder accuracy in the present study, the set of trade-offs resulted in representations reflecting more the latter three processes, and less so the planning component. Whether separate decoders can be constructed to tease apart the representations or networks supporting these overlapping processes is an important future direction of research in this area. For example, work presently underway in our lab constrains the selection of windowing parameters in a manner that allows individual classifiers to be temporally linked to specific planning, execution, evaluation or memory-related processes to discern which brain networks are involved and how they adaptively reorganize with learning. Results from the present study (Figure 4—figure supplement 2) showing hybrid-space decoder prediction accuracies exceeding 74% for temporal windows spanning as little as 25ms and located up to 100ms prior to the keyDown event strongly support the feasibility of such an approach.

Related to the above point, testing only one particular sequence (4-1-3-2-4), aside from the control ones, limits the generalizability of the finding. This also may have contributed to the extremely high decoding accuracy reported in the current study. 

The Reviewer raises a question about the generalizability of the decoder accuracy reported in our study. Fortunately, a comparison between decoder performances on Day 1 and Day 2 datasets does provide some insight into this issue. As the Reviewer points out, the classifiers in this study were trained and tested on keypresses performed while practicing a specific sequence (4-1-3-2-4). The study was designed this way as to avoid the impact of interference effects on learning dynamics. The cross-validated performance of classifiers on MEG data collected within the same session was 90.47% overall accuracy (4-class; Figure 3C). We then tested classifier performance on data collected during a separate MEG session conducted approximately 24 hours later (Day 2; see Figure 3—supplement 3). We observed a reduction in overall accuracy rate to 87.11% when tested on MEG data recorded while participants performed the same learned sequence, and 79.44% when they performed several previously unpracticed sequences. Both changes in accuracy are important with regards to the generalizability of our findings. First, 87.11% performance accuracy for the trained sequence data on Day 2 (a reduction of only 3.36%) indicates that the hybrid-space decoder performance is robust over multiple MEG sessions, and thus, robust to variations in SNR across the MEG sensor array caused by small differences in head position between scans.  This indicates a substantial advantage over sensor-space decoding approaches. Furthermore, when tested on data from unpracticed sequences, overall performance dropped an additional 7.67%. This difference reflects the performance bias of the classifier for the trained sequence, possibly caused by high-order sequence structure being incorporated into the feature weights. In the future, it will be important to understand in more detail how random or repeated keypress sequence training data impacts overall decoder performance and generalization. We strongly agree with the Reviewer that the issue of generalizability is extremely important and have added a new paragraph to the Discussion in the revised manuscript highlighting the strengths and weaknesses of our study with respect to this issue.

In terms of clinical BCI, one of the potential relevance of the study, as claimed by the authors, it is not clear that the specific time window chosen in the current study (up to 200 msec since key press onset) is really useful. In most cases, clinical BCI would target neural signals with no overt movement execution due to patients' inability to move (e.g., Hochberg et al., 2012). Given the time window, the surprisingly high performance of the current decoder may result from sensory feedback and/or planning of subsequent movement, which may not always be available in the clinical BCI context. Of course, the decoding accuracy is still much higher than chance even when using signal before the key press (as shown in Figure 4 Supplement 2), but it is not immediately clear to me that the authors relate their high decoding accuracy based on post-movement signal to clinical BCI settings.

The Reviewer questions the relevance of the specific window parameters used in the present study for clinical BCI applications, particularly for paretic patients who are unable to produce finger movements or for whom afferent sensory feedback is no longer intact. We strongly agree with the Reviewer that any intended clinical application must carefully consider these specific input feature constraints dictated by the clinical cohort, and in turn impose appropriate and complimentary constraints on classifier parameters that may differ from the ones used in the present study.  We now highlight this issue in the Discussion of the revised manuscript and relate our present findings to published clinical BCI work within this context.

One of the important and fascinating claims of the current study is that the "contextualization" of individual finger movements in a trained sequence specifically occurs during short rest periods in very early skill learning, echoing the recent theory of micro-offline learning proposed by the authors' group. Here, I think two points need to be clarified. First, the concept of "contextualization" is kept somewhat blurry throughout the text. It is only at the later part of the Discussion (around line #330 on page 13) that some potential mechanism for the "contextualization" is provided as "what-and-where" binding. Still, it is unclear what "contextualization" actually is in the current data, as the MEG signal analyzed is extracted from 0-200 msec after the keypress. If one thinks something is contextualizing an action, that contextualization should come earlier than the action itself. 

The Reviewer requests that we: 1) more clearly define our use of the term “contextualization” and 2) provide the rationale for assessing it over a 200ms window aligned to the keyDown event. This choice of window parameters means that the MEG activity used in our analysis was coincident with, rather than preceding, the actual keypresses.  We define contextualization as the differentiation of representation for the identical movement embedded in different positions of a sequential skill. That is, representations of individual action elements progressively incorporate information about their relationship to the overall sequence structure as the skill is learned. We agree with the Reviewer that this can be appropriately interpreted as “what-and-where” binding. We now incorporate this definition in the Introduction of the revised manuscript as requested.

The window parameters for optimizing accurate decoding individual finger movements were determined using a grid search of the parameter space (a sliding window of variable width between 25-350 ms with 25 ms increments variably aligned from 0 to +100ms with 10ms increments relative to the keyDown event). This approach generated 140 different temporal windows for each keypress for each participant, with the final parameter selection determined through comparison of the resulting performance between each decoder.  Importantly, the decision to optimize for decoding accuracy placed an emphasis on keypress representations characterized by the most consistent and robust features shared across subjects, which in turn maximize statistical power in detecting common learning-related changes. In this case, the optimal window encompassed a 200ms epoch aligned to the keyDown event (t0 = 0 ms).  We then asked if the representations (i.e. – spatial patterns of combined parcel- and voxel-space activity) of the same digit at two different sequence positions changed with practice within this optimal decoding window.  Of course, our findings do not rule out the possibility that contextualization can also be found before or even after this time window, as we did not directly address this issue in the present study.  Ongoing work in our lab, as pointed out above, is investigating contextualization within different time windows tailored specifically for assessing sequence skill action planning, execution, evaluation and memory processes.

The second point is that the result provided by the authors is not yet convincing enough to support the claim that "contextualization" occurs during rest. In the original analysis, the authors presented the statistical significance regarding the correlation between the "offline" pattern differentiation and micro-offline skill gain (Figure 5. Supplement 1), as well as the larger "offline" distance than "online" distance (Figure 5B). However, this analysis looks like regressing two variables (monotonically) increasing as a function of the trial. Although some information in this analysis, such as what the independent/dependent variables were or how individual subjects were treated, was missing in the Methods, getting a statistically significant slope seems unsurprising in such a situation. Also, curiously, the same quantitative evidence was not provided for its "online" counterpart, and the authors only briefly mentioned in the text that there was no significant correlation between them. It may be true looking at the data in Figure 5A as the online representation distance looks less monotonically changing, but the classification accuracy presented in Figure 4C, which should reflect similar representational distance, shows a more monotonic increase up to the 11th trial. Further, the ways the "online" and "offline" representation distance was estimated seem to make them not directly comparable. While the "online" distance was computed using all the correct press data within each 10 sec of execution, the "offline" distance is basically computed by only two presses (i.e., the last index_OP5 vs. the first index_OP1 separated by 10 sec of rest). Theoretically, the distance between the neural activity patterns for temporally closer events tends to be closer than that between the patterns for temporally far-apart events. It would be fairer to use the distance between the first index_OP1 vs. the last index_OP5 within an execution period for "online" distance, as well. 

The Reviewer suggests that the current data is not convincing enough to show that contextualization occurs during rest and raises two important concerns: 1) the relationship between online contextualization and micro-online gains is not shown, and 2) the online distance was calculated differently from its offline counterpart (i.e. - instead of calculating the distance between last IndexOP5 and first IndexOP1 from a single trial, the distance was calculated for each sequence within a trial and then averaged).

We addressed the first concern by performing individual subject correlations between 1) contextualization changes during rest intervals and micro-offline gains; 2) contextualization changes during practice trials and micro-online gains, and 3) contextualization changes during practice trials and micro-offline gains (Author response image 4). We then statistically compared the resulting correlation coefficient distributions and found that within-subject correlations for contextualization changes during rest intervals and micro-offline gains were significantly higher than online contextualization and micro-online gains (t = 3.2827, p = 0.0015) and online contextualization and micro-offline gains (t = 3.7021, p = 5.3013e-04). These results are consistent with our interpretation that micro-offline gains are supported by contextualization changes during the inter-practice rest period.

Author response image 4.

Distribution of individual subject correlation coefficients between contextualization changes occurring during practice or rest with  micro-online and micro-offline performance gains. Note that, the correlation distributions were significantly higher for the relationship between contextualization changes during rest and micro-offline gains than for contextualization changes during practice and either micro-online or offline gain.

With respect to the second concern highlighted above, we agree with the Reviewer that one limitation of the analysis comparing online versus offline changes in contextualization as presented in the reviewed manuscript, is that it does not eliminate the possibility that any differences could simply be explained by the passage of time (which is smaller for the online analysis compared to the offline analysis). The Reviewer suggests an approach that addresses this issue, which we have now carried out.   When quantifying online changes in contextualization from the first IndexOP1 the last IndexOP5 keypress in the same trial we observed no learning-related trend (Author response image 5, right panel). Importantly, offline distances were significantly larger than online distances regardless of the measurement approach and neither predicted online learning (Author response image 6).

Author response image 5.

Trial by trial trend of offline (left panel) and online (middle and right panels) changes in contextualization. Offline changes in contextualization were assessed by calculating the distance between neural representations for the last IndexOP5 keypress in the previous trial and the first IndexOP1 keypress in the present trial. Two different approaches were used to characterize online contextualization changes. The analysis included in the reviewed manuscript (middle panel) calculated the distance between IndexOP1 and IndexOP5 for each correct sequence, which was then averaged across the trial. This approach is limited by the lack of control for the passage of time when making online versus offline comparisons. Thus, the second approach controlled for the passage of time by calculating distance between the representations associated with the first IndexOP1 keypress and the last IndexOP5 keypress within the same trial. Note that while the first approach showed an increase online contextualization trend with practice, the second approach did not.

Author response image 6.

Relationship between online contextualization and online learning is shown for both within-sequence (left; note that this is the online contextualization measure used in the reviewd manuscript) and across-sequence (right) distance calculation. There was no significant relationship between online learning and online contextualization regardless of the measurement approach.

A related concern regarding the control analysis, where individual values for max speed and the degree of online contextualization were compared (Figure 5 Supplement 3), is whether the individual difference is meaningful. If I understood correctly, the optimization of the decoding process (temporal window, feature inclusion/reduction, decoder, etc.) was performed for individual participants, and the same feature extraction was also employed for the analysis of representation distance (i.e., contextualization). If this is the case, the distances are individually differently calculated and they may need to be normalized relative to some stable reference (e.g., 1 vs. 4 or average distance within the control sequence presses) before comparison across the individuals. 

The Reviewer makes a good point here. We have now implemented the suggested normalization procedure in the analysis provided in the revised manuscript.

Reviewer #3 (Public review): 

Summary: 

One goal of this paper is to introduce a new approach for highly accurate decoding of finger movements from human magnetoencephalography data via dimension reduction of a "multi-scale, hybrid" feature space. Following this decoding approach, the authors aim to show that early skill learning involves "contextualization" of the neural coding of individual movements, relative to their position in a sequence of consecutive movements. Furthermore, they aim to show that this "contextualization" develops primarily during short rest periods interspersed with skill training and correlates with a performance metric which the authors interpret as an indicator of offline learning. <br /> Strengths: 

A clear strength of the paper is the innovative decoding approach, which achieves impressive decoding accuracies via dimension reduction of a "multi-scale, hybrid space". This hybrid-space approach follows the neurobiologically plausible idea of the concurrent distribution of neural coding across local circuits as well as large-scale networks. A further strength of the study is the large number of tested dimension reduction techniques and classifiers (though the manuscript reveals little about the comparison of the latter). 

We appreciate the Reviewer’s comments regarding the paper’s strengths.

A simple control analysis based on shuffled class labels could lend further support to this complex decoding approach. As a control analysis that completely rules out any source of overfitting, the authors could test the decoder after shuffling class labels. Following such shuffling, decoding accuracies should drop to chance level for all decoding approaches, including the optimized decoder. This would also provide an estimate of actual chance-level performance (which is informative over and beyond the theoretical chance level). Furthermore, currently, the manuscript does not explain the huge drop in decoding accuracies for the voxel-space decoding (Figure 3B). Finally, the authors' approach to cortical parcellation raises questions regarding the information carried by varying dipole orientations within a parcel (which currently seems to be ignored?) and the implementation of the mean-flipping method (given that there are two dimensions - space and time - what do the authors refer to when they talk about the sign of the "average source", line 477?). 

The Reviewer recommends that we: 1) conduct an additional control analysis on classifier performance using shuffled class labels, 2) provide a more detailed explanation regarding the drop in decoding accuracies for the voxel-space decoding following LDA dimensionality reduction (see Fig 3B), and 3) provide additional details on how problems related to dipole solution orientations were addressed in the present study.  

In relation to the first point, we have now implemented a random shuffling approach as a control for the classification analyses. The results of this analysis indicated that the chance level accuracy was 22.12% (± SD 9.1%) for individual keypress decoding (4-class classification), and 18.41% (± SD 7.4%) for individual sequence item decoding (5-class classification), irrespective of the input feature set or the type of decoder used. Thus, the decoding accuracy observed with the final model was substantially higher than these chance levels.  

Second, please note that the dimensionality of the voxel-space feature set is very high (i.e. – 15684). LDA attempts to map the input features onto a much smaller dimensional space (number of classes-1; e.g. –  3 dimensions, for 4-class keypress decoding). Given the very high dimension of the voxel-space input features in this case, the resulting mapping exhibits reduced accuracy. Despite this general consideration, please refer to Figure 3—figure supplement 3, where we observe improvement in voxel-space decoder performance when utilizing alternative dimensionality reduction techniques.

The decoders constructed in the present study assess the average spatial patterns across time (as defined by the windowing procedure) in the input feature space.  We now provide additional details in the Methods of the revised manuscript pertaining to the parcellation procedure and how the sign ambiguity problem was addressed in our analysis.

Weaknesses: 

A clear weakness of the paper lies in the authors' conclusions regarding "contextualization". Several potential confounds, described below, question the neurobiological implications proposed by the authors and provide a simpler explanation of the results. Furthermore, the paper follows the assumption that short breaks result in offline skill learning, while recent evidence, described below, casts doubt on this assumption. 

We thank the Reviewer for giving us the opportunity to address these issues in detail (see below).

The authors interpret the ordinal position information captured by their decoding approach as a reflection of neural coding dedicated to the local context of a movement (Figure 4). One way to dissociate ordinal position information from information about the moving effectors is to train a classifier on one sequence and test the classifier on other sequences that require the same movements, but in different positions50. In the present study, however, participants trained to repeat a single sequence (4-1-3-2-4). As a result, ordinal position information is potentially confounded by the fixed finger transitions around each of the two critical positions (first and fifth press). Across consecutive correct sequences, the first keypress in a given sequence was always preceded by a movement of the index finger (=last movement of the preceding sequence), and followed by a little finger movement. The last keypress, on the other hand, was always preceded by a ring finger movement, and followed by an index finger movement (=first movement of the next sequence). Figure 4 - Supplement 2 shows that finger identity can be decoded with high accuracy (>70%) across a large time window around the time of the key press, up to at least +/-100 ms (and likely beyond, given that decoding accuracy is still high at the boundaries of the window depicted in that figure). This time window approaches the keypress transition times in this study. Given that distinct finger transitions characterized the first and fifth keypress, the classifier could thus rely on persistent (or "lingering") information from the preceding finger movement, and/or "preparatory" information about the subsequent finger movement, in order to dissociate the first and fifth keypress. Currently, the manuscript provides no evidence that the context information captured by the decoding approach is more than a by-product of temporally extended, and therefore overlapping, but independent neural representations of consecutive keypresses that are executed in close temporal proximity - rather than a neural representation dedicated to context. 

Such temporal overlap of consecutive, independent finger representations may also account for the dynamics of "ordinal coding"/"contextualization", i.e., the increase in 2-class decoding accuracy, across Day 1 (Figure 4C). As learning progresses, both tapping speed and the consistency of keypress transition times increase (Figure 1), i.e., consecutive keypresses are closer in time, and more consistently so. As a result, information related to a given keypress is increasingly overlapping in time with information related to the preceding and subsequent keypresses. The authors seem to argue that their regression analysis in Figure 5 - Figure Supplement 3 speaks against any influence of tapping speed on "ordinal coding" (even though that argument is not made explicitly in the manuscript). However, Figure 5 - Figure Supplement 3 shows inter-individual differences in a between-subject analysis (across trials, as in panel A, or separately for each trial, as in panel B), and, therefore, says little about the within-subject dynamics of "ordinal coding" across the experiment. A regression of trial-by-trial "ordinal coding" on trial-by-trial tapping speed (either within-subject or at a group-level, after averaging across subjects) could address this issue. Given the highly similar dynamics of "ordinal coding" on the one hand (Figure 4C), and tapping speed on the other hand (Figure 1B), I would expect a strong relationship between the two in the suggested within-subject (or group-level) regression. Furthermore, learning should increase the number of (consecutively) correct sequences, and, thus, the consistency of finger transitions. Therefore, the increase in 2-class decoding accuracy may simply reflect an increasing overlap in time of increasingly consistent information from consecutive keypresses, which allows the classifier to dissociate the first and fifth keypress more reliably as learning progresses, simply based on the characteristic finger transitions associated with each. In other words, given that the physical context of a given keypress changes as learning progresses - keypresses move closer together in time and are more consistently correct - it seems problematic to conclude that the mental representation of that context changes. To draw that conclusion, the physical context should remain stable (or any changes to the physical context should be controlled for). 

The issues raised by Reviewer #3 here are similar to two issues raised by Reviewer #2 above and agree they must both be carefully considered in any evaluation of our findings.

As both Reviewers pointed out, the classifiers in this study were trained and tested on keypresses performed while practicing a specific sequence (4-1-3-2-4). The study was designed this way as to avoid the impact of interference effects on learning dynamics. The cross-validated performance of classifiers on MEG data collected within the same session was 90.47% overall accuracy (4-class; Figure 3C). We then tested classifier performance on data collected during a separate MEG session conducted approximately 24 hours later (Day 2; see Figure 3—supplement 3). We observed a reduction in overall accuracy rate to 87.11% when tested on MEG data recorded while participants performed the same learned sequence, and 79.44% when they performed several previously unpracticed sequences. This classification performance difference of 7.67% when tested on the Day 2 data could reflect the performance bias of the classifier for the trained sequence, possibly caused by mixed information from temporally close keypresses being incorporated into the feature weights.

Along these same lines, both Reviewers also raise the possibility that an increase in “ordinal coding/contextualization” with learning could simply reflect an increase in this mixing effect caused by faster typing speeds as opposed to an actual change in the underlying neural representation. The basic idea is that as correct sequences are generated at higher and higher speeds over training, MEG activity patterns related to the planning, execution, evaluation and memory of individual keypresses overlap more in time. Thus, increased overlap between the “4” and “1” keypresses (at the start of the sequence) and “2” and “4” keypresses (at the end of the sequence) could artefactually increase contextualization distances even if the underlying neural representations for the individual keypresses remain unchanged (assuming this mixing of representations is used by the classifier to differentially tag each index finger press). If this were the case, it follows that such mixing effects reflecting the ordinal sequence structure would also be observable in the distribution of decoder misclassifications. For example, “4” keypresses would be more likely to be misclassified as “1” or “2” keypresses (or vice versa) than as “3” keypresses. The confusion matrices presented in Figures 3C and 4B and Figure 3—figure supplement 3A in the previously submitted manuscript do not show this trend in the distribution of misclassifications across the four fingers.

Following this logic, it’s also possible that if the ordinal coding is largely driven by this mixing effect, the increased overlap between consecutive index finger keypresses during the 4-4 transition marking the end of one sequence and the beginning of the next one could actually mask contextualization-related changes to the underlying neural representations and make them harder to detect. In this case, a decoder tasked with separating individual index finger keypresses into two distinct classes based upon sequence position might show decreased performance with learning as adjacent keypresses overlapped in time with each other to an increasing extent. However, Figure 4C in our previously submitted manuscript does not support this possibility, as the 2-class hybrid classifier displays improved classification performance over early practice trials despite greater temporal overlap.

As noted in the above replay to Reviewer #2, we also conducted a new multivariate regression analysis to directly assess whether the neural representation distance score could be predicted by the 4-1, 2-4 and 4-4 keypress transition times observed for each complete correct sequence (both predictor and response variables were z-score normalized within-subject). The results of this analysis affirmed that the possible alternative explanation put forward by the Reviewer is not supported by our data (Adjusted R2 = 0.00431; F = 5.62). We now include this new negative control analysis result in the revised manuscript.

Finally, the Reviewer hints that one way to address this issue would be to compare MEG responses before and after learning for sequences typed at a fixed speed. However, given that the speed-accuracy trade-off should improve with learning, a comparison between unlearned and learned skill states would dictate that the skill be evaluated at a very low fixed speed. Essentially, such a design presents the problem that the post-training test is evaluating the representation in the unlearned behavioral state that is not representative of the acquired skill. Thus, this approach would not address our experimental question: “do neural representations of the same action performed at different locations within a skill sequence contextually differentiate or remain stable as learning evolves”.

A similar difference in physical context may explain why neural representation distances ("differentiation") differ between rest and practice (Figure 5). The authors define "offline differentiation" by comparing the hybrid space features of the last index finger movement of a trial (ordinal position 5) and the first index finger movement of the next trial (ordinal position 1). However, the latter is not only the first movement in the sequence but also the very first movement in that trial (at least in trials that started with a correct sequence), i.e., not preceded by any recent movement. In contrast, the last index finger of the last correct sequence in the preceding trial includes the characteristic finger transition from the fourth to the fifth movement. Thus, there is more overlapping information arising from the consistent, neighbouring keypresses for the last index finger movement, compared to the first index finger movement of the next trial. A strong difference (larger neural representation distance) between these two movements is, therefore, not surprising, given the task design, and this difference is also expected to increase with learning, given the increase in tapping speed, and the consequent stronger overlap in representations for consecutive keypresses. Furthermore, initiating a new sequence involves pre-planning, while ongoing practice relies on online planning (Ariani et al., eNeuro 2021), i.e., two mental operations that are dissociable at the level of neural representation (Ariani et al., bioRxiv 2023). 

The Reviewer argues that the comparison of last finger movement of a trial and the first in the next trial are performed in different circumstances and contexts. This is an important point and one we tend to agree with. For this task, the first sequence in a practice trial (which is pre-planned offline) is performed in a somewhat different context from the sequence iterations that follow, which involve temporally overlapping planning, execution and evaluation processes.  The Reviewer is particularly concerned about a difference in the temporal mixing effect issue raised above between the first and last keypresses performed in a trial. However, in contrast to the Reviewers stated argument above, findings from Korneysheva et. al (2019) showed that neural representations of individual actions are competitively queued during the pre-planning period in a manner that reflects the ordinal structure of the learned sequence.  Thus, mixing effects are likely still present for the first keypress in a trial. Also note that we now present new control analyses in multiple responses above confirming that hypothetical mixing effects between adjacent keypresses do not explain our reported contextualization finding. A statement addressing these possibilities raised by the Reviewer has been added to the Discussion in the revised manuscript.

In relation to pre-planning, ongoing MEG work in our lab is investigating contextualization within different time windows tailored specifically for assessing how sequence skill action planning evolves with learning.

Given these differences in the physical context and associated mental processes, it is not surprising that "offline differentiation", as defined here, is more pronounced than "online differentiation". For the latter, the authors compared movements that were better matched regarding the presence of consistent preceding and subsequent keypresses (online differentiation was defined as the mean difference between all first vs. last index finger movements during practice).  It is unclear why the authors did not follow a similar definition for "online differentiation" as for "micro-online gains" (and, indeed, a definition that is more consistent with their definition of "offline differentiation"), i.e., the difference between the first index finger movement of the first correct sequence during practice, and the last index finger of the last correct sequence. While these two movements are, again, not matched for the presence of neighbouring keypresses (see the argument above), this mismatch would at least be the same across "offline differentiation" and "online differentiation", so they would be more comparable. 

This is the same point made earlier by Reviewer #2, and we agree with this assessment. As stated in the response to Reviewer #2 above, we have now carried out quantification of online contextualization using this approach and included it in the revised manuscript. We thank the Reviewer for this suggestion.

A further complication in interpreting the results regarding "contextualization" stems from the visual feedback that participants received during the task. Each keypress generated an asterisk shown above the string on the screen, irrespective of whether the keypress was correct or incorrect. As a result, incorrect (e.g., additional, or missing) keypresses could shift the phase of the visual feedback string (of asterisks) relative to the ordinal position of the current movement in the sequence (e.g., the fifth movement in the sequence could coincide with the presentation of any asterisk in the string, from the first to the fifth). Given that more incorrect keypresses are expected at the start of the experiment, compared to later stages, the consistency in visual feedback position, relative to the ordinal position of the movement in the sequence, increased across the experiment. A better differentiation between the first and the fifth movement with learning could, therefore, simply reflect better decoding of the more consistent visual feedback, based either on the feedback-induced brain response, or feedback-induced eye movements (the study did not include eye tracking). It is not clear why the authors introduced this complicated visual feedback in their task, besides consistency with their previous studies.

We strongly agree with the Reviewer that eye movements related to task engagement are important to rule out as a potential driver of the decoding accuracy or contextualization effect. We address this issue above in response to a question raised by Reviewer #1 about the impact of movement related artefacts in general on our findings.

First, the assumption the Reviewer makes here about the distribution of errors in this task is incorrect. On average across subjects, 2.32% ± 1.48% (mean ± SD) of all keypresses performed were errors, which were evenly distributed across the four possible keypress responses. While errors increased progressively over practice trials, they did so in proportion to the increase in correct keypresses, so that the overall ratio of correct-to-incorrect keypresses remained stable over the training session. Thus, the Reviewer’s assumptions that there is a higher relative frequency of errors in early trials, and a resulting systematic trend phase shift differences between the visual display updates (i.e. – a change in asterisk position above the displayed sequence) and the keypress performed is not substantiated by the data. To the contrary, the asterisk position on the display and the keypress being executed remained highly correlated over the entire training session. We now include a statement about the frequency and distribution of errors in the revised manuscript.

Given this high correlation, we firmly agree with the Reviewer that the issue of eye movement-related artefacts is still an important one to address. Fortunately, we did collect eye movement data during the MEG recordings so were able to investigate this. As detailed in the response to Reviewer #1 above, we found that gaze positions and eye-movement velocity time-locked to visual display updates (i.e. – a change in asterisk position above the displayed sequence) did not reflect the asterisk location above chance levels (Overall cross-validated accuracy = 0.21817; see Author response image 1). Furthermore, an inspection of the eye position data revealed that a majority of participants on most trials displayed random walk gaze patterns around a center fixation point, indicating that participants did not attend to the asterisk position on the display. This is consistent with intrinsic generation of the action sequence, and congruent with the fact that the display does not provide explicit feedback related to performance. As pointed out above, a similar real-world example would be manually inputting a long password into a secure online application. In this case, one intrinsically generates the sequence from memory and receives similar feedback about the password sequence position (also provided as asterisks), which is typically ignored by the user. Notably, the minimal participant engagement with the visual task display observed in this study highlights an important difference between behavior observed during explicit sequence learning motor tasks (which is highly generative in nature) with reactive responses to stimulus cues in a serial reaction time task (SRTT).  This is a crucial difference that must be carefully considered when comparing findings across studies. All elements pertaining to this new control analysis are now included in the revised manuscript.

The authors report a significant correlation between "offline differentiation" and cumulative micro-offline gains. However, it would be more informative to correlate trial-by-trial changes in each of the two variables. This would address the question of whether there is a trial-by-trial relation between the degree of "contextualization" and the amount of micro-offline gains - are performance changes (micro-offline gains) less pronounced across rest periods for which the change in "contextualization" is relatively low? Furthermore, is the relationship between micro-offline gains and "offline differentiation" significantly stronger than the relationship between micro-offline gains and "online differentiation"? 

In response to a similar issue raised above by Reviewer #2, we now include new analyses comparing correlation magnitudes between (1) “online differention” vs micro-online gains, (2) “online differention” vs micro-offline gains and (3) “offline differentiation” and micro-offline gains (see Author response images 4, 5 and 6 above). These new analyses and results have been added to the revised manuscript. Once again, we thank both Reviewers for this suggestion.

The authors follow the assumption that micro-offline gains reflect offline learning.

This statement is incorrect. The original Bonstrup et al (2019) 49 paper clearly states that micro-offline gains must be carefully interpreted based upon the behavioral context within which they are observed, and lays out the conditions under which one can have confidence that micro-offline gains reflect offline learning.  In fact, the excellent meta-analysis of Pan & Rickard (2015) 51, which re-interprets the benefits of sleep in overnight skill consolidation from a “reactive inhibition” perspective, was a crucial resource in the experimental design of our initial study49, as well as in all our subsequent work. Pan & Rickard stated:

“Empirically, reactive inhibition refers to performance worsening that can accumulate during a period of continuous training (Hull, 1943). It tends to dissipate, at least in part, when brief breaks are inserted between blocks of training. If there are multiple performance-break cycles over a training session, as in the motor sequence literature, performance can exhibit a scalloped effect, worsening during each uninterrupted performance block but improving across blocks52,53. Rickard, Cai, Rieth, Jones, and Ard (2008) and Brawn, Fenn, Nusbaum, and Margoliash (2010) 52,53 demonstrated highly robust scalloped reactive inhibition effects using the commonly employed 30 s–30 s performance break cycle, as shown for Rickard et al.’s (2008) massed practice sleep group in Figure 2. The scalloped effect is evident for that group after the first few 30 s blocks of each session. The absence of the scalloped effect during the first few blocks of training in the massed group suggests that rapid learning during that period masks any reactive inhibition effect.”

Crucially, Pan & Rickard51 made several concrete recommendations for reducing the impact of the reactive inhibition confound on offline learning studies. One of these recommendations was to reduce practice times to 10s (most prior sequence learning studies up until that point had employed 30s long practice trials). They stated:

“The traditional design involving 30 s-30 s performance break cycles should be abandoned given the evidence that it results in a reactive inhibition confound, and alternative designs with reduced performance duration per block used instead 51. One promising possibility is to switch to 10 s performance durations for each performance-break cycle Instead 51. That design appears sufficient to eliminate at least the majority of the reactive inhibition effect 52,53.”

We mindfully incorporated recommendations from Pan and Rickard51  into our own study designs including 1) utilizing 10s practice trials and 2) constraining our analysis of micro-offline gains to early learning trials (where performance monotonically increases and 95% of overall performance gains occur), which are prior to the emergence of the “scalloped” performance dynamics that are strongly linked to reactive inhibition effects. 

However, there is no direct evidence in the literature that micro-offline gains really result from offline learning, i.e., an improvement in skill level.

We strongly disagree with the Reviewer’s assertion that “there is no direct evidence in the literature that micro-offline gains really result from offline learning, i.e., an improvement in skill level.”  The initial Bönstrup et al. (2019) 49 report was followed up by a large online crowd-sourcing study (Bönstrup et al., 2020) 54. This second (and much larger) study provided several additional important findings supporting our interpretation of micro-offline gains in cases where the important behavioral conditions clarified above were met (see Author response image 7 below for further details on these conditions).

Author response image 7.

Micro-offline gains observed in learning and non-learning contexts are attributed to different underlying causes. (A) Micro-offline and online changes relative to overall trial-by-trial learning. This figure is based on data from Bönstrup et al. (2019) 49. During early learning, micro-offline gains (red bars) closely track trial-by-trial performance gains (green line with open circle markers), with minimal contribution from micro-online gains (blue bars). The stated conclusion in Bönstrup et al. (2019) is that micro-offline gains only during this Early Learning stage reflect rapid memory consolidation (see also 54). After early learning, about practice trial 11, skill plateaus. This plateau skill period is characterized by a striking emergence of coupled (and relatively stable) micro-online drops and micro-offline increases. Bönstrup et al. (2019) as well as others in the literature 55-57, argue that micro-offline gains during the plateau period likely reflect recovery from inhibitory performance factors such as reactive inhibition or fatigue, and thus must be excluded from analyses relating micro-offline gains to skill learning.  The Non-repeating groups in Experiments 3 and 4 from Das et al. (2024) suffer from a lack of consideration of these known confounds.

Evidence documented in that paper54 showed that micro-offline gains during early skill learning were: 1) replicable and generalized to subjects learning the task in their daily living environment (n=389); 2) equivalent when significantly shortening practice period duration, thus confirming that they are not a result of recovery from performance fatigue (n=118);  3) reduced (along with learning rates) by retroactive interference applied immediately after each practice period relative to interference applied after passage of time (n=373), indicating stabilization of the motor memory at a microscale of several seconds consistent with rapid consolidation; and 4) not modified by random termination of the practice periods, ruling out a contribution of predictive motor slowing (N = 71) 54.  Altogether, our findings were strongly consistent with the interpretation that micro-offline gains reflect memory consolidation supporting early skill learning. This is precisely the portion of the learning curve Pan and Rickard51 refer to when they state “…rapid learning during that period masks any reactive inhibition effect”.

This interpretation is further supported by brain imaging evidence linking known memory-related networks and consolidation mechanisms to micro-offline gains. First, we reported that the density of fast hippocampo-neocortical skill memory replay events increases approximately three-fold during early learning inter-practice rest periods with the density explaining differences in the magnitude of micro-offline gains across subjects1. Second, Jacobacci et al. (2020) independently reproduced our original behavioral findings and reported BOLD fMRI changes in the hippocampus and precuneus (regions also identified in our MEG study1) linked to micro-offline gains during early skill learning. 33 These functional changes were coupled with rapid alterations in brain microstructure in the order of minutes, suggesting that the same network that operates during rest periods of early learning undergoes structural plasticity over several minutes following practice58. Third, even more recently, Chen et al. (2024) provided direct evidence from intracranial EEG in humans linking sharp-wave ripple events (which are known markers for neural replay59) in the hippocampus (80-120 Hz in humans) with micro-offline gains during early skill learning. The authors report that the strong increase in ripple rates tracked learning behavior, both across blocks and across participants. The authors conclude that hippocampal ripples during resting offline periods contribute to motor sequence learning. 2

Thus, there is actually now substantial evidence in the literature directly supporting the assertion “that micro-offline gains really result from offline learning”.  On the contrary, according to Gupta & Rickard (2024) “…the mechanism underlying RI [reactive inhibition] is not well established” after over 80 years of investigation60, possibly due to the fact that “reactive inhibition” is a categorical description of behavioral effects that likely result from several heterogenous processes with very different underlying mechanisms.

On the contrary, recent evidence questions this interpretation (Gupta & Rickard, npj Sci Learn 2022; Gupta & Rickard, Sci Rep 2024; Das et al., bioRxiv 2024). Instead, there is evidence that micro-offline gains are transient performance benefits that emerge when participants train with breaks, compared to participants who train without breaks, however, these benefits vanish within seconds after training if both groups of participants perform under comparable conditions (Das et al., bioRxiv 2024). 

It is important to point out that the recent work of Gupta & Rickard (2022,2024) 55 does not present any data that directly opposes our finding that early skill learning49 is expressed as micro-offline gains during rest breaks. These studies are essentially an extension of the Rickard et al (2008) paper that employed a massed (30s practice followed by 30s breaks) vs spaced (10s practice followed by 10s breaks) to assess if recovery from reactive inhibition effects could account for performance gains measured after several minutes or hours. Gupta & Rickard (2022) added two additional groups (30s practice/10s break and 10s practice/10s break as used in the work from our group). The primary aim of the study was to assess whether it was more likely that changes in performance when retested 5 minutes after skill training (consisting of 12 practice trials for the massed groups and 36 practice trials for the spaced groups) had ended reflected memory consolidation effects or recovery from reactive inhibition effects. The Gupta & Rickard (2024) follow-up paper employed a similar design with the primary difference being that participants performed a fixed number of sequences on each trial as opposed to trials lasting a fixed duration. This was done to facilitate the fitting of a quantitative statistical model to the data.  To reiterate, neither study included any analysis of micro-online or micro-offline gains and did not include any comparison focused on skill gains during early learning. Instead, Gupta & Rickard (2022), reported evidence for reactive inhibition effects for all groups over much longer training periods. Again, we reported the same finding for trials following the early learning period in our original Bönstrup et al. (2019) paper49 (Author response image 7). Also, please note that we reported in this paper that cumulative micro-offline gains over early learning did not correlate with overnight offline consolidation measured 24 hours later49 (see the Results section and further elaboration in the Discussion). Thus, while the composition of our data is supportive of a short-term memory consolidation process operating over several seconds during early learning, it likely differs from those involved over longer training times and offline periods, as assessed by Gupta & Rickard (2022).

In the recent preprint from Das et al (2024) 61,  the authors make the strong claim that “micro-offline gains during early learning do not reflect offline learning” which is not supported by their own data.   The authors hypothesize that if “micro-offline gains represent offline learning, participants should reach higher skill levels when training with breaks, compared to training without breaks”.  The study utilizes a spaced vs. massed practice group between-subjects design inspired by the reactive inhibition work from Rickard and others to test this hypothesis. Crucially, the design incorporates only a small fraction of the training used in other investigations to evaluate early skill learning1,33,49,54,57,58,62.  A direct comparison between the practice schedule designs for the spaced and massed groups in Das et al., and the training schedule all participants experienced in the original Bönstrup et al. (2019) paper highlights this issue as well as several others (Author response image 8):

Author response image 8.

(A) Comparison of Das et al. Spaced & Massed group training session designs, and the training session design from the original Bönstrup et al. (2019) 49 paper. Similar to the approach taken by Das et al., all practice is visualized as 10-second practice trials with a variable number (either 0, 1 or 30) of 10-second-long inter-practice rest intervals to allow for direct comparisons between designs. The two key takeaways from this comparison are that (1) the intervention differences (i.e. – practice schedules) between the Massed and Spaced groups from the Das et al. report are extremely small (less than 12% of the overall session schedule) and (2) the overall amount of practice is much less than compared to the design from the original Bönstrup report 49  (which has been utilized in several subsequent studies). (B) Group-level learning curve data from Bönstrup et al. (2019) 49 is used to estimate the performance range accounted for by the equivalent periods covering Test 1, Training 1 and Test 2 from Das et al (2024). Note that the intervention in the Das et al. study is limited to a period covering less than 50% of the overall learning range.

First, participants in the original Bönstrup et al. study 49 experienced 157.14% more practice time and 46.97% less inter-practice rest time than the Spaced group in the Das et al. study (Author response image 8).  Thus, the overall amount of practice and rest differ substantially between studies, with much more limited training occurring for participants in Das et al.  

Second, and perhaps most importantly, the actual intervention (i.e. – the difference in practice schedule between the Spaced and Massed groups) employed by Das et al. covers a very small fraction of the overall training session. Identical practice schedule segments for both the Spaced & Massed groups are indicated by the red shaded area in Author response image 8. Please note that these identical segments cover 94.84% of the Massed group training schedule and 88.01% of the Spaced group training schedule (since it has 60 seconds of additional rest). This means that the actual interventions cover less than 5% (for Massed) and 12% (for Spaced) of the total training session, which minimizes any chance of observing a difference between groups.

Also note that the very beginning of the practice schedule (during which Figure R9 shows substantial learning is known to occur) is labeled in the Das et al. study as Test 1.  Test 1 encompasses the first 20 seconds of practice (alternatively viewed as the first two 10-second-long practice trials with no inter-practice rest). This is immediately followed by the Training 1 intervention, which is composed of only three 10-second-long practice trials (with 10-second inter-practice rest for the Spaced group and no inter-practice rest for the Massed group). Author response image 8 also shows that since there is no inter-practice rest after the third Training practice trial for the Spaced group, this third trial (for both Training 1 and 2) is actually a part of an identical practice schedule segment shared by both groups (Massed and Spaced), reducing the magnitude of the intervention even further.

Moreover, we know from the original Bönstrup et al. (2019) paper49 that 46.57% of all overall group-level performance gains occurred between trials 2 and 5 for that study. Thus, Das et al. are limiting their designed intervention to a period covering less than half of the early learning range discussed in the literature, which again, minimizes any chance of observing an effect.

This issue is amplified even further at Training 2 since skill learning prior to the long 5-minute break is retained, further constraining the performance range over these three trials. A related issue pertains to the trials labeled as Test 1 (trials 1-2) and Test 2 (trials 6-7) by Das et al. Again, we know from the original Bönstrup et al. paper 49 that 18.06% and 14.43% (32.49% total) of all overall group-level performance gains occurred during trials corresponding to Das et al Test 1 and Test 2, respectively. In other words, Das et al averaged skill performance over 20 seconds of practice at two time-points where dramatic skill improvements occur. Pan & Rickard (1995) previously showed that such averaging is known to inject artefacts into analyses of performance gains.

Furthermore, the structure of the Test in Das et. al study appears to have an interference effect on the Spaced group performance after the training intervention.  This makes sense if you consider that the Spaced group is required to now perform the task in a Massed practice environment (i.e., two 10-second-long practice trials merged into one long trial), further blurring the true intervention effects. This effect is observable in Figure 1C,E of their pre-print. Specifically, while the Massed group continues to show an increase in performance during test relative to the last 10 seconds of practice during training, the Spaced group displays a marked decrease. This decrease is in stark contrast to the monotonic increases observed for both groups at all other time-points.

Interestingly, when statistical comparisons between the groups are made at the time-points when the intervention is present (as opposed to after it has been removed) then the stated hypothesis, “If micro-offline gains represent offline learning, participants should reach higher skill levels when training with breaks, compared to training without breaks”, is confirmed.

The data presented by Gupta and Rickard (2022, 2024) and Das et al. (2024) is in many ways more confirmatory of the constraints employed by our group and others with respect to experimental design, analysis and interpretation of study findings, rather than contradictory. Still, it does highlight a limitation of the current micro-online/offline framework, which was originally only intended to be applied to early skill learning over spaced practice schedules when reactive inhibition effects are minimized49. Extrapolation of this current framework to post-plateau performance periods, longer timespans, or non-learning situations (e.g. – the Non-repeating groups from Experiments 3 & 4 in Das et al. (2024)), when reactive inhibition plays a more substantive role, is not warranted. Ultimately, it will be important to develop new paradigms allowing one to independently estimate the different coincident or antagonistic features (e.g. - memory consolidation, planning, working memory and reactive inhibition) contributing to micro-online and micro-offline gains during and after early skill learning within a unifying framework.

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I agree that colors are a big factor for websites, just like they are for other things. For example, the color yellow is used for most road signs and school buses because it's one of the first colors that catches our attention. Warmer colors seem to have more energy, while cooler colors tend to relax. Lighter colors feel "lighter", while darker colors feel heavier. The way you color your website does just as much to set the theme as your content does.

1. Alignment
2. Negative Space
3. Fonts
4. Colors
5. UX vs UI: Usability

It's all about the eye and the visual aspect of the website building. You may be a great coder and developer and can create many crazy and fascinating functions, but if your website is too cluttered with buttons, its not going to be usable.

Thank you for submitting this paper. I think the paper requires substantial, major revisions to be published. Throughout the paper I noted many instances where references or examples would help make the intent clear. I also think the message of the paper would benefit from several figures to demonstrate workflows or ideas. The figures presented are essentially tables, and I think the message could be made clearer for the reader if they were presented as flow charts or at least with clear numbering to hook the ideas to the reader - e.g., Figures 1 & 2 would benefit from having numbers on the key ideas.

The paper is lacking many instances of citation, and at times reads as though it is an essay delivering an opinion. I'm not sure if this is the type of article that the journal would like, but two examples of sentences missing citations are:

1. "Over the last two decades, an unexpectedly large number of peer-reviewed findings across many scientific disciplines have been found to be irreproducible upon closer inspection." (Introduction, page 2)

2. "A large number of examples cited in this context involves faulty software or inappropriate use of software" (Introduction, page 3)

Two examples of sentences missing examples are:

1. Experimental software evolves at a much faster pace than mature software, and documentation is rarely up to date or complete (in Mature vs. experimental software, page 7). Could the author provide more examples of what "experimental software" is? There is also consistent use of universal terms like "...is rarely up to date or complete", which would be better phrased as "is often not up to date or complete"

2. There are various techniques for ensuring or verifying that a piece of software conforms to a formal specification.

Overall the paper introduces many new concepts, and I think it would greatly benefit from being made shorter and more concise, with adding some key figures for the reader to refer back to to understand these new ideas. The paper is well written, and it is clear the author is a great writer, and has put a lot of thought into the ideas. However it is my opinion that because these ideas are so big and require so much unpacking, they are also harder to understand. The reader would benefit from having more guidance to come back to understand these ideas.

I hope this review is helpful to the author.

Review comments

Introduction

Highlight [page 2]: Ever since the beginnings of organized science in the 17th century, researchers are expected to put all facts supporting their conclusions on the table, and allow their peers to inspect them for accuracy, pertinence, completeness, and bias. Since the 1950s, critical inspection has become an integral part of the publication process in the form of peer review, which is still widely regarded as a key criterion for trustworthy results.

• and Note [page 2]: Both of these statements feel like they should have some peer review, or reference on them, I believe. What was the beginnings of organised science in the 1600s? Why since the 1950s? Why not sooner? What happened then?

Highlight [page 2]: Over the last two decades, an unexpectedly large number of peer-reviewed findings across many scientific disciplines have been found to be irreproducible upon closer inspection.

• and Note [page 2]: I would expect at least a couple of citations here, e.g., Stodden et al., https://www.pnas.org/doi/abs/10.1073/pnas.1708290115

Highlight [page 2]: In the quantitative sciences, almost all of today’s research critically relies on computational techniques, even when they are not the primary tool for investigation - and Note [page 2]: Again, it does feel like it would be great to acknowledge research in this space.

Highlight [page 2]: But then, scientists mostly abandoned doubting.

• and Note [page 2]: This feels like an essay, where show me the evidence for where you can say something like this?

Highlight [page 2]: Automation bias

• and Note [page 2]: What is automation bias?

Highlight [page 3]: A large number of examples cited in this context involves faulty software or inappropriate use of software

• and Note [page 3]: Can you provide some examples of the examples cited that you are referring to here?

Highlight [page 3]: A particularly frequent issue is the inappropriate use of statistical inference techniques.

• and Note [page 3]: Please provide citations to these frequent issues.

Highlight [page 3]: The Open Science movement has made a first step towards dealing with automated reasoning in insisting on the necessity to publish scientific software, and ideally making the full development process transparent by the adoption of Open Source practices - and Note [page 3]: Could you provide an example of one of these Open Science movements?

Highlight [page 3]: Almost no scientific software is subjected to independent review today.

• and Note [page 3]: How can you justify this claim?

Highlight [page 3]: In fact, we do not even have established processes for performing such reviews

• and Note [page 3]: I disagree, there is the Journal of Open Source Software: https://joss.theoj.org/, rOpenSci has a guide for development of peer review of statistical software: https://github.com/ropensci/statistical-software-review-book, and also maintain a very clear process of software review: https://ropensci.org/software-review/

Highlight [page 3]: as I will show

• and Note [page 3]: How will you show this?

Highlight [page 3]: is as much a source of mistakes as defects in the software itself

• and Note [page 3]: Again, this feels like a statement of fact without evidence or citation.

Highlight [page 3]: This means that reviewing the use of scientific software requires particular attention to potential mismatches between the software’s behavior and its users’ expectations, in particular concerning edge cases and tacit assumptions made by the software developers. They are necessarily expressed somewhere in the software’s source code, but users are often not aware of them.

• and Note [page 3]: The same can be said of assumptions for equations and mathematics - the problem here is dealing with abstraction of complexity and the potential unintended consequences.

Highlight [page 4]: the preservation of epistemic diversity

• and Note [page 4]: Please define epistemic diversity

Reviewability of automated reasoning systems

Highlight [page 5]: The five dimensions of scientific software that influence its reviewability.

• and Note [page 5]: It might be clearer to number these in the figure, and also I might suggest changing the “convivial” - it’s a pretty unusual word?

Wide-spectrum vs. situated software

Highlight [page 6]: In between these extremes, we have in particular domain libraries and tools, which play a very important role in computational science, i.e. in studies where computational techniques are the principal means of investigation

• and Note [page 6]: I’m not very clear on this example - can you provide an example of a “domain library” or “domain tool” ?

Highlight [page 6]: Situated software is smaller and simpler, which makes it easier to understand and thus to review.

• and Note [page 6]: I’m not sure I agree it is always smaller and simpler - the custom code for a new method could be incredibly complicated.

Highlight [page 6]: Domain tools and libraries

• and Note [page 6]: Can you give an example of this?

Mature vs. experimental software

Highlight [page 7]: Experimental software evolves at a much faster pace than mature software, and documentation is rarely up to date or complete

• and Note [page 7]: Could the author provide more examples of what “experimental software” is? There is also consistent use of universal terms like “…is rarely up to date or complete”, which would be better phrased as “is often not up to date or complete”

Highlight [page 7]: An extreme case of experimental software is machine learning models that are constantly updated with new training data.

• and Note [page 7]: Such as…

Highlight [page 7]: interlocutor

• and Note [page 7]: suggest “middle man” or “mediator”, ‘interlocutor’ isn’t a very common word

Highlight [page 7]: A grey zone

• and Note [page 7]: I think it would be helpful to discuss black and white zones before this.

Highlight [page 7]: The libraries of the scientific Python ecosystem

• and Note [page 7]: Do you mean SciPy? https://scipy.org/. Can you provide an example of the frequent changes that break backward compatibility?

Highlight [page 7]: too late that some of their critical dependencies are not as mature as they seemed to be

• and Note [page 7]: Again, can you provide some evidence for this?

Highlight [page 7]: The main difference in practice is the widespread use of experimental software by unsuspecting scientists who believe it to be mature, whereas users of instrument prototypes are usually well aware of the experimental status of their equipment.

• and Note [page 7]: Again this feels like an assertion without evidence. Is this an essay, or a research paper?

Convivial vs. proprietary software

Highlight [page 8]: Convivial software [Kell 2020], named in reference to Ivan Illich’s book “Tools for conviviality” [Illich 1973], is software that aims at augmenting its users’ agency over their computation

• and Note [page 8]: It would be really helpful if the author would define the word, “convivial” here. It would also be very useful if they went on to give an example of what they meant by: “…software that aims at augmenting its users’ agency over their computation.” How does it augment the users agency?

Highlight [page 8]: Shaw recently proposed the less pejorative term vernacular developers [Shaw 2022]

• and Note [page 8]: Could you provide an example of what makes “vernacular developers” different, or just what they mean by this term?

Highlight [page 8]: which Illich has described in detail

• and Note [page 8]: Should this have a citation to Illich then in this sentence?

Highlight [page 8]: what has happened with computing technology for the general public

• and Note [page 8]: Can you give an example of this. Do you mean the rise of Apple and Windows? MS Word? Facebook? A couple of examples would be really useful to make this point clear.

Highlight [page 8]: tech corporations

• and Note [page 8]: Suggest “tech corporations” be “technology corporations”.

Highlight [page 8]: Some research communities have fallen into this trap as well, by adopting proprietary tools such as MATLAB as a foundation for their computational tools and models.

• and Note [page 8]: Can you provide an example of the alternative here, what would be the way to avoid this trap - use software such as Octave, or?

Highlight [page 8]: Historically, the Free Software movement was born in a universe of convivial technology.

• and Note [page 8]: If it is historic, can you please provide a reference to this?

Highlight [page 8]: most of the software they produced and used was placed in the public domain

• and Note [page 8]: Can you provide an example of this? I’m also curious how the software was placed in the public domain if there was no way to distribute it via the internet.

Highlight [page 8]: as they saw legal constraints as the main obstacle to preserving conviviality

• and Note [page 8]: Again, these are conjectures that are lacking a reference or example, can you provide some examples of references of this?

Highlight [page 9]: Software complexity has led to a creeping loss of user agency, to the point that even building and installing Open Source software from its source code is often no longer accessible to non-experts, making them dependent not only on the development communities, but also on packaging experts. An experience report on building the popular machine learning library PyTorch from source code nicely illustrates this point [Courtès 2021].

• and Note [page 9]: Can you summarise what makes it difficult to install Open Source Software? Again, this statement feels like it is making a strong generalisation without clear evidence to support this. The article by Courtès (https://hpc.guix.info/blog/2021/09/whats-in-a-package/), actually notes that it’s straightforward to install PyTorch via pip, but using an alternative package manager causes difficulty. The point you are making here seems to be that building and installing most open source software is almost prohibitive, but I think you’ve given strong evidence for this claim, and I don’t understand how this builds into your overall argument.

Highlight [page 9]: It survives mainly in communities whose technology has its roots in the 1980s, such as programming systems inheriting from Smalltalk (e.g. Squeak, Pharo, and Cuis), or the programmable text editor GNU Emacs.

• and Note [page 9]: Can you give an example of how it survives in these communities?

Highlight [page 9]: FLOSS has been rapidly gaining in popularity, and receives strong support from the Open Science movement

• and Note [page 9]: Can you provide some evidence to back this statement up?

Highlight [page 9]: the traditional values of scientific research.

• and Note [page 9]: Can you state what you mean by “traditional values of scientific research”

Highlight [page 9]: always been convivial

• and Note [page 9]: Can you provide a further explanation of what makes them convivial?

Transparent vs. opaque software

Highlight [page 9]: Transparent software

• and Note [page 9]: It might be useful to explain a distinction between transparent and open software - or to perhaps open with a statement for why we are talking about transparent and opaque software.

Highlight [page 9]: Large language models are an extreme example.

• and Note [page 9]: Based on your definition of transparent software - every action produces a visible result. If I type something into an LLM and get an immediate and visible result, how is this different? It is possible you are stating that the behaviour is able to be easily interpreted, or perhaps the behaviour is easy to understand?

Highlight [page 10]: Even highly interactive software, for example in data analysis, performs nonobvious computations, yielding output that an experienced user can perhaps judge for plausibility, but not for correctness.

• and Note [page 10]: Could you give a small example of this?

Highlight [page 10]: It is much easier to develop trust in transparent than in opaque software.

• and Note [page 10]: Can you state why it is easier to develop this trust?

Highlight [page 10]: but also less important

• and Note [page 10]: Can you state why it is less important?

Highlight [page 10]: even a very weak trustworthiness indicator such as popularity becomes sufficient

• and Note [page 10]: becomes sufficient for what? Reviewing? Why does it become sufficient?

Highlight [page 10]: This is currently a much discussed issue with machine learning models,

• and Note [page 10]: Given it is currently much discussed, could you link to at least 2 research articles discussing this point?

Highlight [page 10]: treated extensively in the philosophy of science.

• and Note [page 10]: Given that is has been treated extensively, can you please provide some key references after this statement? You do go on to cite one paper, but it would be helpful to mention at least a few key articles.

Size of the minimal execution environment

Highlight [page 11]: The importance of this execution environment is not sufficiently appreciated by most researchers today, who tend to consider it a technical detail

• and Note [page 11]: This statement is a bit of a sweeping generalisation - why is it not sufficiently appreciated? What evidence do you have of this?

Highlight [page 11]: Software environments have only recently been recognized as highly relevant for automated reasoning in science and beyond

• and Note [page 11]: Where have they been only recently recognised?

Highlight [page 11]: However, they have not yet found their way into mainstream computational science.

• and Note [page 11]: Could you provide an example of what it might look like if they were in mainstream computational science? For example, https://github.com/ropensci/rix implements using reproducible environments for R with NIX. What makes this not mainstream? Are you talking about mainstream in the sense of MS Excel? SPSS/SAS/STATA?

Analogies in experimental and theoretical science

Highlight [page 12]: Non-industrial components are occasionally made for special needs, but this is discouraged by their high manufacturing cost

• and Note [page 12]: Can you provide an example of this?

Highlight [page 12]: cables

• and Note [page 12]: What do you mean by a cable? As in a computer cable? An electricity cable?

Highlight [page 13]: which an experienced microscopist will recognize. Software with a small defect, on the other hand, can introduce unpredictable errors in both kind and magnitude, which neither a domain expert nor a professional programmer or computer scientist can diagnose easily.

• and Note [page 13]: I don’t think this is a fair comparison. Surely there must be instances of experiences microscopists not identifying defects? Similarly, why can’t there be examples of domain expert or professional programmer/computer scientist identifying errors. Don’t unit tests help protect us against some of our errors? Granted, they aren’t bullet proof, and perhaps act more like guard rails.

Highlight [page 13]: where “traditional” means not relying on any form of automated reasoning.

• and Note [page 13]: Can you give an example of what a “traditional” scientific model or theory

Improving the reviewability of automated reasoning systems

Highlight [page 14]: Figure 2: Four measures that can be taken to make scientific software more trustworthy.

• and Note [page 14]: Could the author perhaps instead call these “four measures” or perhaps give them a better name, and number them?

Review the reviewable

Highlight [page 14]: mature wide-spectrum software

• and Note [page 14]: Can you give an example of what “mature wide-spectrum software” is?

Highlight [page 15]: The main difficulty in achieving such audits is that none of today’s scientific institutions consider them part of their mission.

• and Note [page 15]: I disagree. Monash provides an example here where they view software as a first class research output: https://robjhyndman.com/files/EBS_research_software.pdf

Science vs. the software industry

Highlight [page 15]: Many computers, operating systems, and compilers were designed specifically for the needs of scientists.

• and Note [page 15]: Could you give an example of this? E.g., FORTRAN? COBAL?

Highlight [page 15]: Today, scientists use mostly commodity hardware

• and Note [page 15]: Can you explain what you mean by “commodity hardware”, and give an example.

Highlight [page 15]: even considered advantageous if it also creates a barrier to reverse- engineering of the software by competitors

• and Note [page 15]: Can you give an example of this?

Highlight [page 15]: few customers (e.g. banks, or medical equipment manufacturers) are willing to pay for

• and Note [page 15]: What about software like SPSS/STATA/SAS - surely many many industries, and also researchers will pay for software like this that is considered mature?

Emphasize situated and convivial software

Highlight [page 16]: a convivial collection of more situated modules, possibly supported by a shared wide-spectrum layer.

• and Note [page 16]: Could you give an example of what this might look like practically? Are you saying things like SciPy would be restructured into many separate modules, or?

Highlight [page 16]: In terms of FLOSS jargon, users make a partial fork of the project. Version control systems ensure provenance tracking and support the discovery of other forks. Keeping up to date with relevant forks of one’s software, and with the motivations for them, is part of everyday research work at the same level as keeping up to date with publications in one’s wider community. In fact, another way to describe this approach is full integration of scientific software development into established research practices, rather than keeping it a distinct activity governed by different rules.

• and Note [page 16]: Could the author provide a diagram or schematic to more clearly show how such a system would work with forks etc?

Highlight [page 17]: a universe is very

• and Note [page 17]: Perhaps this could be “would be very different” - since this doesn’t yet exist, right?

Highlight [page 17]: Improvement thus happens by small-step evolution rather than by large-scale design. While this may look strange to anyone used to today’s software development practices, it is very similar to how scientific models and theories have evolved in the pre-digital era.

• and Note [page 17]: I think some kind of schematic or workflow to compare existing practices to this new practice would be really useful to articulate these points. I also think this new method of development you are proposing should have a concrete name.

Highlight [page 17]: Existing code refactoring tools can probably be adapted to support application-specific forks, for example via code specialization. But tools for working with the forks, i.e. discovering, exploring, and comparing code from multiple forks, are so far lacking. The ideal toolbox should support both forking and merging, where merging refers to creating consensual code versions from multiple forks. Such maintenance by consensus would probably be much slower than maintenance performed by a coordinated team.

• and Note [page 17]: Perhaps an example of screenshot of a diff could be used to demonstrate that we can make these changes between two branches/commits, but comparing multiple is challenging?

Make scientific software explainable

Highlight [page 18]: An interesting line of research in software engineering is exploring possibilities to make complete software systems explainable [Nierstrasz and Girba 2022]. Although motivated by situated business applications, the basic ideas should be transferable to scientific computing

• and Note [page 18]: Is this similar to concepts such as “X-AI” or “X-ML” - that is, “Explainable” Artificial Intelligence or Machine Learning?

Highlight [page 18]: Unlike traditional notebooks, Glamorous Toolkit [feenk.com 2023],

• and Note [page 18]: It appears that you have introduced “Glamorous Toolkit” as an example of these three principles? It feels like it should be introduced earlier in this paragraph?

Highlight [page 18]: In Glamorous Toolkit, whenever you look at some code, you can access corresponding examples (and also other references to the code) with a few mouse clicks

• and Note [page 18]: I think it would be very beneficial to show screenshots of what the author means - while I can follow the link to Glamorous Toolkit, bitrot is a thing, and that might go away, so it would good to see exactly what the author means when they discuss these examples.

Use Digital Scientific Notations

Highlight [page 18]: There are various techniques for ensuring or verifying that a piece of software conforms to a formal specification

• and Note [page 18]: Can you give an example of these techniques?

Highlight [page 18]: The use of these tools is, for now, reserved to software that is critical for safety or security,

• and Note [page 18]: Again, could you give an example of this point? Which tools, and which software is critical for safety or security?

Highlight [page 19]: formal specifications

• and Note [page 19]: It would be really helpful if you could demonstrate an example of a formal specification so we can understand how they could be considered constraints.

Highlight [page 19]: All of them are much more elaborate than the specification of the result they produce. They are also rather opaque.

• and Note [page 19]: It isn’t clear to me how these are opaque - if the algorithm is defined, it can be understood, how is it opaque?

Highlight [page 19]: Moreover, specifications are usually more modular than algorithms, which also helps human readers to better understand what the software does [Hinsen 2023]

• and Note [page 19]: A tight example of this would be really useful to make this point clear. Perhaps with a figure of a specification alongside an algorithm.

Highlight [page 19]: In software engineering, specifications are written to formalize the expected behavior of the software before it is written. The software is considered correct if it conforms to the specification.

• and Note [page 19]: Is an example of this test drive development?

Highlight [page 19]: A formal specification has to evolve in the same way, and is best seen as the formalization of the scientific knowledge. Change can flow from specification to software, but also in the opposite direction.

• and Note [page 19]: Again, I think a good figure here would be very helpful in articulating this clearly.

Highlight [page 19]: My own experimental Digital Scientific Notation, Leibniz [Hinsen 2024], is intended to resemble traditional mathematical notation as used e.g. in physics. Its statements are embeddable into a narrative, such as a journal article, and it intentionally lacks typical programming language features such as scopes that do not exist in natural language, nor in mathematical notation.

• and Note [page 19]: Could we see an example of what this might look like?

Conclusion

Highlight [page 20]: Situated software is easy to recognize.

• and Note [page 20]: Could you provide some examples?

Highlight [page 20]: Examples from the reproducibility crisis support this view

• and Note [page 20]: Can you provide some example papers that you mention here?

Highlight [page 21]: The ideal structure for a reliable scientific software stack would thus consist of a foundation of mature software, on top of which a transparent layer of situated software, such as a script, a notebook, or a workflow, orchestrates the computations that together answer a specific scientific question. Both layers of such a stack are reviewable, as I have explained in section 3.1, but adequate reviewing processes remain to be enacted.

• and Note [page 21]: Again, I think it would be very insightful for the reader to have a clear figure to rest these ideas upon.

Highlight [page 21]: has been neglected by research institutions all around the world

• and Note [page 21]: I do not think this is true - could you instead say “neglected my most/many” perhaps?

Dear editors and reviewers, Thank you for your careful reading of my manuscript and the detailed and insightful feedback. It has contributed significantly to the improvements in the revised version. Please find my detailed responses below.

1 Reviewer 1

Thank you for this helpful review, and in particular for pointing out the need for more references, illustrations, and examples in various places of my manuscript. In the case of the section on experimental software, the search for examples made clear to me that the label was in fact badly chosen. I have relabeled the dimension as “stable vs. evolving software”, and rewritten the section almost entirely. Another major change motivated by your feedback is the addition of a figure showing the structure of a typical scientific software stack (Fig. 2), and of three case studies (section 2.7) in which I evaluate scientific software packages according to my five dimensions of reviewability. The discussion of conviviality (section 2.4), a concept that is indeed not widely known yet, has been much expanded. I have followed the advice to add references in many places. I have been more hesitant to follow the requests for additional examples and illustrations, because of the inevitable conflict with the equally understandable request to make the paper more compact. In many cases, I have preferred to refer to examples discussed in the literature. A few comments deserve a more detailed reply:

Introduction

Highlight [page 3]: In fact, we do not even have established processes for performing such reviews

and Note [page 3]: I disagree, there is the Journal of Open Source Software: https://joss.theoj.org/, rOpenSci has a guide for development of peer review of statistical software: https://github.com/ropensci/statistical software-review-book, and also maintain a very clear process of software review: https://ropensci.org/software-review/

As I say in the section “Review the reviewable”, these reviews are not independent critical examination of the software as I define it. Reviewers are not asked to evaluate the software’s correctness or appropriateness for any specific purpose. They are expected to comment only on formal characteristics of the software publication process (e.g. “is there a license?”), and on a few software engineering quality indicators (“is there a test suite?”).

Highlight [page 3]: This means that reviewing the use of scientific software requires particular attention to potential mismatches between the software’s behavior and its users’ expectations, in particular concerning edge cases and tacit assumptions made by the software developers. They are necessarily expressed somewhere in the software’s source code, but users are often not aware of them.

and Note [page 3]: The same can be said of assumptions for equations and mathematics- the problem here is dealing with abstraction of complexity and the potential unintended consequences.

Indeed. That’s why we need someone other than the authors to go through mathematical reasoning and verify it. Which we do.

Reviewability of automated reasoning systems

Wide-spectrum vs. situated software

Highlight [page 6]: Situated software is smaller and simpler, which makes it easier to understand and thus to review.

and Note [page 6]: I’m not sure I agree it is always smaller and simpler- the custom code for a new method could be incredibly complicated.

The comparison is between situated software and more generic software performing the same operation. For example, a script reading one specific CSV file compared to a subroutine reading arbitrary CSV files. I have yet to see a case in which abstraction from a concrete to a generic function makes code smaller or simpler.

Convivial vs. proprietary software

Highlight [page 8]: most of the software they produced and used was placed in the public domain

and Note [page 8]: Can you provide an example of this? I’m also curious how the software was placed in the public domain if there was no way to distribute it via the internet.

Software distribution in science was well organized long before the Internet, it was just slower and more expensive. Both decks of punched cards and magnetic tapes were routinely sent by mail. The earliest organized software distribution for science I am aware of was the DECUS Software Library in the early 1960s.

Size of the minimal execution environment

Note [page 11]: Could you provide an example of what it might look like if they were in mainstream computational science? For example, https://github.com/ropensci/rix implements using reproducible environments for R with NIX. What makes this not mainstream? Are you talking about mainstream in the sense of MS Excel? SPSS/SAS/STATA?

I have looked for quantitative studies on software use in science that would allow to give a precise meaning to “mainstream”, but I have not been able to find any. Based on my personal experience, mostly with teaching MOOCs on computational science in which students are asked about the software they use, the most widely used platform is Microsoft Windows. Linux is already a minority platform (though overrepresented in computer science), and Nix users are again a small minority among Linux users.

Analogies in experimental and theoretical science

Highlight [page 13]: which an experienced microscopist will recognize. Soft ware with a small defect, on the other hand, can introduce unpredictable errors in both kind and magnitude, which neither a domain expert nor a professional programmer or computer scientist can diag- nose easily.

and Note [page 13]: I don’t think this is a fair comparison. Surely there must be instances of experiences microscopists not identifying defects? Similarly, why can’t there be examples of domain expert or professional program mer/computer scientist identifying errors. Don’t unit tests help protect us against some of our errors? Granted, they aren’t bullet proof, and perhaps act more like guard rails.

There are probably cases of microscopists not noticing defects, but my point is that if you ask them to look for defects, they know what to do (and I have made this clearer in my text). For contrast, take GROMACS (one of my case studies in the revised manuscript) and ask either an expert programmer or an experienced computational biophysicist if it correctly implements, say, the AMBER force field. They wouldn’t know what to do to answer that question, both because it is ill-defined (there is no precise definition of the AMBER force field) and because the number of possible mistakes and symptoms of mistakes is enormous. I have seen a protein simulation program fail for proteins whose number of atoms was in a narrow interval, defined by the size that a compiler attributed to a specific data structure. I was able to catch and track down this failure only because a result was obviously wrong for my use case. I have never heard of similar issues with microscopes.

Improving the reviewability of automated reasoning systems

Review the reviewable

Highlight [page 15]: The main difficulty in achieving such audits is that none of today’s scientific institutions consider them part of their mission.

and Note [page 15]: I disagree. Monash provides an example here where they view software as a first class research output: https://robjhyndman.com/files/EBS_research_software.pdf

This example is about superficial reviews in the context of career evaluation. Other institutions have similar processes. As far as I know, none of them ask reviewers to look at the actual code and comment on its correctness or its suitability for some specific purpose.

Science vs. the software industry

Highlight [page 15]: few customers (e.g. banks, or medical equipment manufacturers) are willing to pay for

and Note [page 15]: What about software like SPSS/STATA/SAS- surely many many industries, and also researchers will pay for software like this that is considered mature?

I could indeed extend the list of examples to include various industries. Compared to the huge number of individuals using PCs and smartphones, that’s still few customers.

Emphasize situated and convivial software

Note [page 16]: Could the author provide a diagram or schematic to more clearly show how such a system would work with forks etc?

I have decided the contrary: I have significantly shortened this section, removing all speculation about how the ideas could be turned into concrete technology. The reason is that I have been working on this topic since I wrote the reviewed version of this manuscript, and I have a lot more to say about it than would be reasonable to include in this work. This will become a separate article.

Make scientific software explainable

Note [page 18]: I think it would be very beneficial to show screenshots of what the author means- while I can follow the link to Glamorous Toolkit, bitrot is a thing, and that might go away, so it would good to see exactly what the author means when they discuss these examples.

Unfortunately, static screenshots can only convey a limited impression of Glamorous Toolkit, but I agree that they have are a more stable support than the software itself. Rather than adding my own screenshots, I refer to a recent paper by the authors of Glamorous Toolkit that includes many screenshots for illustration.

Use Digital Scientific Notations

Highlight [page 19]: formal specifications and Note [page 19]: It would be really helpful if you could demonstrate an example of a formal specification so we can understand how they could be considered constraints.

Highlight [page 19]: Moreover, specifications are usually more modular than algorithms, which also helps human readers to better understand what the software does [Hinsen 2023]

and Note [page 19]: A tight example of this would be really useful to make this point clear. Perhaps with a figure of a specification alongside an algorithm.

I do give an example: sorting a list. To write down an actual formalized version, I’d have to introduce a formal specification language and explain it, which I think goes well beyond the scope of this article. Illustrating modularity requires an even larger example. This is, however, an interesting challenge which I’d be happy to take up in a future article.

Highlight [page 19]: In software engineering, specifications are written to formalize the expected behavior of the software before it is written. The software is considered correct if it conforms to the specification.

and Note [page 19]: Is an example of this test drive development?

Not exactly, though the underlying idea is similar: provide a condition that a result must satisfy as evidence for being correct. With testing, the condition is spelt out for one specific input. In a formal specification, the condition is written down for all possible inputs.

2 Reviewer 2

First of all, I would like to thank the reviewer for this thoughtful review. It addresses many points that require clarifications in the my article, which I hope to have done adequately in the revised version.

One such point is the role and form of reviewing processes for software. I have made it clearer that I take “review” to mean “critical independent inspection”. It could be performed by the user of a piece of software, but the standard case should be a review performed by experts at the request of some institution that then publishes the reviewer’s findings. There is no notion of gatekeeping attached to such reviews. Users are free to ignore them. Given that today, we publish and use scientific software without any review at all, the risk of shifting to the opposite extreme of having reviewers become gatekeepers seems unlikely to me.

Your comment on users being software developers addresses another important point that I had failed to make clear: conviviality is all about diminishing the distinction between developers and users. Users gain agency over their computations at the price of taking on more of a developer role. This is now stated explicitly in the revised article. Your hypothesis that I want scientific software to be convivial is only partially true. I want convivially structured software to be an option for scientists, with adequate infrastructure and tooling support, but I do not consider it to be the best approach for all scientific software.

The paragraph on the relevance and importance of reviewing in your comment is a valid point of view but, unsurprisingly, not mine. In the grand scheme of science, no specific quality assurance measure is strictly necessary. There is always another layer above that will catch mistakes that weren’t detected in the layer below. It is thus unlikely that unreliable software will cause all of science to crumble. But from many perspectives, including overall efficiency, personal satisfaction of practitioners, and insight derived from the process, it is preferable to catch mistakes as closely as possible to their source. Pre-digital theoreticians have always double-checked their manual calculations before submitting their papers, rather than sending off unchecked results and count on confrontation with experiment for finding mistakes. I believe that we should follow this same approach with software. The cost of mistakes can be quite high. Consider the story of the five retracted protein structures that I cite in my article (Miller, 2006, 10.1126/science.314.5807.1856). The five publications that were retracted involved years of work by researchers, reviewers, and editors. In between their publication and their retraction, other protein crystallographers saw their work rejected because it was in contradiction with the high-profile articles that later turned out to be wrong. The whole story has probably involved a few ruined careers in addition to its monetary cost. In contrast, independent critical examination of the software and the research processes in which it was used would likely have spotted the problem rather quickly (Matthews, 2007).

You point out that reviewability is also a criterion in choosing software to build on, and I agree. Building on other people’s software requires trusting it. Incorporating it into one’s own work (the core principle of convivial software) requires understanding it. This is in fact what motivated my reflections on this topic. I am not much interested in neatly separating epistemic and practical issues. I am a practitioner, my interest in epistemology comes from a desire for improving practices.

Review holism is something I have not thought about before. I consider it both impossible to apply in practice and of little practical value. What I am suggesting, and I hope to have made this clearer in my revision, is that reviewing must take into account the dependency graph. Reviewing software X requires a prior review of its dependencies (possibly already done by someone else), and a consideration of how each dependency influences the software under consideration. However, I do not consider Donoho’s “frictionless reproducibility” a sufficient basis for trust. It has the same problem as the widespread practice of tacitly assuming a piece of software to be correct because it is widely used. This reasoning is valid only if mistakes have a high chance of being noticed, and that’s in my experience not true for many kinds of research software. “It works”, when pronounced by a computational scientist, really means “There is no evidence that it doesn’t work”.

This is also why I point out the chaotic nature of computation. It is not about Humphreys’ “strange errors”, for which I have no solution to offer. It is about the fact that looking for mistakes requires some prior idea of what the symptoms of a mistake might be. Experienced researchers do have such prior ideas for scientific instruments, and also e.g. for numerical algorithms. They come from an understanding of the instruments and their use, including in particular a knowledge of how they can go wrong. But once your substrate is a Turing-complete language, no such understanding is possible any more. Every programmer has made the experience of chasing down some bug that at first sight seems impossible. My long-term hope is that scientific computing will move towards domain-specific languages that are explicitly not Turing-complete, and offer useful guarantees in exchange. Unfortunately, I am not aware of any research in this space.

I fully agree with you that internalist justifications are preferable to reliabilistic ones. But being fundamentally a pragmatist, I don’t care much about that distinction. Indisputable justification doesn’t really exist anywhere in science. I am fine with trust that has a solid basis, even if there remains a chance of failure. I’d already be happy if every researcher could answer the question “why do you trust your computational results?” in a way that shows signs of critical reflection.

What I care about ultimately is improving practices in computational science. Over the last 30 years, I have seen numerous mistakes being discovered by chance, often leading to abandoned research projects. Some of these mistakes were due to software bugs, but the most common cause was an incorrect mental model of what the software does. I believe that the best technique we have found so far to spot mistakes in science is critical independent inspection. That’s why I am hoping to see it applied more widely to computation.

2.1 References

Miller, G. (2006) A Scientist’s Nightmare: Software Problem Leads to Five Retractions. Science 314, 1856. https://doi.org/10.1126/science.314.5807.1856

Matthews, B.W. (2007) Five retracted structure reports: Inverted or incorrect? Protein Science 16, 1013. https://doi.org/10.1110/ps.072888607

3 Editor

Bayesian methods often use MCMC, which is often slow and creates long chains of estimates; however, the chains will show if the likelihood does not have a clear maximum, which is usually from a badly specified model...

That is an interesting observation I haven’t seen mentioned bedore. I agree that Bayesian inference is particularly amenable to inspection. One more reason to normalize inspection and inspectability in computational science.

Some reflection on the growing use of AI to write software may be worthwhile.

The use of AI in writing and reviewing software is a topic I have considered for this review, since the technology has evolved enormously since I wrote the current version of the manuscript. However, in view of reviewer 1’s constant admonition to back up statements with citations, I refrained from delving into this topic. We all know it’s happening, but it’s too early to observe a clear impact on research software. I have therefore limited myself to a short comment in the Conclusion section.

I wondered if highly-used software should get more scrutiny.

This is an interesting suggestion. If and when we get serious about reviewing code, resource allocation will become an important topic. For getting started, it’s probably more productive to review newly published code than heavily used code, because there is a better chance that authors actually act on the feedback and improve their code before it has many users. That in turn will help improve the reviewing process, which is what matters most right now, in my opinion.

“supercomputers are rare”, should this be “relatively rare” or am I speaking from a privileged university where I’ve always had access to supercomputers.

If you have easy access to supercomputer, you should indeed consider yourself privileged. But did you ever use supercomputer time for reviewing someone else’s work? I have relatively easy access to supercomputers as well, but I do have to make a re quest and promise to do innovative research with the allocated resources.

I did think about “testthat” at multiple points whilst reading the paper (https://testthat.r-lib.org/)

I hadn’t seen “testthat” before, not being much of a user of R. It looks interesting, and reminds me of similar test support features in Smalltalk which I found very helpful. Improving testing culture is definitely a valuable contribution to improving computational practices.

Can badges on github about downloads and maturity help (page 7)?

Badges can help, on GitHub or elsewhere, e.g. in scientific software catalogs. I see them as a coarse-grained output of reviewing. The right balance to find is between the visibility of a badge and the precision of a carefully written review report. One risk with badges is the temptation to automate the evaluation that leads to it. This is fine for quantitative measures such as test coverage, but what we mostly lack today is human expert judgement on software.

Author response:

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

Reviewer #1 (Public review):

Summary:

The paper presents a model for sequence generation in the zebra finch HVC, which adheres to cellular properties measured experimentally. However, the model is fine-tuned and exhibits limited robustness to noise inherent in the inhibitory interneurons within the HVC, as well as to fluctuations in connectivity between neurons. Although the proposed microcircuits are introduced as units for sub-syllabic segments (SSS), the backbone of the network remains a feedforward chain of HVC_RA neurons, similar to previous models.

Strengths:

The model incorporates all three of the major types of HVC neurons. The ion channels used and their kinetics are based on experimental measurements. The connection patterns of the neurons are also constrained by the experiments.

Weaknesses:

The model is described as consisting of micro-circuits corresponding to SSS. This presentation gives the impression that the model's structure is distinct from previous models, which connected HVC_RA neurons in feedforward chain networks (Jin et al 2007, Li & Greenside, 2006; Long et al 2010; Egger et al 2020). However, the authors implement single HVC_RA neurons into chain networks within each micro-circuit and then connect the end of the chain to the start of the chain in the subsequent micro-circuit. Thus, the HVC_RA neuron in their model forms a single-neuron chain. This structure is essentially a simplified version of earlier models.

In the model of the paper, the chain network drives the HVC_I and HVC_X neurons. The role of the micro-circuits is more significant in organizing the connections: specifically, from HVC_RA neurons to HVC_I neurons, and from HVC_I neurons to both HVC_X and HVC_RA neurons.

We thank Reviewer 1 for their thoughtful comments.

While the reviewer is correct about the fact that the propagation of sequential activity in this model is primarily carried by HVC_RA neurons in a feed-forward manner, we need to emphasize that this is true only if there is no intrinsic or synaptic perturbation to the HVC network. For example, we showed in Figures 10 and 12 how altering the intrinsic properties of HVC_X neurons or for interneurons disrupts sequence propagation. In other words, while HVC_RA neurons are the key forces to carry the chain forward, the interplay between excitation and inhibition in our network as well as the intrinsic parameters for all classes of HVC neurons are equally important forces in carrying the chain of activity forward. Thus, the stability of activity propagation necessary for song production depend on a finely balanced network of HVC neurons, with all classes contributing to the overall dynamics. Moreover, all existing models that describe premotor sequence generation in the HVC either assume a distributed model (Elmaleh et al., 2021) that dictates that local HVC circuitry is not sufficient to advance the sequence but rather depends upon moment to-moment feedback through Uva (Hamaguchi et al., 2016), or assume models that rely on intrinsic connections within HVC to propagate sequential activity. In the latter case, some models assume that HVC is composed of multiple discrete subnetworks that encode individual song elements (Glaze & Troyer, 2013; Long & Fee, 2008; Wang et al., 2008), but lacks the local connectivity to link the subnetworks, while other models assume that HVC may have sufficient information in its intrinsic connections to form a single continuous network sequence (Long et al. 2010). The HVC model we present extends the concept of a feedforward network by incorporating additional neuronal classes that influence the propagation of activity (interneurons and HVC_X neurons). We have shown that any disturbance of the intrinsic or synaptic conductances of these latter neurons will disrupt activity in the circuit even when HVC_RA neurons properties are maintained. 

In regard to the similarities between our model and earlier models, several aspects of our model distinguish it from prior work. In short, while several models of how sequence is generated within HVC have been proposed (Cannon et al., 2015; Drew & Abbott, 2003; Egger et al., 2020; Elmaleh et al., 2021; Galvis et al., 2018; Gibb et al., 2009a, 2009b; Hamaguchi et al., 2016; Jin, 2009; Long & Fee, 2008; Markowitz et al., 2015), all the models proposed either rely on intrinsic HVC circuitry to propagate sequential activity, rely on extrinsic feedback to advance the sequence or rely on both. These models do not capture the complex details of spike morphology, do not include the right ionic currents, do not incorporate all classes of HVC neurons, or do not generate realistic firing patterns as seen in vivo. Our model is the first biophysically realistic model that incorporates all classes of HVC neurons and their intrinsic properties. We tuned the intrinsic and the synaptic properties bases on the traces collected by Daou et al. (2013) and Mooney and Prather (2005) as shown in Figure 3. The three classes of model neurons incorporated to our network as well as the synaptic currents that connect them are based on Hodgkin- Huxley formalisms that contain ion channels and synaptic currents which had been pharmacologically identified. This is an advancement over prior models that primarily focused on the role of synaptic interactions or external inputs. The model is based on feedforward chain of microcircuits that encode for the different sub-syllabic segments and that interact with each other through structured feedback inhibition, defining an ordered sequence of cell firing. Moreover, while several models highlight the critical role of inhibitory interneurons in shaping the timing and propagation of bursts of activity in HVC_RA neurons, our work offers an intricate and comprehensive model that help understand this critical role played by inhibition in shaping song dynamics and ensuring sequence propagation.

How useful is this concept of micro-circuits? HVC neurons fire continuously even during the silent gaps. There are no SSS during these silent gaps.

Regarding the concern about the usefulness of the 'microcircuit' concept in our study, we appreciate the comment and we are glad to clarify its relevance in our network. While we acknowledge that HVC_RA neurons interconnect microcircuits, our model's dynamics are still best described within the framework of microcircuitry particularly due to the firing behavior of HVC_X neurons and interneurons. Here, we are referring to microcircuits in a more functional sense, rather than rigid, isolated spatial divisions (Cannon et al. 2015), and we now make this clear on page 21. A microcircuit in our model reflects the local rules that govern the interaction between all HVC neuron classes within the broader network, and that are essential for proper activity propagation. For example, HVC_INT neurons belonging to any microcircuit burst densely and at times other than the moments when the corresponding encoded SSS is being “sung”. What makes a particular interneuron belong to this microcircuit or the other is merely the fact that it cannot inhibit HVC_RA neurons that are housed in the microcircuit it belongs to. In particular, if HVC_INT inhibits HVC_RA in the same microcircuit, some of the HVC_RA bursts in the microcircuit might be silenced by the dense and strong HVC_INT inhibition breaking the chain of activity again. Similarly, HVC_X neurons were selected to be housed within microcircuits due to the following reason: if an HVC_X neuron belonging to microcircuit i sends excitatory input to an HVC_INT neuron in microcircuit j, and that interneuron happens to select an HVC_RA neuron from microcircuit i, then the propagation of sequential activity will halt, and we’ll be in a scenario similar to what was described earlier for HVC_INT neurons inhibiting HVC_RA neurons in the same microcircuit.

We agree that there are no sub-syllabic segments described during the silent gaps and we thank the reviewer to pointing this out. Although silent gaps are integral to the overall process of song production, we have not elaborated on them in this model due to the lack of a clear, biophysically grounded representation for the gaps themselves at the level of HVC. Our primary focus has been on modeling the active, syllable-producing phases of the song, where the HVC network’s sequential dynamics are critical for song. However, one can think the encoding of silent gaps via similar mechanisms that encode SSSs, where each gap is encoded by similar microcircuits comprised of the three classes of HVC neurons (let’s call them GAP rather than SSS) that are active only during the silent gaps. In this case, the propagation of sequential activity is carried throughout the GAPs from the last SSS of the previous syllable to the first SSS of the subsequent syllable. This is no described more clearly on page 22 of the manuscript.

A significant issue of the current model is that the HVC_RA to HVC_RA connections require fine-tuning, with the network functioning only within a narrow range of g_AMPA (Figure 2B). Similarly, the connections from HVC_I neurons to HVC_RA neurons also require fine-tuning. This sensitivity arises because the somatic properties of HVC_RA neurons are insufficient to produce the stereotypical bursts of spikes observed in recordings from singing birds, as demonstrated in previous studies (Jin et al 2007; Long et al 2010). In these previous works, to address this limitation, a dendritic spike mechanism was introduced to generate an intrinsic bursting capability, which is absent in the somatic compartment of HVC_RA neurons. This dendritic mechanism significantly enhances the robustness of the chain network, eliminating the need to fine-tune any synaptic conductances, including those from HVC_I neurons (Long et al 2010). Why is it important that the model should NOT be sensitive to the connection strengths?

We thank the reviewer for the comment. While mathematical models designed for highly complex nonlinear biological processes tangentially touch the biological realism, the current network as is right now is the first biologically realistic-enough network model designed for HVC that explains sequence propagation. We do not include dendritic processes in our network although that increases the realistic dynamics for various reasons. 1) The ion channels we integrated into the somatic compartment are known pharmacologically (Daou et al. 2013), but we don’t know about the dendritic compartment’s intrinsic properties of HVC neurons and the cocktail of ion channels that are expressed there. 2) We are able to generate realistic bursting in HVC_RA neurons despite the single compartment, and the main emphasis in this network is on the interactions between excitation and inhibition, the effects of ion channels in modulating sequence propagation, etc … 3) The network model already incorporates thousands of ODEs that govern the dynamics of each of the HVC neurons, so we did not want to add more complexity to the network especially that we don’t know the biophysical properties of the dendritic compartments.

Therefore, our present focus is on somatic dynamics and the interaction between HVC_RA and HVC_INT neurons, but we acknowledge the importance of these processes in enhancing network resiliency. Although we agree that adding dendritic processes improves robustness, we still think that somatic processes alone can offer insightful information on the sequential dynamics of the HVC network. While the network should be robust across a wide range of parameters, it is also essential that certain parameters are designed to filter out weaker signals, ensuring that only reliable, precise patterns of activity propagate. Hence, we specifically chose to make the HVC_RA-to-HVC_RA excitatory connections more sensitive (narrow range of values) such that only strong, precise and meaningful stimuli can propagate through the network representing the high stereotypy and precision seen in song production.

First, the firing of HVC_I neurons is highly noisy and unreliable. HVC_I neurons fire spontaneous, random spikes under baseline conditions. During singing, their spike timing is imprecise and can vary significantly from trial to trial, with spikes appearing or disappearing across different trials. As a result, their inputs to HVC_RA neurons are inherently noisy. If the model relies on precisely tuned inputs from HVC_I neurons, the natural fluctuations in HVC_I firing would render the model non-functional. The authors should incorporate noisy HVC_I neurons into their model to evaluate whether this noise would render the model non-functional.

We acknowledge that under baseline and singing settings, interneurons fire in an extremely noisy and inaccurate manner, although they exhibit time locked episodes in their activity (Hahnloser et al 2002, Kozhinikov and Fee 2007). In order to mimic the biological variability of these neurons, our model does, in fact, include a stochastic current to reflect the intrinsic noise and random variations in interneuron firing shown in vivo (and we highlight this in the Methods). However, to make sure the network is resilient to this randomness in interneuron firing, introduced a stochastic input current of the form I_noise (t)= σ.ξ(t) where ξ(t) is a Gaussian white noise with zero mean and unit variance, and σ is the noise amplitude. This stochastic drive was introduced to every model neuron and it mimics the fluctuations in synaptic input arising from random presynaptic activity and background noise. For values of σ within 1-5% of the mean synaptic conductance, the stochastic current has no effect on network propagation. For larger values of σ, the desired network activity was disrupted or halted. We now talk about this on page 22 of the manuscript.  

Second, Kosche et al. (2015) demonstrated that reducing inhibition by suppressing HVC_I neuron activity makes HVC_RA firing less sparse but does not compromise the temporal precision of the bursts. In this experiment, the local application of gabazine should have severely disrupted HVC_I activity. However, it did not affect the timing precision of HVC_RA neuron firing, emphasizing the robustness of the HVC timing circuit. This robustness is inconsistent with the predictions of the current model, which depends on finely tuned inputs and should, therefore, be vulnerable to such disruptions.

We thank the reviewer for the comment. The differences between the Kosche et al. (2015) findings and the predictions of our model arise from differences in the aspect of HVC function we are modeling. Our model is more sensitive to inhibition, which is a designed mechanism for achieving precise song patterning. This is a modeling simplification we adopted to capture specific characteristics of HVC function. Hence, Kosche et al. (2015) findings do not invalidate the approach of our model, but highlights that HVC likely operates with several, redundant mechanisms that overall ensure temporal precision. 

Third, the reliance on fine-tuning of HVC_RA connections becomes problematic if the model is scaled up to include groups of HVC_RA neurons forming a chain network, rather than the single HVC_RA neurons used in the current work. With groups of HVC_RA neurons, the summation of presynaptic inputs to each HVC_RA neuron would need to be precisely maintained for the model to function. However, experimental evidence shows that the HVC circuit remains functional despite perturbations, such as a few degrees of cooling, micro-lesions, or turnover of HVC_RA neurons. Such robustness cannot be accounted for by a model that depends on finely tuned connections, as seen in the current implementation.

Our model of individual HVC_RA neurons and as stated previously is reductive model that focuses on understanding the mechanisms that govern sequential neural activity. We agree that scaling the model to include many of HVC_RA neurons poses challenges, specifically concerning the summation of presynaptic inputs. However, our model can still be adapted to a larger network without requiring the level of fine-tuning currently needed. In fact, the current fine-tuning of synaptic connections in the model is a reflection of fundamental network mechanisms rather than a limitation when scaling to a larger network. Besides, one important feature of this neural network is redundancy. Even if some neurons or synaptic connections are impaired, other neurons or pathways can compensate for these changes, allowing the activity propagation to remain intact.

The authors examined how altering the channel properties of neurons affects the activity in their model. While this approach is valid, many of the observed effects may stem from the delicate balancing required in their model for proper function. In the current model, HVC_X neurons burst as a result of rebound activity driven by the I_H current. Rebound bursts mediated by the I_H current typically require a highly hyperpolarized membrane potential. However, this mechanism would fail if the reversal potential of inhibition is higher than the required level of hyperpolarization. Furthermore, Mooney (2000) demonstrated that depolarizing the membrane potential of HVC_X neurons did not prevent bursts of these neurons during forward playback of the bird's own song, suggesting that these bursts (at least under anesthesia, which may be a different state altogether) are not necessarily caused by rebound activity. This discrepancy should be addressed or considered in the model.

In our HVC network model, one goal with HVC_X neurons is to generate bursts in their underlying neuron population. Since HVC_X neurons in our model receive only inhibitory inputs from interneurons, we rely on inhibition followed by rebound bursts orchestrated by the I_H and the I_CaT currents to achieve this goal. The interplay between the T-type Ca⁺⁺ current and the H current in our model is fundamental to generate their corresponding bursts, as they are sufficient for producing the desired behavior in the network. Due to this interplay, we do not need significant inhibition to generate rebound bursts, because the T-type Ca₊₊ current’s conductance can be stronger leading to robust rebound bursting even when the degree of inhibition is not very strong. This is now highlighted on page 42 in the revised version.

Some figures contain direct copies of figures from published papers. It is perhaps a better practice to replace them with schematics if possible.

We wanted on purpose to keep the results shown in Mooney and Prather (2005) to be shown as is, in order to compare them with our model simulations highlighting the degree of resemblance. We believe that creating schematics of the Mooney and Prather (2005) results will not have the same impact, similarly creating a schematic for Hahnloser et al (2002) results won’t help much. However, if the reviewer still believes that we should do that, we’re happy to do it.

Reviewer #2 (Public review):

Summary:

In this paper, the authors use numerical simulations to try to understand better a major experimental discovery in songbird neuroscience from 2002 by Richard Hahnloser and collaborators. The 2002 paper found that a certain class of projection neurons in the premotor nucleus HVC of adult male zebra finch songbirds, the neurons that project to another premotor nucleus RA, fired sparsely (once per song motif) and precisely (to about 1 ms accuracy) during singing.

The experimental discovery is important to understand since it initially suggested that the sparsely firing RA-projecting neurons acted as a simple clock that was localized to HVC and that controlled all details of the temporal hierarchy of singing: notes, syllables, gaps, and motifs. Later experiments suggested that the initial interpretation might be incomplete: that the temporal structure of adult male zebra finch songs instead emerged in a more complicated and distributed way, still not well understood, from the interaction of HVC with multiple other nuclei, including auditory and brainstem areas. So at least two major questions remain unanswered more than two decades after the 2002 experiment: What is the neurobiological mechanism that produces the sparse precise bursting: is it a local circuit in HVC or is it some combination of external input to HVC and local circuitry? And how is the sparse precise bursting in HVC related to a songbird's vocalizations? The authors only investigate part of the first question, whether the mechanism for sparse precise bursts is local to HVC. They do so indirectly, by using conductance-based Hodgkin-Huxley-like equations to simulate the spiking dynamics of a simplified network that includes three known major classes of HVC neurons and such that all neurons within a class are assumed to be identical. A strength of the calculations is that the authors include known biophysically deduced details of the different conductances of the three major classes of HVC neurons, and they take into account what is known, based on sparse paired recordings in slices, about how the three classes connect to one another. One weakness of the paper is that the authors make arbitrary and not well-motivated assumptions about the network geometry, and they do not use the flexibility of their simulations to study how their results depend on their network assumptions. A second weakness is that they ignore many known experimental details such as projections into HVC from other nuclei, dendritic computations (the somas and dendrites are treated by the authors as point-like isopotential objects), the role of neuromodulators, and known heterogeneity of the interneurons. These weaknesses make it difficult for readers to know the relevance of the simulations for experiments and for advancing theoretical understanding.

Strengths:

The authors use conductance-based Hodgkin-Huxley-like equations to simulate spiking activity in a network of neurons intended to model more accurately songbird nucleus HVC of adult male zebra finches. Spiking models are much closer to experiments than models based on firing rates or on 2-state neurons.

The authors include information deduced from modeling experimental current-clamp data such as the types and properties of conductances. They also take into account how neurons in one class connect to neurons in other classes via excitatory or inhibitory synapses, based on sparse paired recordings in slices by other researchers. The authors obtain some new results of modest interest such as how changes in the maximum conductances of four key channels (e.g., A-type K+ currents or Ca-dependent K+ currents) influence the structure and propagation of bursts, while simultaneously being able to mimic accurately current-clamp voltage measurements.

Weaknesses:

One weakness of this paper is the lack of a clearly stated, interesting, and relevant scientific question to try to answer. In the introduction, the authors do not discuss adequately which questions recent experimental and theoretical work have failed to explain adequately, concerning HVC neural dynamics and its role in producing vocalizations. The authors do not discuss adequately why they chose the approach of their paper and how their results address some of these questions.

For example, the authors need to explain in more detail how their calculations relate to the works of Daou et al, J. Neurophys. 2013 (which already fitted spiking models to neuronal data and identified certain conductances), to Jin et al J. Comput. Neurosci. 2007 (which already discussed how to get bursts using some experimental details), and to the rather similar paper by E. Armstrong and H. Abarbanel, J. Neurophys 2016, which already postulated and studied sequences of microcircuits in HVC. This last paper is not even cited by the authors.

We thank the reviewer for this valuable comment, and we agree that we did not clarify enough throughout the paper the utility of our model or how it advanced our understanding of the HVC dynamics and circuitry. To that end, we revised several places of the manuscript and made sure to cite and highlight the relevance and relatedness of the mentioned papers.

In short, and as mentioned to Reviewer 1, while several models of how sequence is generated within HVC have been proposed (Cannon et al., 2015; Drew & Abbott, 2003; Egger et al., 2020; Elmaleh et al., 2021; Galvis et al., 2018; Gibb et al., 2009a, 2009b; Hamaguchi et al., 2016; Jin, 2009; Long & Fee, 2008; Markowitz et al., 2015; Jin et al., 2007), all the models proposed either rely on intrinsic HVC circuitry to propagate sequential activity, rely on extrinsic feedback to advance the sequence or rely on both. These models do not capture the complex details of spike morphology, do not include the right ionic currents, do not incorporate all classes of HVC neurons, or do not generate realistic firing patterns as seen in vivo. Our model is the first biophysically realistic model that incorporates all classes of HVC neurons and their intrinsic properties. 

No existing hypothesis had been challenged with our model, rather; our model is a distillation of the various models that’s been proposed for the HVC network. We go over this in detail in the Discussion. We believe that the network model we developed provide a step forward in describing the biophysics of HVC circuitry, and may throw a new light on certain dynamics in the mammalian brain, particularly the motor cortex and the hippocampus regions where precisely-timed sequential activity is crucial. We suggest that temporally-precise sequential activity may be a manifestation of neural networks comprised of chain of microcircuits, each containing pools of excitatory and inhibitory neurons, with local interplay among neurons of the same microcircuit and global interplays across the various microcircuits, and with structured inhibition as well as intrinsic properties synchronizing the neuronal pools and stabilizing timing within a firing sequence.

The authors' main achievement is to show that simulations of a certain simplified and idealized network of spiking neurons, which includes some experimental details but ignores many others, match some experimental results like current-clamp-derived voltage time series for the three classes of HVC neurons (although this was already reported in earlier work by Daou and collaborators in 2013), and simultaneously the robust propagation of bursts with properties similar to those observed in experiments. The authors also present results about how certain neuronal details and burst propagation change when certain key maximum conductances are varied. However, these are weak conclusions for two reasons. First, the authors did not do enough calculations to allow the reader to understand how many parameters were needed to obtain these fits and whether simpler circuits, say with fewer parameters and simpler network topology, could do just as well. Second, many previous researchers have demonstrated robust burst propagation in a variety of feed-forward models. So what is new and important about the authors' results compared to the previous computational papers?

A major novelty of our work is the incorporation of experimental data with detailed network models. While earlier works have established robust burst propagation, our model uses realistic ion channel kinetics and feedback inhibition not only to reproduce experimental neural activity patterns but also to suggest prospective mechanisms for song sequence production in the most biophysical way possible. This aspect that distinguishes our work from other feed-forward models. We go over this in detail in the Discussion. However, the reviewer is right regarding the details of the calculations conducted for the fits, we will make sure to highlight this in the Methods and throughout the manuscript with more details.

We believe that the network model we developed provide a step forward in describing the biophysics of HVC circuitry, and may throw a new light on certain dynamics in the mammalian brain, particularly the motor cortex and the hippocampus regions where precisely-timed sequential activity is crucial. We suggest that temporally-precise sequential activity may be a manifestation of neural networks comprised of chain of microcircuits, each containing pools of excitatory and inhibitory neurons, with local interplay among neurons of the same microcircuit and global interplays across the various microcircuits, and with structured inhibition as well as intrinsic properties synchronizing the neuronal pools and stabilizing timing within a firing sequence.

Also missing is a discussion, or at least an acknowledgment, of the fact that not all of the fine experimental details of undershoots, latencies, spike structure, spike accommodation, etc may be relevant for understanding vocalization. While it is nice to know that some models can match these experimental details and produce realistic bursts, that does not mean that all of these details are relevant for the function of producing precise vocalizations. Scientific insights in biology often require exploring which of the many observed details can be ignored and especially identifying the few that are essential for answering some questions. As one example, if HVC-X neurons are completely removed from the authors' model, does one still get robust and reasonable burst propagation of HVC-RA neurons? While part of the nucleus HVC acts as a premotor circuit that drives the nucleus RA, part of HVC is also related to learning. It is not clear that HVC-X neurons, which carry out some unknown calculation and transmit information to area X in a learning pathway, are relevant for burst production and propagation of HVCRA neurons, and so relevant for vocalization. Simulations provide a convenient and direct way to explore questions of this kind.

One key question to answer is whether the bursting of HVC-RA projection neurons is based on a mechanism local to HVC or is some combination of external driving (say from auditory nuclei) and local circuitry. The authors do not contribute to answering this question because they ignore external driving and assume that the mechanism is some kind of intrinsic feed-forward circuit, which they put in by hand in a rather arbitrary and poorly justified way, by assuming the existence of small microcircuits consisting of a few HVC-RA, HVC-X, and HVC-I neurons that somehow correspond to "sub-syllabic segments". To my knowledge, experiments do not suggest the existence of such microcircuits nor does theory suggest the need for such microcircuits. 

Recent results showed a tight correlation between the intrinsic properties of neurons and features of song (Daou and Margoliash 2020, Medina and Margoliash 2024), where adult birds that exhibit similar songs tend to have similar intrinsic properties. While this is relevant, we acknowledge that not all details may be necessary for every aspect of vocalization, and future models could simplify concentrate on core dynamics and exclude certain features while still providing insights into the primary mechanisms.

The question of whether HVC_X neurons are relevant for burst propagation given that our model includes these neurons as part of the network for completeness, the reviewer is correct, the propagation of sequential activity in this model is primarily carried by HVC_RA neurons in a feed-forward manner, but only if there is no perturbation to the HVC network. For example, we have shown how altering the intrinsic properties of HVC_X neurons or for interneurons disrupts sequence propagation. In other words, while HVC neurons are the key forces to carry the chain forward, the interplay between excitation and inhibition in our network as well as the intrinsic parameters for all classes of HVC neurons are equally important forces in carrying the chain of activity forward. Thus, the stability of activity propagation necessary for song production depend on a finely balanced network of HVC neurons, with all classes contributing to the overall dynamics.

We agree with the reviewer however that a potential drawback of our model is that its sole focus is on local excitatory connectivity within the HVC (Kornfeld et al., 2017; Long et al., 2010), while HVC neurons receive afferent excitatory connections (Akutagawa & Konishi, 2010; Nottebohm et al., 1982) that plays significant roles in their local dynamics. For example, the excitatory inputs that HVC neurons receive from Uvaeformis may be crucial in initiating (Andalman et al., 2011; Danish et al., 2017; Galvis et al., 2018) or sustaining (Hamaguchi et al., 2016) the sequential activity. While we acknowledge this limitation, our main contribution in this work is the biophysical insights onto how the patterning activity in HVC is largely shaped by the intrinsic properties of the individual neurons as well as the synaptic properties where excitation and inhibition play a major role in enabling neurons to generate their characteristic bursts during singing. This is true and holds irrespective of whether an external drive is injected onto the microcircuits or not. We elaborated on this further in the revised version in the Discussion.

Another weakness of this paper is an unsatisfactory discussion of how the model was obtained, validated, and simulated. The authors should state as clearly as possible, in one location such as an appendix, what is the total number of independent parameters for the entire network and how parameter values were deduced from data or assigned by hand. With enough parameters and variables, many details can be fit arbitrarily accurately so researchers have to be careful to avoid overfitting. If parameter values were obtained by fitting to data, the authors should state clearly what the fitting algorithm was (some iterative nonlinear method, whose results can depend on the initial choice of parameters), what the error function used for fitting (sum of least squares?) was, and what data were used for the fitting.

The authors should also state clearly the dynamical state of the network, the vector of quantities that evolve over time. (What is the dimension of that vector, which is also the number of ordinary differential equations that have to be integrated?) The authors do not mention what initial state was used to start the numerical integrations, whether transient dynamics were observed and what were their properties, or how the results depended on the choice of the initial state. The authors do not discuss how they determined that their model was programmed correctly (it is difficult to avoid typing errors when writing several pages or more of a code in any language) or how they determined the accuracy of the numerical integration method beyond fitting to experimental data, say by varying the time step size over some range or by comparing two different integration algorithms.

We thank the reviewer again. The fitting process in our model occurred only at the first stage where the synaptic parameters were fit to the Mooney and Prather as well as the Kosche results. There was no data shared and we merely looked at the figures in those papers and checked the amplitude of the elicited currents, the magnitudes of DC-evoked excitations etc … and we replicated that in our model. While this is suboptimal, it was better for us to start with it rather than simply using equations for synaptic currents from the literature for other types of neurons (that are not even HVC’s or in the songbird) and integrate them into our network model. The number of ODEs that govern the dynamics of every model neuron is listed on page 10 of the manuscript as well as in the Appendix.  Moreover, we highlighted the details of this fitting process in the revised version.

Also disappointing is that the authors do not make any predictions to test, except rather weak ones such as that varying a maximum conductance sufficiently (which might be possible by using dynamic clamps) might cause burst propagation to stop or change its properties. Based on their results, the authors do not make suggestions for further experiments or calculations, but they should.

We agree that making experimental testable predictions is crucial for the advancement of the model. Our predictions include testing whether eradication of a class of neurons such as HVC_X neurons disrupts activity propagation which can be done through targeted neuron elimination. This also can be done through preventing rebound bursting in HVC_X by pharmacologically blocking the I_H channels. Others include down regulation of certain ion channels (pharmacologically done through ion blockers) and testing which current is fundamental for song production (and there a plenty of test based our results, like the SK current, the T-type Ca²⁺ current, the A-type K⁺ current, etc…). We incorporated these into the Discussion of the revised manuscript to better demonstrate the model's applicability and to guide future research directions.

Main issues:

(1) Parameters are overly fine-tuned and often do not match known biology to generate chains. This fine-tuning does not reveal fundamental insights.

(1a) Specific conductances (e.g. AMPA) are finely tweaked to generate bursts, in part due to a lack of a dendritic mechanism for burst generation. A dendritic mechanism likely reflects the true biology of HVC neurons.

We acknowledge that the model does not include active dendritic processes and we do not regard this as a limitation. In fact, our present approach, although simplified, is intended to focus on somatic mechanisms to identify minimal conditions required for stable sequential propagation. We know HVC_RA neurons possess thin, spiny dendrites which can contribute to burst initiation and shaping. Future models that include such nonlinear dendritic mechanisms would likely reduce the need for fine tuning of specific conductances at the soma and consequently better match the known biology of HVC_RA neurons. 

In text: “While our simplified, somatically driven architecture enables better exploration of mechanisms for sequence propagation, future extensions of the model will incorporate dendritic compartments to more accurately reflect the intrinsic bursting mechanisms observed in HVC_RA neurons.”

(1b) In this paper, microcircuits are simulated and then concatenated to make the HVC chain, resulting in no representations during silent gaps. This is out of touch with the known HVC function. There is no anatomical nor functional evidence for microcircuits of the kind discussed in this paper or in the earlier and rather similar paper by Eve Armstrong and Henry Abarbanel (J. Neurophy 2016). One can write a large number of papers in which one makes arbitrary unconstrained guesses of network structure in HVC and, unless they reveal some novel principle or surprising detail, they are all going to be weak.

Although the model is composed of sequentially activated microcircuits, the gaps between each microcircuit’s output do not represent complete silence in the network. During these periods, other neurons such as those in other microcircuits may still exhibit bursting activity. Thus, what may appear as a 'silent gap' from the perspective of a given output microcircuit is, in fact, part of the ongoing background dynamics of the larger HVC neuron network. We fully acknowledge the reviewer's point that there is no direct anatomical or physiological evidence supporting the presence of microcircuits with this structure in HVC. Our intention was not to propose the existence of such a physical model but to use it as a computational simplification to make precise sequential bursting activity feasible given the biologically realistic neuronal dynamics used. Hence, our use of 'microcircuits' refers to a modeling construct rather than a structural hypothesis. Even if the network topology is hypothetical, we still believe that the temporal structuring suggested allows us to generate specific predictions for future work about burst timing and neuronal connections.

(1c) HVC interneuron discharge in the author's model is overly precise; addressing the observation that these neurons can exhibit noisy discharge. Real HVC interneurons are noisy. This issue is critical: All reviewers strongly recommend that the authors should, at the minimum in a revision, focus on incorporating HVC-I noise in their model.

We agree that capturing the variability in interneuron bursting is critical for biological realism. In our model, HVC interneurons receive stochastic background current that introduces variability in their firing patterns as observed in vivo. This variability is seen in our simulations and produces more biologically realistic dynamics while maintaining sequence propagation. We clarify this implementation in the Methods section. 

(1d) Address the finding that Kosche et al show that even with reduced inhibition, HVCra neuronal timing is preserved; it is the burst pattern that is affected.

The differences between the Kosche et al. (2015) findings and the predictions of our model arise from differences in the aspect of HVC function we are modeling. Our model is more sensitive to inhibition, which is a designed mechanism for achieving precise song patterning. This is a modeling simplification we adopted to capture specific characteristics of HVC function. 

We acknowledged this point in the discussion: “While findings of Kosche et al. (2015) emphasize the robustness of the HVC timing circuit to inhibition, our model is more sensitive to inhibition, highlighting that HVC likely operates with several, redundant mechanisms that overall ensure temporal precision.”

(1e) The real HVC is robust to microlesions, cooling, and HVCra neuron turnover. The model in this paper relies on precise HVCra connectivity and is not robust.

Although our model is grounded in the biologically observed behavior of HVC neurons in vivo, we don’t claim that it fully captures the resilience seen in the HVC network. Instead, we see this as a simplified framework that helps us explore the basic principles of sequential activity. In the future, adding features like recurrent excitation, synaptic plasticity, or homeostatic mechanisms could make the model more robust.

(1f) There is unclear motivation for Ih-driven HVCx bursting, given past findings from the Mooney group.

Daou et al (2013) noticed that the observed in HVC_X and HVC_INT neurons in response to hyperpolarizing current pulses (Dutar et al. 1998; Kubota and Saito 1991; Kubota and Taniguchi 1998) was completely abolished after the application of the drug ZD 7288 in all of the neurons tested indicating that the sag in these HVC neurons is due to the hyperpolarization-activated inward current (I_h). in addition, the sag and the rebound seen in these two neuron groups were larger as for larger hyperpolarization current pulses.

(1g) The initial conditions of the network and its activity under those conditions, as well as the possible reliance on external inputs, are not defined.

In our model, network activity is initiated through a brief, stochastic excitatory input to a small HVC_RA neuron of one microcircuit. This drive represents a simplified version of external input from upstream brain regions known to project to HVC, such as nuclei in the high vocal center's auditory pathways such as Nif and Uva. Modeling the activity of these upstream regions and their influence on HVC dynamics is an ongoing research work to be published in the future.

(1h) It has been known from the time of Hodgkin and Huxley how to include temperature dependences for neuronal dynamics so another suggestion is for the authors to add such dependences for the three classes of neurons and see if their simulation causes burst frequencies to speed up or slow down as T is varied.

We added this as limitation to the discussion section: “Our model was run at a fixed physiological temperature, but it's well known going all the way back to Hodgkin and Huxley that both ion channel activity and synaptic dynamics can change with temperature. In future work, adding temperature scaling (like Q10 factors) could help us explore how burst timing and sequence speed change with temperature changes, and how neural activity in HVC would/would not preserve its precision under different physiological conditions.”

(2) The scope of the paper and its objectives must be clearly defined. Defining the scope and providing caveats for what is not considered will help the reader contextualize this study with other work.

(2a) The paper does not consider the role of external inputs to HVC, which are very likely important for the capacity of the HVC chain to tile the entire song, including silent gaps.

The role of afferent input to HVC particularly from nuclei such as Uva and Nif is critical in shaping the timing and initiation of HVC sequences throughout the song, including silent intervals. In fact, external inputs are likely involved in more than just triggering sequences, they may also influence the continuity of activity across motifs. However, in this study, we chose to focus on the intrinsic dynamics of HVC as a step toward understanding the internal mechanisms required for generating temporally precise sequences and for this reason, we used a simplified external input only to initiate activity in the chain.

(2b) The paper does not consider important dendritic mechanisms that almost certainly facilitate the all-or-none bursting behavior of HVC projection neurons. the authors need to mention and discuss that current-clamped neuronal response - in which an electrode is inserted into the soma and then a constant current-step is applied - bypasses dendritic structure and dendritic processing and so is an incomplete way to characterize a neuron's properties. In particular, claiming to fit current-clamp data accurately and then claiming that one now has a biophysically accurate network model, as the authors do, is greatly misleading.

While we addressed this is 1a, we do not suggest that our model is a fully accurate biophysical representation of HVC network. Instead, we see it as a simplified framework that helps reveal how much of HVC’s sequential activity can be explained by somatic properties and synaptic interactions alone. However, additional biological mechanisms, like dendritic processing, are likely to play an important role and should be explored in future work.

(2c) The introduction does not provide a clear motivation for the paper - what hypotheses are being tested? What is at stake in the model outcomes? It is not inherently informative to take a known biological representation and fine-tune a limited model to replicate that representation.

We explicitly added the hypotheses to the revised introduction.

(2d) There have been several published modeling efforts applied to the HVC chain (Seung, Fee, Long, Greenside, Jin, Margoliash, Abarbanel). These and others need to be introduced adequately, and it needs to be crystal clear what, if anything, the present study is adding to the canon.

While several influential models have explored how HVC might generate sequences ranging from synfire chains to recurrent dynamics or externally driven sequences (e.g., Seung, Fee, Long, Greenside, Jin, Abarbanel, and others), these models could not capture the detailed dynamics observed in vivo. Our aim was to bridge a gap in the modeling literature by exploring how far biophysically grounded intrinsic properties and experimentally supported synaptic connections that are local to the HVC can alone produce temporally precise sequences. We have proven that these mechanisms are sufficient to generate these sequences, although some missing components (such as dendritic mechanisms or external inputs) might be needed to fully capture the complexity and robustness of HVC function.

(2e) The authors mention learning prominently in the abstract, summary, and introduction but this paper has nothing to do with learning. Most or all mentions of learning should be deleted since they are misleading.

We appreciate the reviewer’s observation however our intent by referencing learning was not to suggest that our model directly simulates learning processes, but rather to place HVC function within the broader context of song learning and production, where temporal sequencing plays a fundamental role. Yet, repeated references to learning may be misleading given that our current model does not incorporate plasticity, synaptic modification, or developmental changes. Hence, we have carefully revised the manuscript to rephrase mentions of learning unless directly relevant to context. 

(3) Using the model for hypothesis generation and prediction of experimental results.

(3a) The utility of a model is to provide conceptual insight into how or why the real HVC functions as it does, or to predict outcomes in yet-to-be conducted experiments to help motivate future studies. This paper does not adequately achieve these goals.

We revised the Discussion of the manuscript to better emphasize potential contributions and point out many experiments that could validate or challenge the model’s predictions. These include dynamic clamp or ion channel blockers targeting A-type K⁺ in HVC_RA neurons to assess their impact on burst precision, optogenetic disruption of inhibitory interneurons to observe changes in burst timing and sequence propagation, pharmacological modulation of I_h or I_CaT in HVC_X and interneurons etc. 

(3b) Additionally, it can be interesting to conduct an experiment on an existing model; for example, what happens to the HVCra chain in your model if you delete the HVCx neurons? What happens if you block NMDA receptors? Such an approach in a modeling paper can help motivate hypotheses and endow the paper with a sense of purpose.

We agree that running targeted experiments to test our computational model such as removing an HVC neuron population or blocking a synaptic receptor can be a powerful way to generate new ideas and guide future experiments. While we didn’t include these specific tests in the current study, the model is well suited for this kind of exploration. For instance, removing interneurons could help us better understand their role in shaping the timing of HVC_RA bursts. These are great directions for future experiments, and we now highlight this in the discussion as a way the model could be used to guide experiments.

(4) Changes to the paper's organization may improve clarity.

(4a) Nearly all equations should be moved to an Appendix so that the main part of the paper can focus on the science: assumptions made, details of simulations, conclusions obtained, and their significance. The authors present many equations without discussion which weakens the paper.

Equations moved to appendix.

(4b) There are many grammatical errors, e.g., verbs do not match the subject in terms of being single or plural. The authors need to run their manuscript through a grammar checker.

Done.

(4c) Many of the figures are poorly designed and should be substantially modified. E.g. in Figure 1B, too many colors are used, making it hard to grasp what is being plotted and the colors are not needed. Figures 1C and 1D are entire figures taken from other papers, and there is no way a reader will be able to see or appreciate all the details when this figure is published on a single page. Figure 2 uses colors for dots that are almost identical, and the colors could be avoided by using different symbols. Figure 5 fills an entire page but most of the figure conveys no information, there is no need to show the same details for all 120 neurons, just show the top 1/3 of this figure; the same for Figure 7, a lot of unnecessary information is being included. Figure 10, the bottom time series of spikes should be replaced with a time series of rates, cannot extract useful information.

Adjusted as requested. 

(4d) Table 1 is long and largely uninteresting, and should be moved to an appendix.

Table 1 moved to appendix.

(4e) Many sentences are not carefully written, which greatly weakens the paper. As one typical example, the first sentence in the Discussion section "In this study, we have designed a neural network model that describes [sic] zebra finch song production in the HVC." This is inaccurate, the model does not describe song production, it just explores some properties of one nucleus involved with song production. Just one or few sentences like this is ok but there are so many sentences of this kind that the reader loses faith in the authors.

Thank you for raising this point, we revised the manuscript to improve the precision of the writing. We replaced the first sentence of the discussion with this: "In this study, we developed a biophysically realistic neural network model to explore how intrinsic neuronal properties and local connectivity within the songbird nucleus HVC may support the generation of temporally precise activity sequences associated with zebra finch song."

This is second important part. In which cases this aliasing resolution is required? "Overlapping" is just one example but not all.

Example one: Suppose that MSTORE is going to store a DataPt "X" (32 bytes) in the memory at offset 0x03. After some time has passed, MLOAD is loading a 32-byte memory value at offset 0x00 to the stack. Say this "Y". Suppose there have been no "overlapping" during the meantime. Do you think the returned stack value "Y" is still the same as "X" even if there was no overlapping?

Example 2: In general, Calldata can be much longer than 32 bytes. So whenever EVM is going to load specific function input argument "Y" onto the stack, it chunks the Calldata.

It's quite tricky for a Synthesizer to shadow this, since DataPts cannot deal with words greater than 32 bytes! The current version of the Synthesizer avoids solving this problem: it simply takes the resulted chunk made by the EVM as an Oracle. The next version, currently in development, will fundamentally solve this: it will create another virtual MemoryPt dedicated to CallData and store DataPts for the function selector and function arguments there—this process is the reverse of resolving aliasing.

Please see this code for dealing with "CALLDATALOAD".

There are a lot of experiments and studies that require other people. The idea of morals and ethnics is something that should be discussed and solidified before doing anything at all.

I feel like this idea is brought up in a lot of conversations but people don't actually know how big of a problem this is. We miss out on important perspectives that couldn't have been found otherwise.

I have never read this article with my teaching group but can already tell this will help us with a plethora of useful information to help us in this teaching journey. At the pre-K age, self-control is really non-existent, especially if the basis for those skills aren't being enforced at home. It's a challenge at this age because they are VERY cute, and I'm just the teacher, so I can image the challenge of establishing boundaries and teaching self-control at home is a large one.

This is definitely something I have referenced in my career, that almost all disruptive or behavioral issues are always developmentally appropriate for children. I do wonder if there is a specific line on when it may pass into inappropriate and how to handle that in the best way. My co-workers and I never take anything personally and always use our experience and knowledge to understand that children are just children and are being developmentally appropriate for their age, probably 99 percent of the time. It's surprising to me that there is any situation that a child's behavior may be considered developmentally inappropriate as I can't say I have had to experience that first hand.

I could just read the article but I'll do that later. but basically, I've always been confused on when hackers release the passwords of a bunch or users of a website or similar. Not so much how they do it (I still don't know how) but more so how they share that information. Like, do they just share the passwords without it's respected user? In that case it wouldn't be absolutely terrible since you still wouldn't know which password is for what account, but a smart hacker to maybe use a bot to try each of the 153 million passwords on one account (would still take ages, but at least you have a finite number of passwords to try). Or, do hackers put up all the password along with the users in a massive spreadsheet? That would make sense, you can just look up an account to hack and hack it easily. But do they share this on public platforms like Reddit? Do they share it directly with each other? Do they post it on some sort of evil dark web place? I'll find out I guess.

Author response:

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

Reviewer #1 (Public review):

Summary:

The manuscript "Lifestyles shape genome size and gene content in fungal pathogens" by Fijarczyk et al. presents a comprehensive analysis of a large dataset of fungal genomes to investigate what genomic features correlate with pathogenicity and insect associations. The authors focus on a single class of fungi, due to the diversity of lifestyles and availability of genomes. They analyze a set of 12 genomic features for correlations with either pathogenicity or insect association and find that, contrary to previous assertions, repeat content does not associate with pathogenicity. They discover that the number of proteincoding genes, including the total size of non-repetitive DNA does correlate with pathogenicity. However, unique features are associated with insect associations. This work represents an important contribution to the attempts to understand what features of genomic architecture impact the evolution of pathogenicity in fungi.

Strengths:

The statistical methods appear to be properly employed and analyses thoroughly conducted. The manuscript is well written and the information, while dense, is generally presented in a clear manner.

Weaknesses:

My main concerns all involve the genomic data, how they were annotated, and the biases this could impart to the downstream analyses. The three main features I'm concerned with are sequencing technology, gene annotation, and repeat annotation.

We thank the reviewer for all the comments. We are aware that the genome assemblies are of heterogeneous quality since they come from many sources. The goal of this study was to make the best use of the existing assemblies, with the assumption that noise introduced by the heterogeneity of sequencing methods should be overcome by the robustness of evolutionary trends and the breadth and number of analyzed assemblies. Therefore, at worst, we would expect a decrease in the power to detect existing trends. It is important to note that the only way to confidently remove all potential biases would be to sequence and analyze all species in the same way; this would require a complete study and is beyond the scope of the work presented here. Nevertheless some biases could affect the results in a negative way, eg. is if they affect fungal lifestyles differently. We therefore made an attempt to explore the impact of sequencing technology, gene and repeat annotation approach among genomes of different fungal lifestyles. Details are described in Supplementary Results and below. Overall, even though the assembly size and annotations conducted with Augustus can sometimes vary compared to annotations from other resources, such as JGI Mycocosm, we do not observe a bias associated with fungal lifestyles. Comparison of annotations conducted with Augustus and JGI Mycocosm dataset revealed variation in gene-related features that reflect biological differences rather than issues with annotation.  

The collection of genomes is diverse and includes assemblies generated from multiple sequencing technologies including both short- and long-read technologies. Not only has the impact of the sequencing method not been evaluated, but the technology is not even listed in Table S1. From the number of scaffolds it is clear that the quality of the assemblies varies dramatically. This is going to impact many of the values important for this study, including genome size, repeat content, and gene number.

We have now added sequencing technology in Table S1 as it was reported in NCBI. We evaluated the impact of long-read (Nanopore, PacBio, Sanger) vs short-read assemblies in Supplementary Results. In short, the proportion of different lifestyles (pathogenic vs. nonpathogenic, IA vs non-IA) were the same for short- and long-read assemblies. Indeed, longread assemblies were longer, had a higher fraction of repeats and less genes on average, but the differences between pathogenic vs. non-pathogenic (or IA vs non-IA) species were in the same direction for two sequencing technologies and in line with our results. There were some discrepancies, eg. mean intron length was longer for pathogens with long-read assemblies, but slightly shorter on average for short-read assemblies (and to lesser extent GC and pseudo tRNA count), which could explain weaker or mixed results in our study for these features.

Additionally, since some filtering was employed for small contigs, this could also bias the results.

The reason behind setting the lower contig length threshold was the fact that assemblies submitted to NCBI have varying lower-length thresholds. This is because assemblers do not output contigs above a certain length, and this threshold can be manipulated by the user. Setting a common min contig length was meant to remove this variation, knowing that any length cut-off will have a larger effect on short-read based assemblies than long-read-based assemblies. Notably, genome assemblies of corresponding species in JGI Mycocosm have a minimum contig length of 865 bp, not much lower than in our dataset. Importantly, in a response to a comment of previous reviewer, repeat content was recalculated on raw assembly lengths instead of on filtered assembly length. 

I have considerable worries that the gene annotation methods could impart biases that significantly affect the main conclusions. Only 5 reference training sets were used for the Sordariomycetes and these are unequally distributed across the phylogeny. Augusts obviously performed less than ideally, as the authors reported that it under-annotated the genomes by 10%. I suspect it will have performed worse with increasing phylogenetic distance from the reference genomes. None of the species used for training were insectassociated, except for those generated by the authors for this study. As this feature was used to split the data it could impact the results. Some major results rely explicitly on having good gene annotations, like exon length, adding to these concerns. Looking manually at Table S1 at Ophiostoma, it does seem to be a general trend that the genomes annotated with Magnaporthe grisea have shorter exons than those annotated with H294. I also wonder if many of the trends evident in Figure 5 are also the result of these biases. Clades H1 and G each contain a species used in the training and have an increase in genes for example.

We have applied 6 different reference training sets (instead of one) precisely to address the problem of increasing phylogenetic distance of annotated species. To further investigate the impact of chosen species for training, we plotted five gene features (number of genes, number of introns, intron length, exon length, fraction of genes with introns) as a function of   branch length distance from the species (or genus) used as a training set for annotation. We don’t see systematic biases across different training sets. However,  trends are very clear for clades annotated with fusarium. This set of species includes Hypocreales and Microascales, which is indeed unfortunate since Microascales is an IA group and at the same time the most distant from the fusarium genus in this set. To clarify if this trend is related to annotation bias or a biological trend, we compared gene annotations with those of Mycocosm, between Hypocreales Fusarium species, Hypocreales non-Fusarium species, and Microascales, and we observe exactly the same trends in all gene features. 

Similarly, among species that were annotated with magnaporthe_grisea, Ophiostomatales (another IA group) are among the most distant from the training set species. Here, however, another order, Diaporthales, is similarly distant, yet the two orders display different feature ranges. In terms of exon length, top 2 species in this training set include Ophiostoma, and they reach similar exon length as the Ophiostoma species annotated using H294 as a training set. In summary, it is possible that the choice of annotation species has some effect on feature values; however, in this dataset, these biases are likely mitigated by biological differences among lifestyles and clades. 

Unfortunately, the genomes available from NCBI will vary greatly in the quality of their repeat masking. While some will have been masked using custom libraries generated with software like Repeatmodeler, others will probably have been masked with public databases like repbase. As public databases are again biased towards certain species (Fusarium is well represented in repbase for example), this could have significant impacts on estimating repeat content. Additionally, even custom libraries can be problematic as some software (like RepeatModeler) will include multicopy host genes leading to bona fide genes being masked if proper filtering is not employed. A more consistent repeat masking pipeline would add to the robustness of the conclusions.

We have searched for the same species in JGI Mycocosm and were able to retrieve 58 genome assemblies with matching species, with 19 of them belonging to the same strain as in our dataset. Overall we found no differences in genome assembly length. Interestingly, repeat content was slightly higher for NCBI genome assemblies compared to JGI Mycocosm assemblies, perhaps due to masking of host multicopy genes, as the reviewer mentioned. By comparing pathogenic and non-pathogenic species for the same 19 strains, we observe that JGI Mycocosm annotates fewer repeats in pathogenic species than Augustus annotations (but trends are similar when taking into account 58 matching species). Given a small number of samples, it is hard to draw any strong conclusions; however, the differences that we see are in favor of our general results showing no (or negative) correlation of repeat content with pathogenicity. 

To a lesser degree, I wonder what impact the use of representative genomes for a species has on the analyses. Some species vary greatly in genome size, repeat content, and architecture among strains. I understand that it is difficult to address in this type of analysis, but it could be discussed.

In our case the use of protein sequences could underestimate divergence between closely related strains from the same species. We also excluded strains of the same species to avoid overrepresentation of closely related strains with similar lifestyle traits. We agree that some changes in the genome architecture can occur very rapidly, even at the species level, though analyzing emergence of eg. pathogenicity at the population level would require a slightly different approach which accounts for population-level processes. 

Reviewer #2 (Public review):

Summary:

In this paper, the authors report on the genomic correlates of the transition to the pathogenic lifestyle in Sordariomycetes. The pathogenic lifestyle was found to be better explained by the number of genes, and in particular effectors and tRNAs, but this was modulated by the type of interacting host (insect or not insect) and the ability to be vectored by insects.

Strengths:

The main strength of this study lies in the size of the dataset, and the potentially high number of lifestyle transitions in Sordariomycetes.

Weaknesses:

The main strength of the study is not the clarity of the conclusions.

(1) This is due firstly to the presentation of the hypotheses. The introduction is poorly structured and contradictory in some places. It is also incomplete since, for example, fungusinsect associations are not mentioned in the introduction even though they are explicitly considered in the analyses.

We thank the reviewer for pointing this out. We strived to address all comments and suggestions of the reviewer to clarify the message and remove the contradictions. We also added information about why we included insect-association trait in our analysis. 

(2) The lack of clarity also stems from certain biases that are challenging to control in microbial comparative genomics. Indeed, defining lifestyles is complicated because many fungi exhibit different lifestyles throughout their life cycles (for instance, symbiotic phases interspersed with saprotrophic phases). In numerous fungi, the lifestyle referenced in the literature is merely the sampling substrate (such as wood or dung), which doesn't mean that this substrate is a crucial aspect of the life cycle. This issue is discussed by the authors, but they do not eliminate the underlying uncertainties.

We agree with the reviewer that lack of certainty in the lifestyle or range of possible lifestyles of studied species is a weakness in this analysis. We are limited by the information available in the literature. We hope that our study will increase interest in collecting such data in the future.

Reviewer #3 (Public review):

Summary:

This important study combines comparative genomics with other validation methods to identify the factors that mediate genome size evolution in Sordariomycetes fungi and their relationship with lifestyle. The study provides insights into genome architecture traits in this Ascomycete group, finding that, rather than transposons, the size of their genomes is often influenced by gene gain and loss. With an excellent dataset and robust statistical support, this work contributes valuable insights into genome size evolution in Sordariomycetes, a topic of interest to both the biological and bioinformatics communities.

Strengths:

This study is complete and well-structured.

Bioinformatics analysis is always backed by good sampling and statistical methods. Also, the graphic part is intuitive and complementary to the text.

Weaknesses:

The work is great in general, I just had issues with the Figure 1B interpretation.

I struggled a bit to find the correspondence between this sentence: "Most genomic features were correlated with genome size and with each other, with the strongest positive correlation observed between the size of the assembly excluding repeats and the number of genes (Figure 1B)." and the Figure 1B. Perhaps highlighting the key p values in the figure could help.

We thank the reviewer for pointing out this sentence. Perhaps the misunderstanding comes from the fact that in this sentence one variable is missing. The correct version should be “Most genomic features were correlated with genome size and with each other, with the strongest positive correlation observed between the genome size, the genome size excluding repeats and the number of genes (Figure 1B)”. Also, the variable names now correspond better to those shown on the figure.

Reviewer #1 (Recommendations for the authors):

The authors have clearly done a lot of good work, and I think this study is worthwhile. I understand that my concerns about the underlying data could necessitate rerunning the entire analysis with better gene models, but there may be another option. JGI has a fairly standard pipeline for gene and repeat annotation. Their gene predictions are based on RNA data from the sequenced strain and should be quite good in general. One could either compare the annotations from this manuscript to those in mycocosm for genomes that are identical and see if there are systematic biases, or rerun some analyses on a subset of genomes from mycocosm. Indeed, it's possible that the large dataset used here compensates for the above concerns, but without some attempt to evaluate these issues, it's difficult to have confidence in the results.

We very appreciate the positive reception of our manuscript. Following the reviewer’s comments we have investigated gene annotations in comparison with those of JGI Mycocosm, even though only 58 species were matching and only 19 of them were from the same strain. This dataset is not representative of the Sordariomycetes diversity (most species come from one clade), therefore will not reflect the results we obtained in this study. To note, the reason for not choosing JGI Mycocosm in the first place, was the poor representation of the insect-associated species, which we found key in this study. In general, we found that assembly lengths were nearly identical, number of genes was higher, and the repeat content was lower for the JGI Mycocosm dataset. When comparing different lifestyles (in particular pathogens vs. non-pathogens), we found the same differences for our and JGI Mycocosm annotations, with one exception being the repeat content. In the small subset (19 same-strain assemblies), our dataset showed the same level of repeats between the two lifestyles, whereas JGI Mycocosm showed lower repeat content for pathogens (but notably for all 58 species, the trend was same for our and JGI Mycocosm annotations). None of these observations are in conflict with our results where we find no or negative association of repeat content with pathogens. 

The figures are very information-dense. While I accept that this is somewhat of a necessity for presenting this type of study, if the authors could summarize the important information in easier-to-interpret plots, that could help improve readability.

We put a lot of effort into showing these complicated results in as approachable manner as possible. Given that other reviewers find them intuitive we decided to keep most of them as they are. To add more clarification, we added one supplementary figure showing distributions of genomic traits across lifestyles. Moreover, in Figure 5, a phylogenetic tree was added with position of selected clades, as well as a scatterplot showing distributions of mean values for genome size and number of genes for those clades. If the reviewer has any specific suggestions on what to improve and in which figure, we’re happy to consider it. 

Reviewer #2 (Recommendations for the authors):

I have no major comments on the analyses, which have already been extensively revised. My major criticism is the presentation of the background, which is very insufficient to understand the importance or relevance of the results presented fully.

Lines are not numbered, unfortunately, which will not help the reading of my review.

(1) The introduction could better present the background and hypotheses:

(a) After reading the introduction, I still didn't have a clear understanding of the specific 'genome features' the study focuses on. The introduction fails to clearly outline the current knowledge about the genetic basis of the pathogenic lifestyle: What is known, what remains unknown, what constitutes a correlation, and what has been demonstrated? This lack of clarity makes reading difficult.

We thank the reviewer for pointing this out. We have now included in the introduction a list of genomic traits we focus on. We also tried to be more precise about demonstrated pathogenic traits and other correlated traits in the introduction. 

(b) Page 3. « Various features of the genome have been implicated in the evolution of the pathogenic lifestyle. » The cited studies did not genuinely link genome features to lifestyle, so the authors can't use « implicated in » - correlation does not imply causation.

This sentence also somehow contradicts the one at the end of the paragraph: « we still have limited knowledge of which genomic features are specific to pathogenic lifestyle

We thank the reviewer for this comment. We added a phrase “correlated with or implicated in” and changed the last sentence of the paragraph into “Yet we still have limited knowledge of how important and frequent different genomic processes are in the evolution of pathogenicity across phylogenetically distinct groups of fungi and whether we can use genomic signatures left by some of these processes as predictors of pathogenic state.”.

(c) Page 3: « Fungal pathogen genomes, and in particular fungal plant pathogen genomes have been often linked to large sizes with expansions of TEs, and a unique presence of a compartmentalized genome with fast and slow evolving regions or chromosomes » Do the authors really need to say « often »? Do they really know how often?

We removed “often”.

(d) Such accessory genomic compartments were shown to facilitate the fast evolution of effectors (Dong, Raffaele, and Kamoun 2015) ». The cited paper doesn't « show » that genomic compartments facilitate the fast evolution of effectors. It's just an observation that there might be a correlation. It's an opinion piece, not a research manuscript.

We changed the sentence to “Such accessory genomic compartments could facilitate the fast evolution of effectors”.

(e) even though such architecture can facilitate pathogen evolution, it is currently recognized more as a side effect of a species evolutionary history rather than a pathogenicity related trait ». This sentence somehow contradicts the following one: « Such accessory genomic compartments were shown to facilitate the fast evolution of effectors".

Here we wanted to point out that even though accessory genome compartments and TE expansions can facilitate pathogen evolution the origin of such architecture is not linked to pathogenicity. We reformulated the sentence to “Even though such architecture can facilitate pathogen evolution, it is currently recognized that its origin is more likely a side effect of a species evolutionary history rather than being caused by pathogenicity”.

(f) As the number of genes is strongly correlated with fungal genome size (Stajich 2017), such expansions could be a major contributor to fungal genome size. » This sentence suggests that pathogens might have bigger genomes because they have more effectors. This is contradictory to the sentence right after « At the end of the spectrum are the endoparasites Microsporidia, which have among the smallest known fungal genomes ».

The authors state that pathogens have bigger genomes and then they take an example of a pathogen that has a minimal genome. I know it's probably because they lost genes following the transition to endoparasitism and not related to their capacity to cause disease. I just want to point out that their writing could be more precise. I invite authors to think of young scholars who are new to the field of fungal evolutionary genomics.

We thank the reviewer for prompting us to clarify the text. We rewrote this short extract as follows “Notably, not all pathogenic species experience genome or gene expansions, or show compartmentalized genome architecture. While gene family expansions are important for some pathogens, the contrary can be observed in others, such as Microsporidia. Due to transition to obligatory intracellular lifestyle these fungi show signatures of strong genome contractions and reduced gene repertoire (Katinka et al. 2001) without compromising their ability to induce disease in the host. This raises questions about universal genomic mechanisms of transition to pathogenic state.”

(g) I find it strange that the authors do not cite - and do not present the major results of two other studies that use the same type of approach and ask the same type of question in Sordariomycetes, although not focusing on pathogenicity:

Hensen et al.: https://pubmed.ncbi.nlm.nih.gov/37820761/

Shen et al.: https://pubmed.ncbi.nlm.nih.gov/33148650/

We thank the reviewer for pointing out this omission. We now added more information in the introduction to highlight the importance of the phylogenetic context in studying genome evolution as demonstrated by these studies. The following part was added to introduction:  “Other phylogenomic studies investigating a wide range of Ascomycete species, while not explicitly focusing on the neutral evolution hypothesis, have found strong phylogenetic signals in genome evolution, reflected in distinct genome characteristics (e.g., genome size, gene number, intron number, repeat content) across lineages or families (Shen et al. 2020; Hensen et al. 2023). Variation in genome size has been shown to correlate with the activity of the repeat-induced point mutation (RIP) mechanism (Hensen et al. 2023; Badet and Croll 2025), by which repeated DNA is targeted and mutated. RIP can potentially lead to a slower rate of emergence of new genes via duplication (Galagan et al. 2003), and hinder TE proliferation limiting genome size expansion (Badet and Croll 2025). Variation in genome dynamics across lineages has also been suggested to result from environmental context and lifestyle strategies (Shen et al. 2020), with Saccharomycotina yeast fungi showing reductive genome evolution and Pezizomycotina filamentous fungi exhibiting frequent gene family expansions. Given the strong impact of phylogenetic membership,  demographic history (Ne) and host-specific adaptations of pathogens on their genomes, we reasoned that further examination of genomic sequences in groups of species with various lifestyles can generate predictions regarding the architecture of pathogenic genomes.”

(h) Genome defense mechanisms against repeated elements, such as RIP, are not mentioned while they could have a major impact on genome size (Hensen et al cited above; Badet and Croll https://www.biorxiv.org/content/10.1101/2025.01.10.632494v1.full).

This citation is added in the text above.

(i) Should the reader assume that the genome features to be examined are those mentioned in the first paragraph or those in the penultimate one?

In the last paragraph of the introduction we included the complete list of investigated genomic traits.

(j) The insect-associated lifestyle is mentioned only in the research questions on page 4, but not earlier in the introduction. Why should we care about insect-associated fungi?

We apologize for this omission. We added a sentence explaining how neutral evolution hypotheses can explain patterns of genome evolution in endoparasites and species with specialized vectors (traits present in insect-associated species) and added a sentence in the last paragraph that this is the reason why we have selected this trait for analysis.  

(2) Why use concatenation to infer phylogeny?

(a) Kapli et al. https://pubmed.ncbi.nlm.nih.gov/32424311/ « Analyses of both simulated and empirical data suggest that full likelihood methods are superior to the approximate coalescent methods and to concatenation »

(b) It also seems that a homogeneous model was used, and not a partitioned model, while the latter are more powerful. Why?

We thank the reviewer for the comment. When we were reconstructing the phylogenetic tree  we were not aware of the publication and we followed common practices from literature for phylogenetic tree reconstruction even though currently they are not regarded as most optimal. In fact, in the first round of submission, we have included both concatenation as well as a multispecies coalescent method based on 1000 busco sequences and a concatenation method with different partitions for 250 busco sequences. All three methods produced similar topologies. Since the results were concordant, we chose to omit these analyses from the manuscript to streamline the presentation and focus on the most important results.

(3) Other comments:

Is there a table listing lifestyles?

Yes, lifestyles (pathogenicity and insect-association) are listed in Supplementary Table S1. 

(4) Summary:

(a) seemingly similar pathogens »: meaning unclear; on what basis are they similar? why « seemingly »?

We removed “seemingly” from the sentence.

(b) Page 4: what's the difference between genome feature and genome trait?

There is no difference. We apologize for the confusion. We changed “feature” to “trait” whenever it refers to the specific 13 genomic traits analyzed in this study.

(c) Page 22: Braker, not Breaker

corrected

What do the authors mean when they write that genes were predicted with Augustus and Braker? Do they mean that the two sets of gene models were combined? Gene counts are based on Augustus (P24): why not Braker?

We only meant here that gene annotation was performed using Braker pipeline, which uses a particular version of Augustus. We corrected the sentence.

(d) Figure 2B and 2C:

'Undetermined sign' or 'Positive/Negative' would be better than « YES » or it's just impossible to understand the figure without reading the legend.

We changed “YES” to “UNDETERMINED SIGN” as suggested by the reviewer.

I think that it's fascinating that the term used is poison. Almost implying that it will affect or poison others, like the internet is connected and that we can work together just like in real life.

I find this passage meaningful because it reminds teachers that students’ behavior often reflects hidden struggles rather than lack of effort. I agree that empathy and cultural understanding are key for educators to truly connect with and support students from low-income backgrounds. My question is how schools can ensure that this kind of professional learning becomes a lasting part of teacher training instead of just a one-time workshop.

As much as I enjoy the concept of trolling and feel that it's one of the most unique parts of the internet, bad faith arguing has gotten so out of control and soiled so much discourse that takes place online. The idea that now people will engage in discussions or arguments while positing opinions and ideas they don't really stand for completely derails the concept of debate in the first place, and so while I enjoy a bit of trolling here and there, bad faith I believe is just unhealthy.

This article outlines how direct messaging systems have evolved across social media platforms, but what stood out to me is few of these systems are truly private. Even when messages are labeled as direct or personal, they are still stored on centralized servers that companies can access for moderation, data analysis, or even advertising purposes. This connects directly to 9.1's discussion of privacy illusions. How private online communication is often just a matter of perception. It makes me question whether privacy online is ever absolute, or if it's always conditional on the platform's policies and profit motives.

I find this section very relatable because it captures how fragile our sense of privacy really online. The example of private messaging makes me think about how I often assume my DMs are confidential, even though they are stored and possibly analyzes by the platform itself. What feels private to users is often just conveniently invisible. I think this blurring between private and public spaces is what makes digital privacy so psychologically complex. It's not only about hiding information but about controlling context and audience. The idea that company can read what I write to a friend reminds me that privacy online is less of a right and more of a temporary permission.

Honestly, it’s kind of wild how social media uses our data to keep us hooked. I get how targeted ads can be helpful sometimes, like showing you stuff you might actually want, but it also feels manipulative. The part that stood out to me most is how they use data to figure out what keeps people on the app longer—it’s like they’re studying us just to make sure we don’t stop scrolling. I’ve definitely noticed that when I like one type of video, suddenly my feed is full of that topic, and it’s super easy to waste time without realizing it. It makes me wonder how much control we really have over what we see online.