Author Response

Reviewer #1 (Public Review):

Summary:

This manuscript introduces an exciting way to measure SARS-CoV-2 aerosolized shedding using a disposable exhaled breath condensate collection device (EBCD). The paper draws the conclusion that the contagious shedding of the virus via aerosol route persists at a high level 8 days after symptoms.

Strengths:

The methodology is potentially of high importance and the paper is clearly written. The study design is clever. If aerosolized viral load kinetics truly differed from those of nasal swabs, then this would be a very important finding.

Thank you for your encouraging remarks. We agree that a comparison between aerosolized viral load and nasal swabs would strengthen our findings, and we have collected new specimens which will enable this comparison: In each session we collected both nasal swabs and exhaled breath samples, and we are in the process of analyzing these data. These data will be included in our revised manuscript.

Weaknesses:

The study conclusions are not entirely supported by the data for several reasons:

(1) Most data points in the study are relatively late during infection when viral loads from other compartments (nasal and oral swabs) are typically much lower than peak viral loads which often occur in the pre-symptomatic or early symptomatic phase of infection. Moreover, the generation time for SARS-CoV-2 has been estimated to be 3-4 days on average meaning that most infections occur before or very early during symptoms. Therefore, the available epidemiologic data does not support 12 days of infection (day 8 symptoms) as important for most transmissions. Therefore, many of the measurement timepoints in this study may not be relevant for transmission.

Thank you for your comment. Notably, our new data set includes a small number of specimens that were collected prior to the start of symptoms, and so we may be able to partially address this concern with those data. That said, we agree that a limitation of our study is that we were unable to collect specimens prior to symptom onset, and that this pre-symptomatic period represents a fruitful area for future work. However, significant questions do remain open regarding transmission dynamics of SARS-CoV-2, including the extent of transmission after symptom onset, and therefore, despite this limitation of our data, we feel that our method may contribute to further understanding of those dynamics. However, we will include a more prominent discussion of this limitation in the revised manuscript.

(2) Fig 1A would be more powerful as a correlation plot between viral load from nasal samples (x-axis) and aerosol (y-axis). One would expect at least a rough correlation (as has been seen between viral loads in oral and nasal samples) and deviations from this correlation would provide crucial information about how and when aerosol shedding is discordant from nasal samples (ie early vs late time points, low versus high viral loads< etc...). It is too strong to state correspondence is 100% when viral load is only measured in one compartment and nasal swabs are reduced to the oversimplified "positive or negative".

Thank you for this suggestion, we agree that the figure would be more powerful as a correlation plot between viral load from nasal samples and aerosol. Unfortunately, at the time these samples were collected, the ER at Northwestern Hospital was diagnosing SARS-CoV-2 patients using the Abbott ID NOW rapid diagnostic platform, which, despite being a PCR-based system, does not provide quantitative information about viral loads, and instead provides a binary positive/negative result. Since we were looking for a direct comparison between the clinical diagnostic test and our test, we considered the binary aspect of our data (detected/undetected), and found 100% correspondence, meaning that when the clinical test detected SARS-CoV-2, our test did too. We have collected additional data which includes quantitative PCR values from nasal swabs collected at the same time as breath samples and we will include these data in the format you suggest, once analyzed, in our revised manuscript.

(3) Results are reported in RNA copies which is fine but particle-forming units (pfu, or quantitative culture) are likely a more accurate surrogate of infectivity. It is quite possible that all of these samples would have been negative for pfu given that the ratio of RNA: pfu is often >1000 (though also dynamic over time during infection). This could be another indicator that most samples in the study were collected too late during infection to represent contagious time points.

We agree that culturing exhaled breath samples would be an important addition to our understanding of the transmission dynamics of SARS-CoV-2 and we consider this to be an important next step for our method. Because we did not perform culturing of our breath samples in this study, we avoided making claims about infectivity of our samples in this manuscript, and instead speculate about the future utility of our method in understanding transmission dynamics, once an appropriate surrogate of infectivity is performed. We will make sure this is clearer in the revised manuscript. That said, other groups have successfully cultured breath samples with corresponding CT values in a range that are well within the range we found in our study, and sufficient for transmission (for example, Alsved et al, 2023, CT range ~33-38). These studies support the idea that a significant portion of the viral RNA measured in our samples may come from viable virus. Therefore, quantifying the ratio of viable to nonviable virus in our samples is an important next step. We appreciate this comment, and we will add a clearer discussion of this point to the revised manuscript.

(4) Individual kinetic curves should be shown for participants with more than three time points to demonstrate whether there are clear kinetic trends within individuals that would help further validate this approach. The inclusion of single samples from individuals is less informative.

We will add individual kinetic curves to the revised manuscript.

(5) The S-shaped model in 2A is somewhat misleading as it is fit to means but there is tremendous variability within the data. Therefore the 8-day threshold should be listed clearly as a mean but not a rule for all individuals. The statement that viral RNA copies do not decrease until 8 days from symptom onset is unlikely to be true for all infected people and can't be made based on the available data in this study given that many people contributed only one datapoint.

We will clarify the language in the manuscript and make limitations of the 8-day interpretation clearer.

(6) The incubation period for SARS-CoV-2 is highly variable. Therefore duration of symptoms is a rather poor correlate of the duration of infection. This further diminishes the interpretive value of positive samples from individuals who were only sampled once.

We will add a discussion of this point to the revised manuscript.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Lane and colleagues measured the abundance of SARS-CoV-2 on breath in 60 outpatients after the development of COVID-19 symptoms using a novel breath collection apparatus. They found that, overall, viral abundance remains high for approximately eight days following the development of symptoms, after which viral abundance on breath drops to a low level that may persist for approximately 20 days or more. They did not identify significant differences in viral shedding on breath by vaccination status or viral variant. They also noted substantial variation in the degree and duration of shedding across individuals.

Strengths:

The primary strengths of this study are (1) the focus on breath, rather than the more traditional nasal/oropharyngeal swabs, and (2) the fact that the data were collected at multiple time points for each infection. This allows the authors to characterize not only mean viral abundance across individuals but also how that abundance changes over time, allowing for a better understanding of the potential duration of infectiousness of SARS-CoV-2.

Weaknesses:

The sample size is moderate (60) and focuses only on outpatients. While these are minor weaknesses (as the authors note, the majority of SARS-CoV-2 transmission likely occurs among those with symptoms below the threshold of hospitalization), it would nevertheless be useful to have a fuller understanding of variation in viral shedding across clinical groups.

We agree this would be very interesting and feel our method, which is straightforward to perform in clinical settings, lends itself to future studies across clinical groups. We have added discussion of this to the discussion section of the manuscript.

Furthermore, the study lacks information on viral shedding prior to the development of symptoms, which may be a critical period for transmission. Since the samples were collected at home by study participants using a novel apparatus, it is difficult to assess the degree to which actual variation in viral abundance, user variability, and/or measurement variation is inherent to the apparatus.

This is a great point, which we will discuss in our revised manuscript.

Author Response

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

Reviewer #1

Reviewer #1’s main concerns revolved around the evidential strength of the study’s conclusion that age-specific effects of birth weight on brain structure are more localized and less consistent across cohorts than age-uniform, stable effects. Specifically, the reviewer points out the evidence (or lack of such) for age-specific effects. We have rearticulated as a “bullet-point summarization” the reviewer’s concerns for a better response (please, see the original reviewer’s response in the annexed document). We thank the reviewer for his/her comment.

Concern #1: No direct statistical comparisons are conducted between samples (beyond the spin-tests).

In the initial version of the manuscript, the spin-tests represented a key test since they compared the spatial distribution of birth weight effects across samples. In the revised manuscript, we additionally perform a replicability analysis across samples both for birth weight effects on brain characteristics and on brain change in a similar fashion as described for the within-sample analysis. The results of these analyses provide complementary evidence of robust associations of birth weight effects on cortical characteristics (for area and volume, less so for thickness) and of unreliable associations of birth weight on cortical change. These analyses are briefly mentioned in the main document and fully described as supplementary information. Briefly, the effects of birth weight on cortical area and cortical volume showed high (exploratory and confirmatory) replicability while replicability was almost nonexistent for the effects of birth weight on cortical change. See below, under Reviewer #1, concern #2, for a description of the changes in the revised manuscript.

Concern #2: The differential composition of samples in terms of age distribution leads to the possibility that lack of results is explained by methodological differences.

The revised version of the manuscript provides now a within-sample replicability analysis of the birth weight effects on cortical change. This analysis addresses the reviewer’s concern as the lack of replicability in this analysis cannot be attributed to sample or methodological differences. We thank the reviewer for suggesting this analysis which provides further quantification of the (lack of) robustness of the birth weight effects on cortical change. See below for changes in the revised version of the manuscript concerning additional replicability analyses which were carried out as a response to reviewer #1 concerns #1 and #2.

pp. 12-3. “Additionally, we performed replicability analyses both across and within samples to further investigate the robustness of the effects of birth weight on cortical characteristics and cortical change. Split-half analyses within datasets were performed, to investigate the replicability of significant effects 36,37 of BW on cortical characteristics within samples (refer to Figure 1). These analyses further confirmed that the significant effects were largely replicable for volume and area, but not for thickness (see Supplementary Figure 11). Split-half analyses of BW on cortical change (refer to Figure 2) showed, in general, a very low degree of replicability on the three different cortical measures. See Supplementary Table 3. Replicability across datasets showed a similar pattern, that is, replicability was high for the effect of brain weight on cortical characteristics but very low for the effects of cortical change. See Supplementary Table 4 for stats. See Supplementary statistical methods for a full description of the analyses. These analyses provide complementary evidence of robust associations of BW with cortical area and volume – but not cortical change - across and within samples.”

p. 41. “For each dataset and cortical measure, we assessed the effects of birth weight on cortical structure and cortical change (…)”

p. 42. “Across samples replicability was performed as described in the within-sample replicability analysis (i.e., we assessed the exploratory and confirmatory replicability) except that split-half was not performed - the three datasets were compared with each other - and the analyses were performed in the original fsaverage space.”

pp. 54-55. “The exploratory replicability of birth weight on cortical change was negligible across datasets and measures [.00 (.00), .00 (.00), .00 (.00) for area, .02 (.09), .00 (.02), .01 (.03) for volume, and .01 (.05), .01 (.14), .00 (.01) for thickness] while confirmatory replicability was generally poor, except for the ABCD dataset [.02 (.05), .68 (.35), .00 (.00) for area, .08 (.14), .56 (.25), .00 (.02) for volume, and .37 (.26), .60 (.27), .01 (.03) for thickness] (see Supplementary Table 3).

These results are not fully comparable to other studies assessing the replicability of brain phenotype associations due to analytical differences (e.g. sample size, multiple-comparison correction method)20,36, yet clearly show that the rate of replicability of BW associations with cortical area and volume are comparable to benchmark brain-phenotype associations such as body-mass index and age68. Lower levels of replicability in the LCBC subsample are likely attributable to higher sample variability (e.g. increased age span). Kinship may lead to inflated patterns of replicability within the ABCD cohort. Confirmatory replicability is, also, to some degree, affected by sample size, and thus the estimates of confirmatory replicability may be somewhat inflated in the ABCD dataset.

Finally, the degree of across-sample replicability was high for the effects of birth weight on cortical area and volume (average confirmatory replicability = .96 and .93), low for thickness (.27), and negligible for the effects of birth weight on cortical change (.03, .06, and .06). See further information in Supplementary Table 4.”

Concern #3: Some datasets have a narrow age range precluding the detection of age-related effects.

We do not believe concern #3 is a major problem since timebirth weight refers to a within subject contrast, e.g., longitudinal-only-based contrast. Birth weight, even when self reported, is a highly reliable measure and the sample sizes are relatively large (n = 635, 1759, and 3324 unique individuals). Note that the smaller dataset does have longer follow-up times and more observations per participant, increasing the reliability of estimations in individual change. Structural MRI measures have very high reliability. Clearly, longitudinal brain change is less reliable, yet the present sample size and the high reliability of birth weight should provide enough statistical power to capture even small time-varying effects of birth weight on brain structure. Note as well that in each model age is treated as a covariate. Rather, the consistency of timebirth weight (that is, the effects of birth weight on cortical change) is assessed with split-half replications within and across samples. In this methodological pipeline, a narrow age range for a given dataset, if anything, may constitute an advantage. We have clarified the statistical model (see changes in the revised manuscript, referred to in response to reviewer #1, concern #5).

Concern #4 The modeling strategy does not allow for non-linear interaction between age and BW suggesting the use of spline models instead in a mega-analytical fashion.

Indeed, we agree that some - if not most - brain structures follow non-linear trajectories throughout life. In the present study, age regressors are used only for accounting for variance in the data rather than capturing any effect of interest. Rather, it is the time*birth weight regressor that captures age-varying changes in brain structure. Time reflects within-subject follow-up time. We believe non-linear modeling of age will only account for additional variance (compared to linear models) in the LCBC dataset given the dataset’s wider age range, while it will not have any consequential effect in the ABCD and UKB datasets (as predicted in the provisional response). In any case, we recognize it as a valid concern. Consequently, we have rerun the main models in an ROI-based fashion using or not using spline models to fit age. Specifically, we have fitted the models in each of Desikan-Killiany’s ROIs using generalized additive mixed models (GAMM with age as a smooth term) or linear mixed models (LME with age as a linear regressor). The results are shown in Supplementary Figures 13 and 14. The Beta regressors are nearly identical. As expected, the differences are noticeable in the LCBC dataset while the effect of using - or not using- splines to fit age is almost null in the other two datasets. See also FDR-corrected maps below for both birth weight effects on brain structure and brain change (we opted to show Beta-maps as supplementary material as the multiple-comparisons correction in the ROI-based analysis is not fully comparable with the one used in the vertex-wise approach).

p. 9: “Both birth weight effects on cortical characteristics and cortical change were rerun (ROIwise) using spline models that accounted for possible non-linear effects of age on cortical structure. The results were comparable to those reported above in Figures 1 and 2. See Supplementary Figures 13 and 14 for birth weight effects on cortical characteristics and cortical change, respectively.”

Caption to Supplementary Figure 13. “Comparison between spline (GAMM) and linear (LME) models on the effect of birth weight on cortical characteristics. Age was fitted either as a smoothing spline using generalized additive mixed models (GAMM, mgcv r-package) or a linear regressor with a linear mixed models (LME, lmer r-package) framework. The analyses were performed ROI-wise using the Desikan-Killiany atlas. Significance was considered at a FDR corrected threshold of p < 0.04. All the remaining parameters were comparable to the main analyses shown in Figure 1. The viridis-yellow scale represents the lower-higher Beta regressors. Red contour displays regions showing significant effects of birth weight. Note the high correspondence with both fitting models. Differences are only noticeable in the LCBC sample due to the datasets’ wider age range (i.e., lifespan dataset).” Caption to Supplementary Figure 14. “Comparison between spline (GAMM) and linear (LME) models on the effect of birth weight on cortical change. Age was fitted either as a smoothing spline using generalized additive mixed models (GAMM, mgcv r-package) or a linear regressor with a linear mixed models (LME, lmer r-package) framework. The analyses were performed on ROI-based using the Desikan-Killiany atlas. Significance was considered at a FDR corrected threshold of p < 0.04. All the remaining parameters were comparable to the main analyses shown in Figure 1. The viridis-yellow scale represents the lower-higher Beta regressors. Red contour displays regions showing significant effects of birth weight. Note the high correspondence with both fitting models. Differences are only noticeable in the LCBC sample due to the datasets’ wider age range (i.e., lifespan dataset).” The figures below show the birth weight effects on brain characteristics (above) and change (below) using a GAMM or an LME approach; that is, using age as a smooth term or as a regressor. FDR-corrected p < 0.05 values are shown in a signed logarithmic scale. Red-yellow values represent positive associations between birth weight and brain while blue-lightblue values represent negative associations. The results are qualitatively comparable and quantitative differences exist only in the LCBC dataset. Please see Supplementary Figures 13 and 14 in the revised manuscript.

Author response image 1.

Concern #5: Greater clarity regarding the statistical models and the provision of effect-size maps.

The revised manuscript provides additional information regarding the statistical model, especially in the results section, to avoid misunderstanding (see below examples of clarifications in the revised manuscript). We now provide Beta-maps, F-maps, unthresholded p-values maps, and degrees of freedom for the main univariate analyses. That is, we provide this information for both the whole sample and the twin analyses which correspond to Figures 1, 2, 4, and 5. We opted not to compute effect-size estimates (e.g. partial eta-squared, cohen’s d) due to the ambiguous interpretation of these maps in the context of linear mixed models.

p.8. “To test the effect of birth weight on cortical change we rerun the analyses with BW x time and age x time interactions. Note BW x time (i.e., within-subject follow-up time) represents the contrasts of interest while age – and age interactions – are used to account for differences in age across individuals.”

p.11. “In contrast, the spatial correlation of the maps capturing BW-associated cortical change (i.e., BW x time contrast) …”

p. 12. “Additionally, we performed replicability analysis both across and within samples to further investigate the robustness of the effects of birth weight on cortical characteristics and cortical change.”

p. 14: “BW discordance analyses on twins specifically were run as described for the main analyses above, with the exception that twin scans were reconstructed using FS v6.0.1. for ABCD and the addition of the twin’s mean birth weight as a covariate.”

p .31. “Group-level unthresholded p-maps, F-maps, Beta-maps, and degrees of freedom for the univariate analyses accompany this manuscript as additional material.”

Author Response

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

Reviewer #1 (Recommendations For the Authors):

(1) While not absolutely necessary - it would be nice to see at least at the in-situ level what happens to the handful of other HC-important transcription factors in the Rbm24 KO (IKZF2, Barlh1, RFX) as the authors did look at Insm1.

Reply: Thanks for your suggested experiments. We agree that knowing whether the genes that are known to be involved in cell survival regulation are changed will provide insights into the mechanisms underlying cell death of Rbm24-/- HCs. Our data showed that Ikzf2 seemed to be upregulated when in the Rbm24-/- HCs, relative to Rbm24+/+ HCs at P5. We also tested Barlh1 and RFX, but we did not obtain confident data to present. Nonetheless, following the reviewer’s logic, we further tested Gata3, another gene involved in HC survival, and found that Gata3 was down-regulated in Rbm24 -/- HCs, compared to Rbm24+/+ HCs. Please refer to the text on lines 12-22 on page 12 and lines 1-10 on page 13, and Figure 3-figure supplement 1.

(2) Major comments: The nomenclature for mouse gene vs. mouse protein needs to be addressed throughout the manuscript. The nomenclature when referring to a mouse gene: gene symbols are italicized, with only the first letter in upper-case (e.g. Rbm24).

The nomenclature when referring to a mouse protein: Protein symbols are not italicized, and all letters are in upper-case (e.g. RBM24).

Reply: Thanks for pointing it out. In the entire manuscript, we have followed the reviewer’s comments to list gene and protein.

(3) Supplemental Figure 2D: Individual data points should be displayed on the bar graph via dots. SEM is not appropriate for this graph as SEM precision with only 3 samples is low. Furthermore, readers are more interested in knowing the variability within samples and not proximity of mean to the population mean, therefore standard deviation (SD) should be used instead.

Reply: We have edited the Figure 1-figure supplement 2D, as suggested. The Figure 1figure supplement 2 legend was updated, too. Please refer to line 21-22 on page 32.

(4) Red/Green should be avoided, especially when both are on the same image (merged immunofluorescence images that are found throughout the manuscript). I highly recommend changing to a color-blind friendly color scheme (such as cyan/green/magenta, cyan/magenta/yellow, etc.) for inclusivity.

Reply: Thanks for pointing it out. We have changed the red to magenta in all our Figures and figure supplements.

(5) Minor comments: As CRISPR-stop is a major method used throughout the paper, a brief explanation is needed for readers to understand what this methodology entails and why it was used. Something along the lines of," The CRISPR-stop technique allows for the introduction of early stop codons without the induction of DNA damage via Cas9 which can cause deleterious effects".

Reply: We have further elaborated how CRISPR-stop works and its advantages. Please refer to lines 8-13 on page 5.

(6) Page 5; line 5 - "Phenotypes occur earlier..." Grammar

Reply: The grammar error was corrected. Please refer to line 4, page 5.

(7) Page 5; line 5 - "Given Pou4f3 is the upstream regulator..." Not proven, rephrase

Reply: We have rephrased this sentence. Please refer to lines 5-6 on page 5.

(8) Supplemental 1A: Fine, Proof of knockout, I wouldn't mention INSM1 being "irregular"

Reply: We have rephrased this sentence. Please refer to lines 2-3 on page 6.

(9) Page 5; line21 - "Alignment of Insm1+ OHCs was not as regular..." Not a good description

Reply: We have rephrased this sentence. Please refer to lines 2-3 on page 6.

(10) Page 6; line11 - "Rbm24 was completely absent.." Redundancy with line 9

Reply: Thanks for pointing it out, and we have removed the redundant sentence.

(11) Page 7 - HA tag should be indicated originally as: Hemaglutinin (HA)

Reply: We have switched “HA” to “Hemaglutinin (HA)”. Please refer to line 15, page 7.

(12) Page 9, line 11- "Determine if autonomous/noncell autonomous." Disagree, cells still clustered in supplemental fig 4.

Reply: We have removed this sentence.

Reviewer #2 (Recommendations For The Authors):

The writing of the manuscript is adequate, but it would certainly be improved by professional editing.

Reply: Thanks for the reviewer’s encouraging comments. The revised version of our manuscript has been edited by an English native speaker.

Author Response

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

eLife assessment

The manuscript from Richter et al. is a very thorough anatomical description of the external sensory organs in Drosophila larvae. It represents an important tool for investigating the relationship between the structure and function of sensory organs. Using improved electron microscopy analysis and digital modeling, the authors provide compelling evidence offering the basis for molecular and functional studies to decipher the sensory strategies of larvae to navigate through their environment.

Public Reviews:

Summary

This is a very meticulous and precise anatomical description of the external sensory organs (sensillia) in Drosophila larvae. Extending on their previous study (Rist and Thum 2017) that analyzed the anatomy of the terminal organ, a major external taste organ of fruit fly larva, the authors examined the anatomy of the remaining head sensory organs - the dorsal organ, the ventral organ, and the labial organ-also described the sensory organs of the thoracic and abdominal segments. Improved serial electron microscopy and digital modeling are used to the fullest to provide a definitive and clear picture of the sensory organs, the sensillia, and adjacent ganglia, providing an integral and accurate map, which is dearly needed in the field. The authors revise all the data for the abdominal and thoracic segments and describe in detail, for the first time, the head and tail segments and construct a complete structural and neuronal map of the external larval sensilla.

Strengths

It is a very thorough anatomical description of the external sensory organs of the genetically amenable fruitfly. This study represents a very useful tool for the research community that will definitely use it as a reference paper. In addition to the classification and nomenclature of the different types of sensilla throughout the larval body, the wealth of data presented here will be valuable to the scientific community. It will allow for investigating sensory processing in depth. Serial electron microscopy and digital modeling are used to the fullest to provide a comprehensive, definitive, and clear picture of the sensory organs. The discussion places the anatomical data into a functional and developmental frame. The study offers fundamental anatomical insights, which will be helpful for future functional studies and to understand the sensory strategies of Drosophila larvae in response to the external environment. By analyzing different larval stages (L1 and L3), this work offers some insights into the developmental aspects of the larval sense organs and their corresponding sensory cells.

Weaknesses

There are no apparent weaknesses, although it is not a complete novel anatomical study. It revisits many data that already existed, adding new information. However, the repetitiveness of some data and prior studies may be avoided for easy readability.

We would like to thank the reviewers for their respective reviews. The detailed comments and efforts have helped us to improve our manuscript. In the following, we have listed the comments one by one and provide the respective information on how we addressed the concerns.

Recommendations for the authors:

We have tried to address every single comment as far as possible. In order to structure our response a little better, we have listed the relevant page number and the original comments once again. Directly following this you will find our response and a description of what we have changed in the manuscript.

REVIEWER #1 (Recommendations For The Authors):

I have a few comments that will help the reader navigate this long and detailed paper.

REVIEWER 1.1. page 4

The final section of "the Structural organization of Drosophila larvae" needs some reorganization.

Specifically:

"The DO and the TO are prominently located on the tip of the head lobes" Can the authors rewrite the sentence in a way that it is clear that there is one DO and one VO on each side of the head? Check at the beginning of each section, please. There is a mention about hemi-segments but it is still confusing.

Done – replaced with “The largest sense organs of Drosophila larvae are arranged in pairs on the right and left side of the head.”

REVIEWER 1.2. page 5

"The sequence of sensilla is always similar for and different between T1, T2-T3, and A1-A7" This sentence is not clear, please break it into two sentences.

Done – replaced with: “We noticed varying arrangements for T1, T2-T3, and A1-A7, with a consistent sequence of sensilla in each configuration.”

REVIEWER 1.3. figures page 4

Double hair can't be found in Figure 1B or C (is it h3, h4?) - please clarify.

Done - changed to double hair organ in page 11, included double hair sketch in legend in figure 1B. We changed the name of the structure to double hair organ, to clarify that this is a compound sensillum consisting of two individual sensilla.

REVIEWER 1.4. page 5

The authors go back and forth in their descriptions of the different sensory organs. Knob sensilla and then papilla sensilla are discussed and then a few lines later a further description is done. Please unify the description of each separately.

Done – we restructured the whole section.

REVIEWER 1.5. figures page 6

"We found three hair sensilla on T1-T3, and "two" on A1-A7" - in the figure there seem to be "four" on A1-A7.

Done – we included the two hair sensilla of the double hair organ

REVIEWER 1.6. figures page 6

DORSAL ORGAN:

Can the authors explain the colour map meaning in Figure 2A? It is explained in 2C but the image already has colours. Add your sentence "Color code in A applies to all micrographs in this Figure".

Done – we added a sentence to explain that the color code in A applies to the whole figure.

REVIEWER 1.7. page 6

Page 10: which comprises seven olfactory sensilla "composing" three dendrites each: replace this with"with". At the end, we want to think 7 X 3= 21 ORNs.

Done – replaced.

REVIEWER 1.8. page 9

CHORDOTONAL ORGANS:

"We find these these DO associated ChO (doChO).. .". Please remove one "these"

Done – removed.

REVIEWER 1.9. page 8

Is the DO associated ChO part of the dorsal ganglion???? It does not look like it. Could you clarify?

Done – we added a sentence that clarifies that the ChO neuron is not iside the DOG.

REVIEWER 1.10. page 9 VENTRAL ORGAN: A figures page 12

Please add to the Figure 8 legend the description of 8c' and 8c'?

Done – added description in figure legend.

B page 9

8H, what are the *, arrows? Please clarify - it is hard to interpret the figure.

Done – we added parentheses in the figure legend that state which structures the asterisks and arrows indicate.

C page 9

"Three of them are innervated by a single neuron () and one by two neurons () (Figure 8F-I). Please add which are innervated by 1 (VO1, VO2-VO4) and which by 2 (VO3).

Done – we added parentheses that clarify which sensilla are innervated by 1 or 2 neurons.

REVIEWER 1.11. page 9

Can you add something (or speculate) about the difference in sensory processing of the different types of sensilla?

Done – new sentence in discussion:

‘Their different size and microtubule organization likely correlate with processing of different stimulus intesities applied to the mechanotransduction apparatus (Bechstedt et al. 2010).’

REVIEWER 1.12. figures page 16

PAPILLA AND HAIR SENSILLA:

FIGURE 10a, please add the name of each sensillum from p1, p2, px py, etc... (if not we have to go back to figure 1 when you describe specific ps.)

Thanks for the comment, it really makes it a lot easier for the reader.

REVIEWER 1.13. figures page 18 Figure 11, can you add the name of each hair, please?

Done – updated figure.

REVIEWER 1.14. figures pages 16, 18, 20

In Figures 10, 11, and 12 you clearly draw an area on the internal side that I assume is what you call the "electron-dense sheath". It is wider in papilla sensilla than in hair sensilla, most likely due to the difference in stimuli sensed that you explain in detail in the discussion. Can you say in the figure what this "internal" thing is? Can you add this difference to your list "Apart from the difference in outer appearance and structure of the tubular body"?

This is the basal septum, but it is not certain that it is wider in the papillae sensillae, at least we could not observe this in our data sets. The impression could have been created by different scales in the 3D reconstructions and a perspective view. Therefore, we do not want to list this as a difference here, as we are not sure.

However, we have now specified the socket septum in the figure legends and in Figures 10A, 11A and 12A.

REVIEWER 1.15. page 11

KNOB SENSILLA:

Page 25;" Knob sensilla have been described under "vaious" names such as": add various.

Done

REVIEWER 1.16. page 12

"reveals that the three hair and the two papilla sensilla are associated with a single dendrite." Can you write that "reveals THAT EACH OF the three hair and the two papilla sensilla" if not it seems that there is only one dendrite.

Done

REVIEWER 1.17. figures page 25 TERMINAL SENSORY CONES:

Please name the t1-t7 cones in Figure 15A.

Done – we updated the figure.

REVIEWER 1.18. page 13

The spiracle sense organ deserves a new paragraph. As does the papilla sensillum of the anal plate.

Done – we added subtitles before the prargraphs.

Discussion:

REVIEWER 1.19. page 15

Page 38: "v'entral" correct typo

PAGE 15

Done – we have updated the nomenclature  ventral 1 (v), ventral 2 (v’) and ventral 3 (v’’)

REVIEWER #2 (Recommendations For The Authors):

I have only a few comments:

REVIEWER 2.1. page 5

p.5, right column, middle: the use of trichoid, campaniform, and basiconical (sensilla) in previous works were based on even older papers and reviews that attempted to link EM architecture to function (e.g., KEIL, T. A. & STEINBRECHT, R. A. (1986). Mechanosensitive and olfactory sensilla of insects. In Insect Ultrastructure, vol. 2. (ed. R. C. King & H. Akai), pp. 477-516. New York/London: Plenum Press). Trichoid sensilla can be mechano-sensitive, olfactory, or gustatory; trichoid simply refers to the shape (hair). The same applies to basiconical sensilla. The use of "campaniform", which Ghysen et al called "papilla sensilla", was the only really problematic case, because these (Drosophila larval) sensilla did not really resemble closely the classical campaniform sensilla (e.g., adult haltere). The only reason we called them campaniform is because they were not more similar to any other type of (previously named) sensillum.

Thank you for the explanation. The nomenclature of structures is generally always a complex topic with often different approaches and principles. We are aware of this and have therefore tried to be as careful as possible. We were not sure from this comment whether you were suggesting to change the text or whether you wanted to explain how these names were assigned to the sensilla in the past. However, we hope that the current version is in line with your understanding, but could of course make changes if necessary (see also comments of reviewer 1).

REVIEWER 2.2. page 9

p.21, Labial Organ: the ventral lip is the labium; the dorsal one is the labrum.

Done – replaced labrum with labium.

REVIEWER 2.3. page 9

p.20/21, Ventral organ and labial organ: here, the projection of the axons could be mentioned as an ordering principle. In the previous literature, for larva and embryo, a labial organ (lbo) was described that most likely corresponds to the labial organ presented here. This (previously mentioned) lbo characteristically projects along the labial nerve to the labial segment (hence the name). It fasciculates with axons of another sensory complex, also generated by the labial segment, namely the ventral pharyngeal sensory organ (VPS). Does the labial organ described here share this axonal path?

Yes, it has the same axonal pathway and is the same organ as the lbo. We have tried to standardise the nomenclature for all important external head organs (DO, TO, VO, LO) and have therefore used abbreviations with two letters. However, to avoid confusion, we have now added that the LO was also called lbo in the past.

For the ventral organ, the segmental origin (to my knowledge) was never clarified. The axons of the ventral organ project along the maxillary nerve (which carries axons of the terminal=maxillary organ). This nerve, closely before entering the VNC, splits into a main branch to the maxillary segment (TO axons) and a thinner branch that appears to target the mandibular segment. This branch could contain the axons of the ventral organ (as described previously and in this paper). Could the authors confirm this axonal projection of the VO?

In this work, we did not focus on the axonal projections into the SEZ. This is also not a simple and fast process, as in the entire larval dataset, the large head nerves unfortunately exhibit a highly variable quality of representation. Therefore, the reconstruction of nerves and individual neurons within it is often challenging and very time-consuming. The research question is, of course, very intriguing, and one could also attempt to match each sensory neuron of the periphery with the existing map of the brain connectome. However, this is a project in itself, exceeding the scope of this work, and is therefore more feasible as a subsequent project.

REVIEWER #3 (Recommendations For The Authors):

Minor suggestions that the authors might consider:

REVIEWER 3.1. figures all

Recheck the scale bar in figures and figure legends. Missing in a few places.

Done – we replaced or added some (missing) scale bars in figures and figure legends (see annotated figure document).

REVIEWER 3.2. figures page 4

The color schematic in Figure 1 can be improved for readability.

Done – we changed the color schematic, especially for the head region to improve readability.

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The manuscript titled "Coevolution due to physical interactions is not a major driving force behind evolutionary rate covariation" by Little et al., explores the potential contribution of physical interaction between correlated evolutionary rates among gene pairs. The authors find that physical interaction is not the main driving of evolutionary rate covariation (ECR). This finding is similar to a previous report by Clark et al. (2012), Genome Research, wherein the authors stated that "direct physical interaction is not required to produce ERC." The previous study used 18 Saccharomycotina yeast species, whereas the present study used 332 Saccharomycotina yeast species and 11 outgroup taxa. As a result, the present study is better positioned to evaluate the interplay between physical interaction and ECR more robustly.

Strengths & Weaknesses:

Various analyses nicely support the authors' claims. Accordingly, I have only one significant comment and several minor comments that focus on wordsmithing - e.g., clarifying the interpretation of statistical results and requesting additional citations to support claims in the introduction.

We are pleased the reviewer found the analyses to support the claims. We have addressed comments related to clarifying interpretations as suggested in the Recommendations to the Authors. For example, we have added discussion and clarification on the other parameters that could affect the strength of ERC correlations.

Reviewer #2 (Public Review):

Summary:

The authors address an important outstanding question: what forces are the primary drivers of evolutionary rate covariation? Exploration of this topic is important because it is currently difficult to interpret the functional/mechanistic implications of evolutionary covariation. These analyses also speak to the predictive power (and limits) of evolutionary rate covariation. This study reinforces the existing paradigm that covariation is driven by a varied/mixed set of interaction types that all fall under the umbrella explanation of 'co-functional interactions'.

Strengths:

Very smart experimental design that leverages individual protein domains for increased resolution.

Weaknesses:

Nuanced and sometimes inconclusive results that are difficult to capture in a short title/abstract statement.

We appreciate the reviewer’s acknowledgement of the experimental design. We have addressed the nuance of the results by changing the title and clarifying other statements throughout the manuscript as suggested in the reviewer’s recommendations. We have also addressed reviewer comments asking for further explanation on using Fisher transformations when normalizing the Pearson correlations for branch counts.

Reviewer #3 (Public Review):

Summary:

The paper makes a convincing argument that physical interactions of proteins do not cause substantial evolutionary co-variation.

Strengths:

The presented analyses are reasonable and look correct and the conclusions make sense.

Weaknesses:

The overall problem of the analysis is that nobody who has followed the literature on evolutionary rate variation over the last 20 years would think that physical interactions are a major cause of evolutionary rate variation. First, there have been probably hundreds of studies showing that gene expression level is the primary driver of evolutionary rate variation (see, for example, [1]). The present study doesn't mention this once. People can argue the causes or the strength of the effect, but entirely ignoring this body of literature is a serious lack of scholarship. Second, interacting proteins will likely be co-expressed, so the obvious null hypothesis would be to ask whether their observed rates are higher or lower than expected given their respective gene expression levels. Third, protein-protein interfaces exert a relatively weak selection pressure so I wouldn't expect them to play much role in the overall evolutionary rate of a protein.

We thank the reviewer for their comments and suggestions. A point to immediately clarify is that the methods studied in this manuscript deal with rate variation of individual proteins over time, and if that variation correlates with that of another protein.. The numerous studies the reviewer refers to deal with explaining the differences in average rate between proteins. These are different sources of variation. It has not, to our knowledge, been shown that variation in the expression level of a single protein over time is responsible for its variation in evolutionary rate over time, let alone to a degree that allows its variation to correlate with that of a functionally related protein. That question interests us, but it is not the focus of this study.

In our study, we sought to test for a contribution of physical interaction to the correlation of evolutionary rate changes as they vary over time, i.e. between branches. We made many changes to clarify this distinction in our revisions.

We agree that the manuscript would be more clear to define the forces proposed to lead to difference in rate in general, which includes expression levels. We had generally considered expression level as one of the many potential non-physical forces, but failed to make that explicit and instead focused on selection pressure. In our revision we describe expression level as another potential driver of evolutionary rate variation over time. References to previous literature have been made in the introduction. We also added a more explicit explanation of the rate covariation over time that we are measuring in contrast with the association between expression level and rate differences between proteins that was studied in previous literature.

On point 3, the authors seem confused though, as they claim a co-evolving interface would evolve faster than the rest of the protein (Figure 1, caption). Instead, the observation is they evolve slower (see, for example, [2]). This makes sense: A binding interface adds additional constraint that reduces the rate at which mutations accumulate. However, the effect is rather weak.

The values in Fig 1B are a measure of correlation, specifically a Fisher transformed correlation coefficient. They are not evolutionary rates, so they are not reflecting faster or slower evolution, rather more or less covariation of evolutionary rates over time. We are not predicting that physically interacting interfaces evolve faster than the rest of the protein, but rather that if physical interaction drives covariation in evolutionary rates over time, their correlation would be stronger between pairs of physically interacting domains. In response, we have used clearer language in the figure caption and reorganized labels in Figure 1B to clearly show that the values are correlations. Revised Figure 1 Legend:

“Overview of experimental schema and hypotheses. Proteins that share functional/physical relationships have similar relative rates of evolution across the phylogeny, as shown in (A) with SMC5 and SMC6. The color scale along the bottom indicates the relative evolutionary rate (RER) of the specific protein for that species compared to the genome-wide average. A higher (red) RER indicates that the protein is evolving at a faster rate than the genome average for that branch. Conversely, a lower (blue) RER indicates that protein is evolving at a slower rate than the genome average. The ERC (right) is a Pearson correlation of the RERs for each shared branch of the gene pair. (B) Suppose the correlation in relative evolutionary rates between two proteins is due to compensatory coevolution and physical interactions. In that case, the correlation of their rates (ie. ERC value) would be higher for just the amino acids in the physically interacting domain. (C) Outline of experimental design. Created with Biorender.com”

All in all, I'm fine with the analysis the authors perform, and I think the conclusions make sense, but the authors have to put some serious effort into reading the relevant literature and then reassess whether they are actually asking a meaningful question and, if so, whether they're doing the best analysis they could do or whether alternative hypotheses or analyses would make more sense.

[1] https://www.ncbi.nlm.nih.gov/pmc/articles/PMC4523088/

[2] https://www.ncbi.nlm.nih.gov/pmc/articles/PMC4854464/

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Major comments

(1) Numerous parameters influence ECR calculation. The authors note that their use of a large dataset of budding yeast provides sufficient statistical power to calculate ECR. I agree with that. However, a discussion of other parameters needs to be improved, especially when comparing the present study to others like Kann et al., Hakes et al., and Jothi et al.. For example, what is the evolutionary breadth and depth used in the Kann, Hakes, Jothi and other studies? How does that compare to the present study? Budding yeast evolve rapidly with gene presence/absence polymorphisms observed in genes otherwise considered universally conserved. Is there any reason to expect different results in a younger, slower-evolving clade such as mammals? There is potential to acknowledge and discuss other parameters that may influence ECR, such as codon optimization and gene/complex "essentiality," among others.

More discussion of these parameters is a good idea. We have added the number and phylogeny of species used in the previous studies in the discussion paragraph starting with “Previous studies attributed varying degrees of evolutionary rate covariation signal to physical interactions between proteins.” We also like the idea of studying the effect of younger and more slowly evolving clades as opposed to the contrary, but currently we lack the required number of datasets to do this.

We have also added more discussion and clarification of potential non-physical forces leading to ERC correlations in the introduction.

Minor comments

(1) It would be good to add a citation to the second sentence of the first paragraph, which reads, "It has been observed that some genes have rates that covary with those of other genes and that they tend to be functionally related."

Added citation to Clark et al. 2012

(2) In the last sentence of the first paragraph of the introduction, ERC is discussed in the context of only amino acid divergence, however, there is no reason that DNA sequences can't be used, especially if ERC is being calculated among species that are less ancient than, for example, Saccharomycotina yeasts. Thus, it may be more accurate to suggest that ERC measures how correlated branch-specific rates of sequence divergence are with those of another gene.

Nice suggestion to generalize. We have made this change.

(3) ERC was not calculated in reference #2. For the sentence "Protein pairs that have high ERC values (i.e., high rate covariation) are often found to participate in shared cellular functions, such as in a metabolic pathway2 or meiosis3 or being in a protein complex together," I think more appropriate citations (including inspiring work by the corresponding author) would be

a) Coevolution of Interacting Fertilization Proteins (https://journals.plos.org/plosgenetics/article?id=10.1371/journal.pgen.1000570)

b) Evolutionary rate covariation analysis of E-cadherin identifies Raskol as a regulator of cell adhesion and actin dynamics in Drosophila (https://journals.plos.org/plosgenetics/article?id=10.1371/journal.pgen.1007720)

c) An orthologous gene coevolution network provides insight into eukaryotic cellular and genomic structure and function (https://www.science.org/doi/10.1126/sciadv.abn0105)

d) PhyKIT: a broadly applicable UNIX shell toolkit for processing and analyzing phylogenomic data (https://academic.oup.com/bioinformatics/article/37/16/2325/6131675)

Thank you for pointing out these works. We agree that there are more appropriate citations and we have referenced your suggested b-d.

(4) The dataset of 343 yeast species also includes outgroup taxa. Therefore, indicating that 332 species are Saccharomycotina yeast and 11 are closely related outgroup taxa may be more accurate.

Thank you for the suggestion, the following sentence has been added, citing the Shen et. al 2018 paper that the dataset was derived from:

“To investigate the discrepancy between contributions to ERC signal from co-function and physical interaction, we used a dataset of 343 evolutionarily distant yeast species. 332 of the species are Saccharomycotina with 11 closely related outgroup species providing as much evolutionary divergence as humans to roundworms3”

(5) Are there statistics/figures to support the claim that "Almost all complexes and pathways had mean ERC values significantly greater than a null distribution consisting of random protein pairs"?

This is shown in supplementary figure 1. A reference to this figure was added as well as quantification within the text.

(6)Similar to the previous comment, can quantitative values be added to the statement "While protein complexes appear to have higher mean ERC scores than the pathways..."?

The median of the mean ERC scores for protein complexes is 5.366 while the median for the mean ERC score in pathways is 4.597. This quantification has been included in the text: “While protein complexes have higher mean ERC scores (median 5.366) than the pathways (median 4.597), the members of a given complex are also co-functional, making interpretation of the relative contribution of physical interactions to the average ERC score difficult”

These quantifications are were also added to the figure caption for figure 2A

(7) A semantic point: In the sentence "The lack of significance in the global permutation test shows that the...", I recommend saying that the analysis suggests, not shows, because there is potential for a type II error.

Good suggestion, we have made this change.

(8) The authors suggest that shared evolutionary pressures, "and hence shared levels of constraint," drive signatures of coevolution. The manuscript does not delve into selection measures (e.g., dN/dS). Perhaps it would be more representative to remove any implication of selection.

We have added better language to clarify that discussion of selection is purely a hypothesis and that selection is not probed in our analyses.

“Previous work finds evidence that relaxation of selective constraint can lead to drastic rate variation and hence covariation6. Rather, the greater and consistent contribution comes from non-physical interaction drivers that could include variation in essentiality, expression level, codon adaptation, and network connectivity. These non-physical forces would be under shared selective pressures and hence shared levels of constraint, the result of which was elevated ERC between non-interacting proteins, as visible in our study of genetic pathways that do not physically interact (Figure 2).”

Reviewer #2 (Recommendations For The Authors):

Major comments:

-Title: In my opinion, the title of the manuscript is a somewhat misleading summary of the results of this paper. In the majority of the analyses in this paper, physical interactions do account for a significantly outsized portion of the ERC signature. The current title downplays the consistent (although sometimes small effect-sized) result that physically interacting domains do show higher ERC than non-physically interacting domains by every statistical measure employed in this paper to compare physical vs non-physical interactions. The authors' interpretation of their results within the manuscript body is that the effect of physical interactions is an inconsistent, weak, and non-generalizable driver of ERC. I generally agree with the authors' interpretations, but the nuance of these interpretations is lost in the title of the paper. I would suggest rewording the title to try to capture the nuance or at least be subjectively accurate. For example, stating that "...physical interactions are not the sole driving force.." is inarguably accurate based on these results.

As an alternative title, I would suggest focusing on an important takeaway from the paper: ERC is a reliable predictor of co-functional interactions but not necessarily physical interactions. I agree with the statement that "there is not a strong enough signal to confidently call an interaction physical or not and would be of little value to an experimentalist wanting to infer interacting domains" and I think that a title that emphasizes this idea would be more accurate and impactful.

Great suggestion. We agree that the current title is downplaying the minutiae of the method and the signal we capture with it, we have used your suggested title.

There are an outsized number of complexes that had ROC-AUCs greater than 0.5 which is why we performed the permutation tests to determine how significant each of the individual ROC-AUCs were given the differing number of protein/domain pairs in each complex. Between the statistical methods used only 3 of the 17 complexes ranked physical interactions significantly higher than non-physically interacting domains in every analysis. Even among the 3 that were statistically significant some of the physically interacting domains still fell among the bottom portion of the ERC scores for that complex (Figure 5: MCM and CUL8 complexes) This is why we concluded that physical interactions are not the sole driving force of the signal captured by ERC.

-Abstract: related to my preceding comment, the word "negligible" in the abstract is misleading. If physical interactions were truly entirely negligible, the comparisons of physically interacting vs non-physically interacting domains would yield 0.5. Instead, these comparisons always yielded results greater than 0.5. Consider rewording.

Thank you for the suggestion this phrasing has been changed to “Therefore, we conclude that coevolution due to physical interaction is weak, but present in the signal captured by ERC”

We agree that “negligible” may be too strong of a word, however, the comparisons do not always yield results greater than 0.5.

5 of the 17 complexes do not reach the 0.5 threshold for the initial ROC analysis and even among those that do, only 4 had significantly high ROC-AUCs. You are correct that the signal is not completely negligible which is why we continued by determining if the physical interaction was driving high ERC only within proteins (Figure 5)

-Figure 3: I think there may be an error in the domain labeling in Figure 3. The comparison between OKP1_2 and AME1_3 is the highest ERC value in the matrix. From the complex structure, it appears that OKP1_2 and AME1_3 are two helix domains that appear to physically interact. However, in the ERC matrix, they are not shaded to indicate they are a physical interaction pair. Please double-check that the interacting domains are properly annotated, since mis-annotation would have a large impact on the interpretation of this figure with respect to the overall question the paper addresses.

Thank you for catching this - fixed.

Minor comments:

-Methods: "The full ERC pipeline can be found at (Github)." Provide github URL here? Thanks for the catch, fixed

-Discussion: "Evidence for physical coevolution however was tempered by a global permutation test, which did not reach significance, indicating that this inference is sensitive to approach and further underlines the relatively weak contribution of physical coevolution." The word "relatively" may not be a good choice of words. In comparison to what? As is, the phrasing could be interpreted as implying "in comparison to non-physical interactions". This would not be accurate, because the results show that in general, physical interactions are a stronger contributor to ERC (consistent trend but varied significance, depending on methodology) than non-physical interactions.

Thank you for your help with clarification. The word relatively was removed.

However, we do not agree that in general physical interactions are a stronger contributor to ERC than non-physical interactions (such as gene expression, codon adaptation, etc.). In all of our statistical tests a maximum of 5 of the 17 complexes ranked physical interactions significantly higher than non-physical interactions. While the ROC-AUC is greater than 0.5 for 12 of the 17 complexes only 4 of those were significant.

-I have not seen Fisher-transformed correlation coefficients used in the context of ERC. I understand that it's helpful in normalizing the results so that they are comparable between ERC comparisons with differing numbers of overlapping branches (i.e. points on a linear correlation plot). A reference of where the authors got this idea or a little more verbiage to describe the rationale would be helpful. On a related note, I would expect that using linear correlation p-value instead of R-squared would account for differences in overlapping branches, eliminating the need to apply fisher-transformation. It would be helpful for the authors to outline their rationale for using a correlation coefficient rather than a P-value.

We agree that this method could be made clearer. We made a methodological choice to use Fisher transformation over linear correlation p-value. Both methods should achieve the same end result by taking the number of branches into consideration. We have added additional explanation to the results section “Both protein pathways and complexes have elevated ERC”:

“ERC was calculated for all pairs of the 12,552 genes. For each pair the correlation is Fisher transformed to normalize for the number of shared branches that contribute to the correlation. This normalization is necessary to reduce false positives that have high correlation solely due to a small number of data points. This normalization also allows for direct comparison of ERC between gene pairs that have differing numbers of branches contributing to the score.”

We also added additional explanation in the methods section including the formula used to calculate the Fisher transformation

-Did the authors use Pearson or Spearman correlation coefficient?

Pearson. We clarified this in the methods section, “Calculating evolutionary rate covariation” : “Evolutionary rate covariation is calculated by correlating relative evolutionary rates (RERs) between two gene trees using a Pearson correlation.”

-Did the authors explore ERC between domains within a single protein? Do domains within a protein exhibit ERC? I would expect that they do. If they do, this could likely be attributed to linkage/genetic hitchhiking, representing a new angle/factor beyond physical interaction that could lead to ERC. This is just an idea for a future analysis, not necessarily a request within the scope of the present paper.

We did calculate the ERC between domains of a single protein but did not include them in the analysis since they didn’t address the specific question we posed. As expected they are highly correlated, and past unpublished studies in the lab do find a very weak, but detectable genome-wide, signature of rate covariation between neighboring colinear genes on a chromosome. That signal was however so weak as to be eclipsed by true functional relationships, when present.

Reviewer #3 (Recommendations For The Authors):

Please read the literature and revise accordingly.

We understand the confusion surrounding previous literature on the relationship between expression levels and evolutionary rates when comparing between different proteins. Those studies clearly showed how expression level is highly predictive of a given protein’s average evolutionary rate. However, we are studying the change in evolutionary rate over branches for single proteins. This is inherently different because we’re following rate fluctuations in the same protein over time. To our knowledge it has not yet been shown that expression level commonly varies enough over time to produce large rate variations over time in the same protein, and if it is responsible for the correlations of rate we observe between co-functional proteins. It is however reasonable to expect that what governs between-protein differences in rate could also contribute to between-branch differences (over time for a single protein). In fact, our earlier study approached this (Clark et al. Genome Research 2012). We expect expression level could influence rate over time and lump its effect together with general non-physical forces, such as selection pressures. We recognize we could do better in defining more of the non-physical forces and the past literature. We added the following section to the introduction and many other clarifying statements throughout the manuscript:

“For the purposes of this study, the forces that contribute to correlated evolutionary rates are grouped into two bins, physical and non-physical. The physical force is coevolution occurring at physical interaction interfaces. Non-physical forces include gene co-expression, codon adaptation, selective pressures, and gene essentiality. There is a well accepted negative relationship between gene expression and rate of protein evolution where genes that are highly expressed generally have slower rates of evolution14,15. However, Cope et al.16 found that there is a weak relationship between both gene expression and the number of interactions a protein has with the coevolution of expression level. Conversely, they found a strong relationship between proteins that physically interact and the coevolution of gene expression. These findings illuminate the difference between the strong relationship of gene expression level on the average evolutionary rate of a protein and the weak contribution of gene expression level to correlated evolutionary rates of proteins across branches. The finding that physically interacting proteins have strong expression level coevolution brings to question how much coevolution of physically interacting proteins contributes to overall covariation in protein evolutionary rates.”

Author Response

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

eLife assessment

This manuscript provides novel and important findings regarding the impact of noradrenergic signaling from the locus coeruleus on hippocampal gene expression. The locus coeruleus is the sole source of noradrenaline to the hippocampus and many rapid molecular changes induced by stress are regulated by noradrenaline. This manuscript provides a rigorous investigation into hippocampal genes uniquely regulated by noradrenaline in the presence or absence of stress. Data were collected and analyses were performed using solid methodology, and the results mostly convincingly support the conclusion made with few weaknesses. The study would benefit from a more comprehensive analyses of sex differences.

Response: We thank the reviewers and the editors for the positive evaluation of our work and for the constructive feedback. To address some of the key criticisms, we have performed several new experiments and analyses. Importantly, we now provide a much more rigorous comparison of males and females, which strongly suggests that there are no major sex differences in the transcriptomic response to stress and noradrenaline in the hippocampus. We think that these - and other additions discussed below - significantly strengthen the manuscript. We provide detailed responses to all the reviewers comments. We have added numbers to the reviewers’ comments for easier referencing.

Reviewer #1 (Public Review):

Comment 1: Privitera et al., provide a comprehensive and rigorous assessment of how noradrenaline (NA) inputs from the locus coeruleus (LC) to the hippocampus regulate stress-induced acute changes in gene expression. They utilize RNA-sequencing with selective activation/inhibition of LC-NA activity using pharmacological, chemogenetic and optogenetic manipulations to identify a great number of reproducible sets of genes impacted by LC activation. It is noteworthy that this study compares transcriptomic changes in the hippocampus induced by stress alone, as compared with selective circuit activation/inhibition. This reveals a small set of genes that were found to be highly reproducible. Further, the publicly available data will be highly useful to the scientific community.

Response: We are very grateful for this positive evaluation.

Comment 2: A major strength of the study is the inclusion of both males and females. However, with this aspect of the study also lies the biggest weakness. While the experiments tested males and females, they were not powered for identifying sex differences. There are vast amounts of literature documenting the inherent sex differences, both under resting and stress-evoked conditions, in the LC-NA system and this is a major missed opportunity to better understand if there is an impact of these sex-specific differences at the genetic level in a major LC projection region. There are many instances whereby sex effects are apparent, but do not pass multiple testing correction due to low n's. The authors highlight one of them (Ctla2b) in supplemental figure 6. This gene is only upregulated by stress in females. It is appreciated that the manuscript provides an incredible amount of novel data, making the investigation of sex differences ambitious. Data are publicly available for others to conduct follow up work, and therefore it may be useful if a list of those genes that were different based on targeted interrogation of the dataset be provided with a clear statement that multiple testing corrections failed. This will aid further investigations that are powered to evaluate sex effects.

Response: The assessment of the reviewers and the editorial feedback encouraged us to look more thoroughly into potential sex differences, because we believe it would indeed be a major additional strength if our manuscript could make a firm statement on this important issue. To this end, we have expanded the manuscript in two major ways:

(1) To expand the analysis of sex effects also to the dorsal hippocampus, and to increase robustness of the data, we have performed RNA-seq in 32 additional samples of male and female mice exposed to stress (or control) and propranolol (or saline) injection. Figure 1fh and Supplementary Figure 1d-f have been updated to reflect this new addition, and the results are presented in a new section on Pages 3-4 (pasted below for ease of reviewing). In summary, the strongly support our initial observation that the effects of stress on gene expression, as well as the effects of propranolol on blocking stress-induced effects, are highly similar in both sexes.

(2) To further increase the power for detection of sex-effects, we have performed a small meta-analysis. For this, we combined several RNAseq datasets from the current manuscript and published datasets from our previous work (Floriou-Servou et al., 2018; von Ziegler et al., 2022), which also investigated transcriptomic sex-differences in the hippocampus 45 min after cold swim stress exposure in the same setup as used for the current manuscript. This approach increased our sample size to 51 males and 20 females. In summary, this well-powered approach shows no evidence for sex differences in the transcriptional response to stress, even when more lenient analyses were applied. These results are described in a new section on page 4, and summarized in Supplementary Figures 1f+g. This section is pasted below for ease of reviewing.

"While blocking β-adrenergic receptors was able to block stress-induced gene expression, we did not test whether propranolol might decrease gene expression already at baseline, independent of stress. Additionally, all tests had thus far been conducted in male mice, raising the question about potential sex differences in NA-mediated transcriptomic responses. To address these two issues, we repeated the experiment in both sexes and included a group that received a propranolol injection but was not exposed to stress (Fig. 1f). Combining the data from both experiments, we repeated the analysis for each region, to identify genes whose response to stress was inhibited by propranolol (Figure 1g). As in the previous experiment, we found that many of the stress-induced gene expression changes were blocked by propranolol injection in both dHC (Figure 1g, left panel) and vHC (Figure 1g, right panel). Importantly, propranolol did not change the expression level of these genes in the absence of stress. We then directly compared the genes sensitive to stress and propranolol treatment in both dHC and vHC. To this end, we plotted the union of genes showing a significant stress:propranolol interaction in either region in one heatmap across both dHC and vHC (Supplementary Figure 1d). This showed again that the stress-induced changes were very similar in dHC and vHC, and that propranolol similarly blocked many of them. Finally, we asked whether the response differs between males and females. Despite clear sex differences in gene expression at baseline (data not shown), we found no significant sex differences in response to stress or propranolol between male and female mice (FDR<0.05; Fig. 1g). To more directly visualize this, we compared females and males by plotting the log2-fold changes of the stress:propranolol interaction across all stress-induced genes that were blocked by propranolol. We find very similar regulation patterns in both sexes (Figure 1h). Although none of these sex differences are significant, some genes seem to show quantitative differences, so we plotted the expression patterns of the 5 genes showing the largest difference in interaction term as box-plots, which suggest that these spurious differences are likely due to noisy coefficient estimates (Supplementary Fig. 1e). To address concerns that our analysis of sex differences might not have been sufficiently powered, we performed a meta-analysis of the experiments shown here along with previously published datasets from our lab (Floriou-Servou et al. 2018; von Ziegler et al. 2022). In all these experiments, the vHC of male and female mice was profiled 45 min after exposure to an acute swim stress challenge. This resulted in a sample size of 51 males and 20 females. Despite this high number of independent samples, we could not identify any statistically significant interaction between sex and the stress response. To identify candidates that might not reach significance while discounting differences due to noise in fold-change estimates, we reproduced the same analysis using DESeq2 with Approximate Posterior Estimation for generalized linear model (apeglm) logFC shrinkage (A. Zhu, Ibrahim, and Love 2018). This analysis also did not reveal any sex differences in the stress response (Supplementary Fig. 1f). We then tailored the meta-analysis specifically to the set of stress-responsive genes that were blocked by propranolol, and also for these genes the response to stress was strikingly similar in both sexes (Supplementary Fig. 1g). Altogether, we conclude that there are no major sex differences in the rapid transcriptomic stress response in the hippocampus, and that blocking beta-receptors prevents a large set of stress-induced genes in both females and males."

To put these findings in context with existing literature, we agree with the reviewer that there are many studies that have reported sex differences in the LC-circuitry as summarized by Bangasser and colleagues (Bangasser et al., 2016, 2019). However, these studies primarily focus on the LC itself, suggesting that female rats have more LC neurons, denser LC-dendrites in the peri-LC region, and that LC neurons are more readily activated by stress in females because of heightened sensitivity to CRF-signaling. A recent study in mice reports, in contrast, that females have fewer TH-positive neurons in the LC, but they also find enhanced excitability of LC neurons in females (Mariscal et al., 2023). Similarly, one study has suggested molecular differences in the makeup of the LC (Mulvey et al., 2018). Our experiments, however, focus on the impact of NA release in a projection region (hippocampus). Further, we use a strong stress induction protocol (swim stress) and various potent modes of direct LC activation, so differences in "LC-excitability" are likely less relevant in this context. We added evidence showing that we trigger powerful NA release in both sexes (Supplementary Figure 2c-h; see response to Reviewer #2, Comment #3 for more details). In addition, we show that the intensity or pattern of LC stimulation does not appear to alter the molecular response (Figure 3a-b), and that various stressors (mild or intense) all trigger the same NA-dependent molecular changes (Figure 4a-b). Therefore, our results suggest that once NA is released (in the hippocampus), the molecular downstream effects on gene expression are very similar - independent of stimulation intensity, sex, or hippocampal subregion (dorsal/ventral). This does not mean that there are no sex differences for activation of LC, but rather that the transcriptional response to NA release in the hippocampus is robust across sexes, and that propranolol seems to block NA-dependent effects similarly in both sexes. This does not rule out quantitative differences between sexes that only emerge with targeted analyses of individual genes, or once fluctuations in ovarian hormones are taken into account. We have updated the section in the discussion to summarize these considerations in light of the new results (see pages 20-21, section: "A uniform molecular response to stress and noradrenaline release in both sexes").

Comment 3: A major finding of the present study is the involvement of noradrenergic transcriptomic changes occurring in astrocytic genes in the hippocampus. Given the stated importance of this finding within the discussion, it seems that some additional dialogue integrating this with current literature about the role of astrocytes in the hippocampus during stress or fear memory would be important.

Response: We thank the reviewer for giving us an opportunity to add a more detailed discussion about the role of astrocytes and thyroid hormones in the hippocampus during learning and memory formation. We have added these statements to the discussion:

“Within the hippocampus, astrocytic pathways are emerging as important players for learning and memory processes (Gibbs, Hutchinson, and Hertz 2008; Bohmbach et al. 2022). In fact, it is well-known that NA enhances memory consolidation (Schwabe et al. 2022; McGaugh and Roozendaal 2002), and recent work suggests that these effects are mediated by astrocytic β-adrenergic receptors (Gao et al. 2016; Iqbal et al. 2023). Our transcriptomic screens revealed Dio2 as the most prominent target influenced by LC activity. Dio2 is selectively expressed in astrocytes and encodes for the intracellular type II iodothyronine deiodinase, which converts thyroxine (T4) to the bioactive thyroid hormone 3,3',5-triiodothyronine (T3) and therefore regulates the local availability of T3 in the brain (Bianco et al. 2019). Enzymatic activity of DIO2 has further been shown to be increased by prolonged noradrenergic transmission through desipramine treatment in LC projection areas (Campos-Barros et al. 1994). This suggests that the LC-NA system and its widespread projections could act as a major regulator of brain-derived T3. Notably, T3-signaling plays a role in hippocampal memory formation (Rivas and Naranjo 2007; Sui et al. 2006), raising the possibility that NA-induced Dio2 activity in astrocytes might mediate some of these effects.”

Comment 4: The comparison of the candidate genes activated by the LC in the present study (swim) with datasets published by Floriou-Servou et al., 2018 (Novelty, swim, restraint, and footshock) is an interesting and important comparison. Were there other stressors identified in this paper or other publications that do not regulate these candidate genes? Further, can references be added to clarify to the reader, that prior studies have identified that novelty, restraint and footshock all activate LC-NA neurons.

ponse: Thank you for the positive feedback. We have only tested the stressors reported in Figure 4a-b (novelty, swim, restraint, and footshock). It is known that all these stressors trigger noradrenaline release, in fact we are not aware of stressors that do not trigger NA release. This reproducible finding supports the notion that the identified set of genes is indeed highly NAresponsive. As suggested, we have now included references that show increased NA release in response to all these stressors:

“Therefore, we assessed their expression in a dataset comparing the effect of various stressors on the hippocampal transcriptome (Floriou-Servou et al., 2018). The stressors included restraint, novelty and footshock stress, which have all previously been shown to increase hippocampal NA release (HajósKorcsok et al., 2003; Lima et al., 2019; Masatoshi Tanaka et al., 1982).”

Comment 5: Comparisons are made between chemogenetic studies and yohimbine, stating that fewer genes were activated by chemogenetic activation of LC neurons. There is clear justification for why this may occur, but a caveat may need to be mentioned, that evidence of neuronal activation in the LC by each of these methods were conducted at 90 (yohimbine) versus 45 (hM3Dq) minutes, and therefore it cannot be ruled out that differences in LC-NA activity levels might also contribute.

Response: The reviewer raises an important point about some inconsistencies between the time points chosen in our study, an aspect that was also pointed out by Reviewer #2. We have chosen the 45 and 90 min time points for two different reasons. On the one hand, cFos changes on the protein level are known to peak 90 min after neuronal activation, and we wanted to capture the strongest possible cFos signal in the LC. On the other hand, we wanted to measure gene expression changes triggered by NA release, which already occur 45 min after noradrenergic activation (Roszkowski et al., 2016). Thus, when the experimental design allowed separate experiments (e.g. systemic yohimbine injection), we chose to measure gene expression after 45 min, but to validate cFos activation in the LC separately after 90min. In response to DREADD activation, however, we wanted to confirm within the same animal that LC activation was successful, and thus we collected LC and hippocampus simultaneously (Figure 2c,d). While the cFos increase is already very pronounced at the 45min time point (Figure 2g), the quality of IHC is slightly lower because the tissue cannot be perfused in this experimental design. Therefore, we do not think that the time point for cFos sampling matters in this context. However, we agree with the reviewer that it remains unclear whether yohimbine and DREADDs activate the LC with similar potency. To directly compare NA release would require a set of photometry-based experiments to measure NA release using genetically-encoded NA-sensors. While we have added such experiments for LC activation with DREADDs and optogenetics to show rapid NA release indeed occurs in the hippocampus (see Reviewer #2, Comment 3; Supplementary Figure 2c-h), yohimbine interferes with the NA-sensors as explained in detail in response to Reviewer 2, Comment 3. Thus, it was too challenging for us to directly compare the release dynamics in response to DREADDs and yohimbine, which was also not the main focus of our work. To explicitly address this caveat, we have extended the corresponding section in the discussion:

"Finally, our observation that systemic administration of the α2-adrenergic receptor antagonist yohimbine very closely recapitulates the transcriptional response to stress stands in contrast to the much more selective transcriptional changes observed after chemogenetic or optogenetic LC-NA activation. This difference could be due to various factors. First, it remains unclear how strong the LC gets activated by yohimbine versus hM3Dq-DREADDs. However, given the potent LC activation observed after DREADD activation, it seems unlikely that yohimbine would lead to a more pronounced LC activation, thus explaining the stronger transcriptional effects. Second, contrary to LC-specific DREADD-activation, systemic yohimbine injection will also antagonize postsynaptic α2-adrenergic receptors throughout the brain (and periphery). More research is needed to determine whether this could have a more widespread impact on the hippocampus (and other brain regions) than isolated LC-NA activation, further enhancing excitability by preventing α2-mediated inhibition of cAMP production. Finally, systemic yohimbine administration and noradrenergic activity have been shown to induce corticosterone release into the blood (Johnston, Baldwin, and File 1988; Leibowitz et al. 1988; Fink 2016). Thus, yohimbine injection could have broader transcriptional consequences, including corticosteroid-mediated effects on gene expression."

Comment 6: Please add information about how virus or cannula placement was confirmed in these studies. Were missed placements also analyzed separately?

Response: Pupillometry recordings were performed with all animals involving optogenetic or chemogenetic manipulations of the LC, before subjecting them to stress experiments. These assessments account for both correct optic fiber placement and virus expression (Privitera et al., 2020). If an animal did not show a clear pupil response, it was not included any further in the study. To demonstrate correct cannula placement for drug infusion of isoprotenerol in the dorsal hippocampus, we added a representative image of cannula placement in Supplementary Figure 1h.

Comment 7: Time of day for tissue collection used in genetic analysis should be reported for all studies conducted or reanalyzed.

Response: Thank you for pointing out this omission. Tissue collection for RNA-seq analysis was always performed between 11am and 5pm during the dark phase of the reversed light-dark cycle. We have added this information to the corresponding method section (“Tissue collection”).

Reviewer #1 (Recommendations For The Authors):

Comment 8: This is a well written, comprehensive and rigorous manuscript that will be of great interest to those in the scientific community.

Response: Thank you for the positive evaluation of our work and for the constructive feedback.

Reviewer #2 (Public Review):

Comment 1: The present manuscript investigates the implication of locus coeruleus-noradrenaline system in the stress-induced transcriptional changes of dorsal and ventral hippocampus, combining pharmacological, chemogenetic, and optogenetic techniques. Authors have revealed that stress-induced release of noradrenaline from locus coeruleus plays a modulatory role in the expression of a large scale of genes in both ventral and dorsal hippocampus through activation of β-adrenoreceptors. Similar transcriptional responses were observed after optogenetic and chemogenetic stimulation of locus coeruleus. Among all the genes analysed, authors identified the most affected ones in response to locus coeruleus-noradrenaline stimulation as being Dio2, Ppp1r3c, Ppp1r3g, Sik1, and Nr4a1. By comparing their transcriptomic data with publicly available datasets, authors revealed that these genes were upregulated upon exposure to different stressors. Additionally, authors found that upregulation of Ppp1r3c, Ppp1r3g, and Dio2 genes following swim stress was sustained from 90 min up to 2-4 hours after stress and that it was predominantly restricted to hippocampal astrocytes, while Sik1 and Nr4a1 genes showed a broader cellular expression and a sharp rise and fall in expression, within 90 min of stress onset.

Overall, the paper is well written and provides a useful inventory of dorsal and ventral hippocampal gene expression upregulated by activation of LC-NA system, which can be used as starting point for more functional studies related to the effects of stress-induced physiological and pathological changes.

Response: We thank the reviewer for the careful assessment of our work.

Comment 2: However, I believe that the study would have benefited of a more comprehensive analyses of sex differences. Experiments in females were conducted only in one experiment and analyses restricted to the ventral hippocampus.

Response: In response to the comments by the reviewer, as well as Reviewer #1 and the editors, we have sequenced an additional 32 brain samples to expand the comparison of sex effects in females and males across dorsal and ventral hippocampus, and we included a new meta-analysis of 3 experimental datasets (51 male and 20 female) samples, to thoroughly assess sex differences in the transcriptomic response to stress. We refer the reviewer to our detailed response provided above to Reviewer #1, comment #2, and the updated results section on pages 3-4.

Comment 3: Although, the experiments were overall sound and the results broadly support the conclusion made, I think some methodological choices should be better explained and rationalized. For instance, the study focuses on identifying transcriptional changes in the hippocampus induced by stress-mediated activation of the LC-NA system, however NA release following stress exposure and pharmacological or optogenetic manipulation was mostly measured in the cortex.

Response: Because the hippocampus was used for RNA-sequencing, we could not assess NA release in the hippocampus (as this would require fiber implants that would interfere with molecular measures, or different tissue processing for HPLC). Nonetheless, we wanted to assess the transcriptional changes in the hippocampus, while simultaneously measuring successful stimulation of the LC-NA system in the same animals. To achieve this, we pursued 3 routes: 1) we used pupillometry to confirm functional LC activation; 2) we measured cFOS in the LC to directly demonstrate LC activation; 3) we assessed NA release using uHPLC (which requires larger tissue samples) and we chose the cortex because both cortex and hippocampus receive NA predominantly from the LC (Samuels & Szabadi, 2008). Importantly, we had previously shown that chemogenetic LC activation leads to a similar NA turnover in both the cortex and hippocampus, as measured by uHPLC (Zerbi et al., 2019). The relevant figure from that paper is inserted below to quickly show the striking similarity between hippocampus and cortex.

Author response image 1.

Levels of noradrenaline (NE) turnover (MHPG/NE ratio) in the cortex (CTX) and hippocampus (HC), measured in whole tissue with uHPLC 90min after hM3Dq-DREADD activation of the LC (copied and cropped from Zerbi et al, 2019, Neuron).

In response to the reviewers comment, we performed additional experiments to directly demonstrate that LC-activation with DREADDs as well as optogenetics causes an increase in hippocampal NA-release. We recorded NA release in the hippocampus (using fiber photometry combined with genetically encoded NA sensors). For DREADD activation, we observed a strong increase in hippocampal noradrenaline that started a few minutes after clozapine administration, and this increase was sustained throughout the duration of the 21 minute recording (see Supplementary Figure2c-e). For optogenetic LC activation, we find a rapid and immediate sharp increase in NA levels in the hippocampus (Supplementary Figure 2f-h). These experiments were performed in females and males and triggered similar responses. An adapted and cropped version of Supplementary Figure 2 is pasted below for ease of reading.

Please note that we could not perform a similar experiment using yohimbine, because the GRABNE sensors are based on the alpha-2 adrenergic receptor, thus yohimbine administration interferes with the photometry recording. However, we believe that it is clear from this response that strong activation of the LC leads to uniform release of NA in the hippocampus and cortex.

Author response image 2.

c, Schematic of fiber photometry recording of hippocampal NA during chemogenetic activation of the LC. After 5 min baseline recording in the homecage animals were injected with clozapine (0.03mg/kg, i.p.) and placed in the OFT for 21min. d, Average ΔF/F traces of GRABNE2m photometry recordings in response to chemogenetic activation of the LC (mean±SEM for hM3DGq+ and hM3DGq- split into females and males, n=3/group/sex). e, Peak ΔF/F response of fiber photometry trace. f, Schematic of fiber photometry recording of hippocampal NA during optogenetic activation of the LC. Animals were lightly anesthetized (1.5% isoflurane) and recorded in a stereotaxic frame. After 1 min baseline recording, animals were stimulated three times with 5Hz for 10s (10ms pulse width, ~8mW laser power) and recorded for 2 min post-stimulation. g, Average ΔF/F traces of the NA sensors GRABNE1m and nLightG in response to optogenetic activation of the LC (mean±SEM for females and males, n(females)= 10, n(males)=5. h, Peak ΔF/F response of fiber photometry trace.

Comment 4: Furthermore, behavioral changes following systemic pharmacologic or chemogenetic manipulation were observed in the open field task immediately after peripheral injections of yohimbine or CNO, respectively. Is this timing sufficient for both drugs to cross the blood brain barrier and to exert behavioral effects?

Response: We have previously shown that chemogenetic activation of the LC through clozapine elicits pupil responses within 1-2 minutes after injection (Privitera et al., 2020; Zerbi et al., 2019). This indicates that clozapine rapidly crosses the blood brain barrier and affects LC activity within a few minutes after injection. Our additional experiments using genetically encoded sensors in the hippocampus show this even more directly (Supplementary Figure 2d), see also the response to Comment 3 above.

Similarly, yohimbine also rapidly crosses the blood brain barrier within the same time frame (Hubbard et al., 1988). These observations are consistent with the rapid behavioral effects that can be detected within a few minutes after injection of clozapine for LC-DREADD activation (Zerbi et al., 2019), and for yohimbine as well (von Ziegler et al., 2023). In response to another comment of this reviewer, we have also re-analyzed the behavior presented in the current manuscript in time-bins of 3 minutes, which also shows the rapid onset of effects in response to yohimbine (within the first 3 min) and DREADDs (within 6 min), see Supplementary Fig. 3.

Comment 5: Finally, the study shows that activation of noradrenergic hippocampus-projecting LC neurons is sufficient to regulate the expression of several hippocampal genes, although the necessity of these projection to induce the observed transcriptional effects has been tested to some extent through systemic blockade of beta-adrenoceptor, I believe the study would have benefited of more selective (optogenetic or chemogenetic) necessity experiments.

Response: We understand the reviewer's point that blocking the LC during stress exposure would be an interesting experiment. However, it is very hard to completely silence the LC during intense stressors. In fact, despite intense efforts, we have not been able to silence the LC during swim stress exposure using DREADDs or other chemogenetic approaches (PSAM/PSEM). We were in fact able to silence the LC with the optogenetic inhibitor JAWS (and others have reported successful LC silencing with GtACR2), but there is a major issue involving the "rebound effect", where more NA is released once the inhibition is stopped. We would thus have had to optogenetically silence the LC for 45-90 min, which would create heat artifacts, and require challenging control experiments to draw firm conclusions. Given all these issues, we reasoned that blocking adrenergic receptors is a simple and elegant solution, which provides clear evidence for the necessity of beta-adrenergic signaling.

Reviewer #2 (Recommendations For The Authors):

Major concerns:

Comment 6: The study focuses on the identification of transcriptional changes in the hippocampus induced by stress-mediated activation of the LC-NA system, however, noradrenaline release following stress exposure or yohimbine injection was measured in the cortex. Authors should consider measuring NA concentrations in the hippocampus after exposure to swim stress or administration of yohimbine, or at least explain their choice to analyse to cortex in the manuscript.

Response: We have addressed this issue in detail in Response to "Reviewer 2, Comment #3", where we provided an overview of the additional data that support our approach. As mentioned before, measuring NA release after yohimbine is not compatible with our GRABNE-photometry approach, as the GRAB-sensor is based on alpha2-adrenoceptor. Here, we would like to add that measuring NA release using photometry during swim stress is also challenging. The challenge is the vigorous movement (swimming, typically in one direction), which creates pressure on the cables/implants. We felt that overcoming these experimental challenges (setup, troubleshooting and controls) would be beyond the scope of the paper, given that it is already known that this stressor leads to strong NA release in the hippocampus. We have now included references that demonstrate that all the stressors used in our work trigger NA increase in the hippocampus (see response to Reviewer 1, Comment 3): “Therefore, we assessed their expression in a dataset comparing the effect of various stressors on the hippocampal transcriptome (Floriou-Servou et al., 2018). The stressors included restraint, novelty and footshock stress, which have all previously been shown to increase hippocampal NA release (Hajós-Korcsok et al., 2003; Lima et al., 2019; Masatoshi Tanaka et al., 1982).”

Comment 7: Concerning the experiment aimed at investigating sex differences in gene expression, it is not clear the reason why authors decided to restrict their analyses in females to the ventral hippocampal only. The explanation that in males they did not detect major differences between the dorsal and ventral hippocampus is not sufficient, because there could have been different effects in females. Therefore, the conclusion made by the authors that their "results suggest that the transcriptomic response is independent of sex" is not entirely correct, since sex differences were only evaluated in the ventral hippocampus.

Response: We appreciate the reviewer's critique. As described above, we have now also sequenced the dorsal hippocampal tissue from the propranolol experiment (males and females, 32 samples) and additionally added an extensive meta-analysis of three large datasets (n=71) to compare transcriptional sex differences in response to stress. A detailed description of these experiments and how they have extended/supported our conclusions have been provided in response to Reviewer #1, Comment #2.

Comment 8: Besides the effects on females, the same experiment examined whether propranolol by itself (in the absence of stress) would have been able to alter gene expression: such effects were not examined in the dorsal hippocampus. In contrast, in a different experiment, the effects of isoproterenol on genes expression were restricted to the dorsal hippocampus only. Furthermore, related to this latter experiment, intra-dorsal hippocampal injection of isoproterenol should presumably mimic the rise in NA observed after stress exposure, why was gene expression measured 90 min after isoproterenol central injections while in the other experiments gene expression was determined 45 min after stress, that is when authors observe the peak NA concentration?

Response: We have addressed the reviewer's critique of dorsal vs ventral hippocampus by reanalyzing 32 additional samples from dorsal hippocampus of male and female mice after propranolol (or saline) injection. Please see response to Reviewer #1, comment #2.

Regarding the time points: We have chosen the 45 and 90 min time points mainly for two reasons. First, cFos protein changes are known to be strongest 90 min after neuronal activation. Second, because we wanted to capture gene expression changes triggered by NA release, we reasoned that these effects must be fast and should thus be measured at an early transcriptional time-point (45min). However, after performing the time-course experiment after swim stress exposure (Figure 4d,c), we observed that the LC-NA-sensitive genes (e.g. Dio2 and several PP1-subunits) show the strongest changes 90 min after stress exposure. Therefore, in some of our experiments we opted to analyze gene expression changes at 90min, converging with the time-point we typically use for cFos staining. Contrary to the reviewer's statement, peak NA concentrations are not observed 45 min after the various interventions, but rather the peak in the main metabolite (MHPG) is observed then, due to the temporal dynamics of NA release and breakdown. NA release occurs immediately upon stress exposure (or direct LC activation), which we also show in the new photometry data described above. Thus, rapid NA release triggers intracellular cascades that lead to downstream transcriptional changes, which peak presumably between 4590 min later.

Comment 9: Behavioral changes following systemic pharmacologic or chemogenetic manipulation were observed in the open field task immediately after peripheral injections of yohimbine or CNO, respectively. Is this timing sufficient for both drugs to cross the blood brain barrier and to exert behavioral effects? It is also not immediately clear the reason why the open field tasks have different durations depending on the experiments, which can also impact the results. Authors might also consider to split the open field data analyses in 2 or 3 min time-bins, to allow for a better comparison across the different results.

Response: We thank the reviewer for the suggestion to plot the behavior data as time-bins. We have implemented this change for the yohimbine and DREADD experiments, and updated the corresponding figure accordingly (Supplementary Figure 3, pasted below for ease of reading). The new visualization clearly shows that yohimbine injection triggers rapid behavioral effects already in the first three minutes, whereas the LC-DREADD activation triggers behavioral changes within 3-6 minutes after injection. Thus, clear drug effects are visible in the first 10 minutes, which is comparable to the standard OFT test (10min testing) shown in response to swim stress exposure (Suppl. Figure 3a). The choice to expose mice to the OFT for 21 minutes in total was due to the fact that we based our experimental approach on the optogenetic LC-stimulation protocol first published by McCall and colleagues (McCall et al, Neuron, 2015), in which the LC is stimulated for 3 min followed by 3 min pauses (see Suppl. Figure 3d). Because of this on-off design, we decided to keep the optogenetic analysis simple and show the overall effect (Supplementary Figure 3d), particularly as we know that NA dynamics do not recover rapidly enough after 3 min continuous stimulation to justify a bin-analysis (unpublished data).

Author response image 3.

Effects of acute stress and noradrenergic stimulation on anxiety-like behaviour in the open field test. a, Stress-induced changes in the open field test 45 min after stress onset. Stressed animals show overall reductions in distance traveled (unpaired t-test; t=3.55, df=22, p=0.0018), time in center (welch unpaired t-test; t=3.50, df=13.61, p=0.0036), supported rears (unpaired t-test; t=3.39, df=22, p=0.0026) and unsupported rears (unpaired t-test; t=5.53, df=22, p = 1.47e-05) compared to controls (Control n = 12; Stress n = 12). This data have been previously published (von Ziegler et al., 2022). b, Yohimbine (3 mg/kg, i.p.) injected animals show reduced distance traveled (unpaired t-test; t=2.39, df=10, p=0.03772), reduced supported rears (unpaired t-test; t=6.56, df=10, p=0.00006) and reduced unsupported rears (welch unpaired t-test; t=3.69, df=4.4, p = 0.01785) compared to vehicle injected animals (Vehicle n = 6; Yohimbine n = 7). c, Chemogenetic LC activation induced changes in the open field test immediately after clozapine (0.03 mg/kg, i.p.) injection. hM3Dq+ animals show reduced distance traveled (unpaired t-test; t=6.28, df=13, p=0.00003), reduced supported rears (unpaired t-test; t=4.28, df=13, p=0.0009), as well as reduced unsupported rears (welch unpaired t-test; t=4.28, df=13, p = 0.00437) compared to hM3D- animals (hM3Dq- n = 7; hM3Dq+ n = 8). d, Optogenetic 5 Hz LC activation induced changes during the open field test. ChR2+ animals show reduced supported rears (unpaired t-test; t=2.42, df=64, p=0.0185) and reduced unsupported rears (unpaired ttest; t=2.91, df=64, p = 0.00499) compared to ChR2- animals (ChR2- n = 32; ChR2+ n = 36). Data expressed as mean ± SEM. p < 0.05, p < 0.01, p < 0.001, **p < 0.0001.

Comment 9: The study shows that activation of noradrenergic hippocampus-projecting LC neurons is sufficient to regulate the expression of several hippocampal genes. I believe the study would have benefited of more selective necessity experiments. Authors might consider adding optogenetic (or chemogenetic) experiments aimed at inhibiting LC-NA hippocampal projections during stress exposure (or, alternatively, perform intrahippocampal pharmacological blockade of β-adrenoreceptors during stress exposure), and determine the effects on gene expression.

Response: We kindly refer the reviewer to our previous response to Comment #2 above.

Minor concerns:

There is a typo in the abstract. Please correct "LN-NA" with "LC-NA"

Response: Thank you, we have corrected it.

References

Bangasser, D. A., Eck, S. R., & Ordoñes Sanchez, E. (1/2019). Sex differences in stress reactivity in arousal and attention systems. Neuropsychopharmacology: Official Publication of the American College of Neuropsychopharmacology, 44(1), 129–139.

Bangasser, D. A., Wiersielis, K. R., & Khantsis, S. (06/2016). Sex differences in the locus coeruleusnorepinephrine system and its regulation by stress. Brain Research, 1641, 177–188.

Author Response

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

Reviewer #1 (Recommendations For The Authors):

All comments made in the public section.

We would like to thank the reviewer for their assessment of our study and for suggestions for additional experiments to follow up our studies.

Reviewer #2 (Recommendations For The Authors):

‐ Preparation of spike proteins and VLPs. Although Triton‐X114 extraction was done to remove endotoxin from the recombinant spike protein preparations, its removal efficiency depends on the levels of endotoxin in the samples. Therefore, the residual endotoxin levels in each of the test samples and batches should be measured. Even very low but varying levels of residual endotoxin would substantially impact the reported results, as they create inconsistent data that are not interpretable.

Certainly, endotoxin contamination in instilled materials is always an issue. Established protocols for inducing acute inflammatory responses using endotoxin outline specific ranges of endotoxin levels in the instillation materials. To induce acute lung inflammation in mice at least 2 µg of endotoxin must be instilled. We have endeavored to reduce the possibility of endotoxin contamination in our recombinant proteins by using a mammalian expression system; careful aseptic culture and protein purification techniques; and a final Triton-X114 partitioning protocol. We assessed the possibility of endotoxin contamination using the Pierce™ Chromogenic Endotoxin Quant Kit, which is based on the amebocyte lysate assay. Our analysis revealed that the endotoxin level in the purified recombinant protein preparation is below 1.0 EU/ml, which closely aligns with the levels specified for recombinant proteins. An endotoxin concentration of 1.0 EU/ml is equivalent to approximately 0.1 ng/ml. Throughout all mouse nasal instillation experiments, the total volume of recombinant protein administered did not exceed 6 µl. The amount of contaminant endotoxin instilled did not exceed 1 pg (50 µl of 0.02 ng/ml of endotoxin). Consequently, we can confirm that the extent of endotoxin contamination is at trace levels. Moreover, our study reveals multiple results indicating that the level of endotoxin contamination in the recombinant protein was inadequate to independently induce neutrophil recruitment in the cremaster muscle, lymph nodes, and liver. For further insights, refer to Figure 5.

‐ Doses of spike and VLPs: The amount of spike protein incorporated into HIV Gag‐based VLPs should be determined and compared to that found in the native SARS‐CoV‐2 virus particles. This should provide more physiologic doses (or dose ranges/titration) of spike than the arbitrary doses (3 ug or 5 ug) used in the mouse experiments.

To visualize the acquisition of spike protein and track cells that have acquired the spike protein, we conducted a series of tests and optimizations using different concentrations of Alexa 488 labeled spike protein, ranging from 0.5 to 5 µg. During the processing of lung tissue for microscopic imaging, it was of utmost importance to preserve the integrity of the labeled spike protein in the tissue samples. We determined that instillation of 3 µg of Alexa 488 labeled spike protein yielded the optimal signal strength across the lung sections. Notably, in many mouse models employing intra-nasal instillation protocols for SARS-CoV2 spike protein or RBD domain-only recombinant proteins, a dosage of approximately 3 µg or higher were commonly used. Regarding the titer of spike-incorporated VLPs, it is important to highlight that we did not directly compare the quantity of spike protein present in NL4.3 VLPs to that of the naïve SARS-CoV-2 virus. HIV-1 and SARS-CoV-2 viruses typically carry around 70 gp120 spikes and 30 spikes, respectively. We estimated that SARS-CoV-2 spike-incorporated NL4.3 VLPs may display twice the number of spikes compared to naïve SARS-CoV-2. Notably, our measurements of SARS-CoV-2 spike on NL4.3 VLPs demonstrated similar behavior to SARS-CoV-2 in terms of specific binding to ACE2-expressing 293T cells, indicating their functional similarity in this context.

Author response image 1.

Spike protein-incorporated NL4.3 VLPs test with human ACE2-transfected HEK293 cells. The wild-type spike protein-incorporated VLPs and delta envelope NL4.3 VLPs were analyzed using human ACE2-transfected HEK293 cells. The first plot shows ACE2 expression levels in HEK293 cells. The second plot displays the binding pattern of Delta Env NL4.3 VLPs on ACE2-expressing HEK293 cells. The third plot illustrates the binding pattern of wild-type spike protein-incorporated NL4.3 VLPs on ACE2expressing HEK293 cells. The histogram provides a comparison of VLP binding strength to ACE2expressing HEK293 cells.

‐ The PNGase F‐treated protein was not studied in Fig 1. In Fig 2, glycan‐removal by PNGaseF has little effects on cell uptake and cell recruitment in the lung. If binding to one of the Siglec lectins is a critical initial step, experiments should be designed to evaluate this aspect of the spike‐cell interaction in a greater depth.

As the reviewer states results with the PNGase F-treated protein were not shown in Fig. 1 although we showed results in Figs. 2 & 3. See discussion below about our preparation of the PNGase F-treated protein. Perhaps because we elected to use a purified fraction that retained ACE2 binding, the protein we used likely retained some complex glycans. As the reviewer notes the PNGase F treated protein had similar overall cellular recruitment and uptake profiles compared to the untreated spike protein. The PNGase Ftreated fraction we used no longer bound Siglec-F in the flow-based assay, shown in Fig. 7. This argues that the initial uptake and cellular recruitment following intranasal instillation of the Spike protein did not depend upon the engagement of Siglec-F. While Siglec-F on the murine alveolar macrophage can likely efficiently capture the spike proteins other cellular receptors contribute and the overall impact of the spike protein on alveolar macrophages likely reflects its engagement of multiple receptors.

• Enzymatic removal of sialic acids from spike may be one parameter to explore. The efficiency of enzymatic removal should also be verified prior to experiments. Finally, the authors need to assess whether the proteins remained functional, folded properly, and did not aggregate.

To obtain the de-glycosylated form of the SARS-CoV-2 spike protein, we employed PNGase F enzymatic digestion to remove glycans. Subsequently, the spike protein was purified using a size exclusion column. During this purification process, the PNGase F-treated spike protein segregated into two distinct fractions, specifically fraction 6 to 8 and fraction 9 to 11 (see revised Figure 1- figure supplement 1).

Author response image 2.

Size exclusion chromatography. The peak lines represent the absorbance at 280 nm. PNGase F-treated spike proteins were loaded onto a Superdex 26/60 column, resolved at a flow rate of 1.0 ml/min, and collected in 1 ml fractions.

The Coomassie blue staining of an SDS-PAGE gel revealed that fractions 6 to 8 likely underwent a more pronounced de-glycosylation by PNGase F compared to fractions 9 to 11. Additionally, during the size column purification, we noticed that fraction 6 to 8 exhibited a faster mobility than the untreated spike protein, implying a potentially substantial modification of the protein's conformation. To probe the functional characteristics of the de-glycosylated spike protein in fraction 6 to 8, we conducted binding tests with human ACE2. Strikingly, the spike protein in fraction 6 to 8 completely lost its binding affinity to ACE2, indicating a loss of its ACE2-binding capability. Conversely, the protein in fraction 9 to 11 showed partial de-glycosylation but still retained its original functionality to bind to ACE2 and its antibody.

Author response image 3.

FACS analysis of various spike protein-bound beads. Protein bound beads were detected with labeled spike antibody, recombinant human ACE2, and recombinant mouse Siglec-F.

Based on these results, we concluded that fraction 9 to 11 would be the most suitable choice for further studies as the de-glycosylated spike protein, considering its retained functional properties relevant for ligating ACE2 and antibody motifs yet had lost Siglec-F binding. In the revised manuscript we have describe in more detail the purification of the PNGase F treated Trimer and its functional assessment.

‐ Increases in macrophages and alveolar macrophages by Kifunensine Tx spike in Fig 2A suggest effects that are not related to Siglec lectins. These effects are not seen with the wild type or D614 spike trimers, so the relevance of high‐ mannose spike is unclear. On the other hand, there were clear differences between Wuhan and D614 trimers seen in Fig 2A and 2B, but there was no verification to ascertain whether these differences were indeed due to strain differences and not due to batch‐to‐batch variability of the recombinant protein production. The overall glycan contents of the Wuhan and D614 spike protein samples should be measured. If Siglec interaction is the main interest in this study, the terminal sialic acid contents should be determined and compared to those in the corresponding strains in the context of native SARS‐CoV‐2 virions.

Our initial observation that Siglec-F positive alveolar macrophages (AMs) avidly acquired spike proteins followed by a rapid leukocyte recruitment provided the rational for us to examine the impact of modifying the glycosylation pattern on the spike protein (de-glycosylated and spike variants) on their binding tropism and their cellular recruitment profiles in the lung. In this context, we examined the influence of several glycan modification on spike proteins, hypothesizing that these modifications would alter the acquisition of the spike protein by mouse AMs compared to the wild-type trimer. While we did not conduct an indepth analysis of the glycan composition and terminal sialic acid contents of the SARS-CoV-2 spike proteins we used we did verify that the different proteins behaved as expected. Most of the biochemical studies were performed in Jim Arthos’ laboratory, which has a long interest in the glycosylation of the HIV envelope protein. On SDS-PAGE the SARS-CoV-2 spike protein purified from the Kifunesine treated CHO cells exhibited a 12 kDa reduction. It bound much better to L-Sign, DC-Sign, and maltose binding lectin, and poorly to Siglec-F. In the cellular studies it bound less well to most of the cellular subsets examined including murine alveolar macrophages. In studies with human blood leukocytes, it relied on cations for binding. However, it retained its toxicity directed at mouse and human neutrophils and it elicited a similar cytokine profile when added to human macrophages. The D614G mutation increased the spike protein binding to P-Selectin, CD163, and snowdrop lectin (mannose binding) suggesting that the mutation had altered the glycan content of the protein. We used the D614G spike protein in a limited number of experiments as it behaved like the wild-type protein except for a slightly altered cellular retention pattern 18 hrs after intranasal instillation. In the revised manuscript we have included its binding to peripheral blood leukocytes. The D614G mutation conferred stronger binding to human monocytes than the original Spike protein. As discussed above, we recovered two fractions following the PNGase F treatment, one with a 40 kDa reduction on SDS-PAGE and the other a 60 kDa decrease and we chose to evaluate the fraction with a 40 kDa reduction in subsequent experiments. Consistent with a loss of N-linked glycans the PNGase F treatment reduced the binding to the lectin PHA, which recognizes complex carbohydrates, and it resulted in a sharp reduction in Siglec-F binding. The lower molecular weight fraction recovered after PNGase F treatment no longer bound ACE2. While our studies showed that alveolar macrophages likely employ Siglec-F as a capturing receptor they possess other receptors that also can capture the spike protein. The downstream consequences of engaging SiglecF and other Siglecs by the SARS-CoV-2 spike protein will require additional studies.

While acknowledging the possibility of some batch-batch variation in recombinant protein preparation, we don’t think this was a major issue. We have noted some batch-batch variations in yield- efficiency, however the purified proteins consistently gave similar results in the various experiments.

‐ Fig 3: The same concern described above applies to the hCoV‐HKU1 spike protein. In Panel D, the PNGase and Kifunensine treatment did not appear to abrogate the neutrophil recruitment. Panel A did not include PNGase and Kif Tx spike proteins. Quantification of images in panel D is missing and should be done on many randomly selected areas.

We analyzed the neutrophil count of images in panel D and the results are presented. (Figure 3-figure supplement 1C). The Kifunensine treatment reduced the neutrophil recruitment at 3 hours, while the PNGase F treated Spike protein recruited as well or slightly more neutrophils. The hCoV-HKU1 S1 domain did not differ much from the saline control.

‐ Fig 4: Kifunensine Tx spike caused more increase in neutrophil damage after intrascrotal injections. PNGase Tx spike was not tested. Connection between Siglec‐spike binding and neutrophil recruitment/damage is lacking.

Exteriorized cremaster muscle imaging functions as a model system for monitoring neutrophil behavior recruited by spike proteins within the local tissue, distinct from Siglec F-positive alveolar macrophages residing in lung tissue. Hence, our primary focus was not on investigating the Siglec/Spike protein interaction. Consequently, we did not utilize PNGase F-treated spike protein in these experiments. To clarify this issue, we added a sentence in main text ‘Although this model lacks Siglec F-positive macrophages, it is worth monitoring the effect of the SARS-CoV-2 Spike protein on neutrophils recruited in the inflammatory local tissue.’

‐ Fig 5. Neutrophil injury was also seen after inhalation (intranasal) of spike protein in mice and in vitro with human neutrophils. Panel B shows no titrating effects of spike (from 0.1 to 2) on Netosis of murine neutrophils. Panel C: Netosis was seen with human neutrophils at 1 but not 0.1. Is this species difference important?

Given the observation of neutrophil NETosis in the mouse imaging experiment, our objective was to characterize the direct impact of the spike protein on human and murine neutrophils. The origins of the neutrophils are different as the murine neutrophils were purified from mouse bone marrow while the human neutrophils were purified from human blood. Both purification protocols led to greater than 98% neutrophils. However, the murine neutrophils contain many more immature cells (50-60%) because the bone marrow served as their source. Furthermore, the murine neutrophils are from 6–8-week-old mice while the human neutrophils are from 30-50 year-old humans. More work would be needed to sort out whether there is any difference between human and mouse neutrophils in their propensity to undergo netosis in response to Spike protein.

‐ Kifunensine Tx again did not cause any reduction, indicating the lack of involvement of sialic acid. How was this related to Siglec participation directly or indirectly? There was no quantification for Panel D.

We do not think that Siglecs play a role in the induction of neutrophil netosis as the Spike proteins lacking Siglec interactions induced similar levels of netosis. Likely other neutrophil receptors are important. As noted in the text,

"human neutrophils express several C-type lectin receptors including CLEC5A, which has been implicated in SARS-CoV-2 triggered neutrophil NETosis." Our goal with the data in Panel D was to visualize human neutrophil NETosis on trimer-bearing A549 cells we relied on the flow cytometry assays for quantification.

‐ The rationale for testing cation dependence is unclear and should be described. What is the significance of "cations enhanced leukocyte binding particularly so with the high mannose protein"? Are there cationdependent receptors for spike independent of glycans and huACE‐2? If so, how is this relevant to the main topic of this paper?

It is well known that many glycan bindings by C-type lectins are calcium-dependent, involving specific amino acid residues that coordinate with calcium ions and bind to the hydroxyl groups of sugars. As discussed in our previous draft, the C-type lectin receptor L-SIGN has been suggested as a calciumdependent receptor for SARS-CoV-2, specifically interacting with high-mannose-type N-glycans on the SARS-CoV-2 spike protein. Therefore, it was worthwhile to investigate the calcium-dependent manner of spike protein binding to various types of immune cells. We added some data to this figure. It now includes the binding profile of the D614G protein. In addition, we corrected the binding data by subtracting the fluorescent signal from the unstained control cells.

‐ Fig 7: human Siglec 5 and 8 were studied in comparison with mouse Siglec F. Recombinant protein data are not congruent with transfected 293 cell data. Panel A, the best binding to hSiglec 5 and 8 are the PNGase F Tx spike protein; how to interpret these data? Panel B: only the WT and D614G spike proteins binding to Siglec 5 and 8 on transfected cells. It made sense that kif Tx (high‐mannose) and PNGaseF Tx (no glycan) spike would not bind to the Siglecs, but they did not bind to ACE2 either, indicative of nonfunctional spike proteins.

We discussed this as follows: ‘The closest human paralog of mouse Siglec-F is hSiglec-8 (reference 40). While expressed on human eosinophils and mast cells, human AMs apparently lack it. In contrast, human AMs do express Siglec-5 (reference 37). Along with its paired receptor, hSiglec-14, Siglec-5 can modulate innate immune responses (reference 41). When tested in a bead binding assay, in contrast to Siglec-F, neither hSiglec-5 or -8 bound the recombinant spike protein, yet their expression in a cellular context allowed binding. The in vitro bead binding assay we established demonstrated the specific binding of the bait molecule to target molecules. However, it does have limitations in replicating the complexities of the actual cellular environment. As discussed previously the PNGase Tx fraction we used in these experiments retained ACE2 binding, but loss binding to Siglec-F in the bead assay. In a biacore assay, not shown, the PNGase Tx fraction bound L-Sign and DC-Sign better than the untreated trimer, and it retained human ACE2 binding although it bound less well than wild type-trimer. Why the PNGase Tx fractions bound poorly to the human ACE2 transfected HEK293 cells is unclear. A higher density of recombinant ACE2 on the beads compared to that expressed on the surface of HEK293 may explain the difference. Alternatively in the bead assay we used a recombinant human ACE2-Fc fragment fusion protein purified from HEK293 cells, while in the transfection assay, we expressed human full length ACE2. The biacore, the bead binding, and the functional assays we performed all suggest that we had used intact recombinant proteins.

‐ Fig 8: This last set of experiment was to measure cytokine release by different types of macrophage cultures treated with spike from different cells with vs without Kifunensine Tx. The connection of these experiments to the rest is tenuous and is not explained. This is one of the examples where bits of data are presented without tying them together.

Dysregulated cytokine production significantly contributes to the pathogenesis of severe COVID-19 infection. Since we had observed strong binding of the spike protein to human monocytes and murine alveolar macrophages, we tested whether the spike protein altered cytokine production by human monocyte-derived macrophages. Depending on the culture conditions human monocytes can be differentiated M0, M1, or M2 phenotypes. Each type of macrophage responds differently to stimulants, often leading to distinct patterns of cytokine secretion. These patterns offer valuable insights into the immune response. The cytokine profiling conducted in this study enhances our understanding of how distinct macrophage types react to the spike protein.

‐ Discussion section did not describe how the various experiments and data are tied together. The authors explained the interactions of spike with different cell types in each paragraph separately, leaving this reviewer really confused as to what the authors want to convey as the main message of the paper.

We have modified discussion to address this issue.

Reviewer #3 (Recommendations For The Authors):

‐ The authors may want to refer to "intranasal instillation" to distinguish it from inhalation of an aerosolised liquid. How was the dose of the spike protein selected? There is some dose information in different settings, but usually between 0.1‐1 µg/ml or 0.1 µg‐5 µg range for in vivo injection, but the rationale for these ranges should be discussed. Is this mimicking a real situation during infections or a condition that might be used for vaccines?

While inhalation of aerosolized liquid closely mimics the natural route of human exposure to respiratory infectious materials, intranasal instillation with a liquid inoculum remains a widely accepted standard approach for virus or vaccine inoculation across various laboratory species. To clearly define our mouse model, we are changing the term 'inhalation' to 'instillation'. We previously answered to Reviewer #2 as following: To visualize the acquisition of spike protein and track cells that have acquired the spike protein, we conducted a series of tests and optimizations using different concentrations of Alexa Fluor 488 labeled spike protein, ranging from 0.5 to 5 µg. During the processing of lung tissue for microscopic imaging, it was of utmost importance to preserve the integrity of the labeled spike protein on the tissue samples. Through our investigations, we determined that an instillation of 3 µg of Alexa Fluor 488 labeled spike protein yielded the most optimal signal strength across the lung sections. Notably, in many mouse models employing intra-nasal instillation protocols for SARS-CoV-2 spike protein or RBD domain-only recombinant proteins, a dosage of approximately 3 µg or higher was commonly used. Hence, based on these references and our preliminary studies, we selected 3 µg as the optimal concentration of instilled spike protein per mouse.

‐ Controls are not evenly applied. In some cases, the control for the large and complex SARS‐CoV2 spiker trimer is PBS. This seems insufficient to control against effects of injecting such complex proteins that can undergo significant conformational changes after uptake by a cell. In some cases, human coronavirus spike proteins from different viruses are used, but not much is said about these proteins and the different glycoforms are not explored. Are these prepared in the same way and do they have similar glycoforms. For example, if the Siglecs bind sialic acid on N‐linked glycans, then why do the purified Siglecs or Siglecs expressed in cells not bind the HKU‐1 spike, which would have such sialic acids if expressed in the same way as the CoV2 spike?

We have taken careful consideration to select an appropriate control material for these experiments. Initially, we opted to employ Saline or PBS for intranasal instillation as a vehicle control, a choice aligned with the approach taken in numerous previous studies involving lung inflammation mouse models. However, as the reviewer pointed out, we share the concern for achieving more meaningful and comparable control materials, particularly considering the size and complexity of the recombinant protein. In accordance with this perspective, we introduced glycan-modified spike proteins and the HCoV-HKU1 S1 subunit. Figure 3 illustrates our comprehensive evaluation of various spike proteins in terms of their impact on neutrophil recruitment. The diversity of sialic acid structures observed on recombinant proteins expressed within the same cell emerges from the intricate interplay of multiple factors within the cellular glycosylation machinery. This complex enzymatic process empowers cells to finely modulate glycan structures and sialic acid patterns, tailoring them to suit the diverse biological functions of distinct proteins. Despite structural similarities between the HCoV-HKU1 and SARS-CoV-2 spike proteins, their glycan modifications vary, thereby leading to distinct binding properties with various Siglec subtypes. All recombinant proteins used in this study except for the S1 subunits were generated within our laboratory. These include the wild-type spike protein, the D614G Spike protein, the Kifunensine-treated high mannose spike proteins, and the PNGase F-treated deglycosylated spike proteins. All the proteins were produced using the same protocol using CHO cells or on occasion HEK293F cells. We have indicated in the manuscript where we used HEK293F cells for the protein production otherwise they were produced in CHO cells.

‐ Figure 1 F‐I, there should be a control for VLP without SARS‐CoV2 spike as the VLP will contain other components that may be active in the system.

We tested the delta Env VLP for alveolar macrophage acquisition and neutrophil recruitment. We found a similar alveolar macrophage acquisition of the VLPs, but significantly less neutrophil recruitment compared to the free Spike protein. Since the uptake pattern with the VLPs matched that of the spike protein we did not consider adding a non-spike bearing VLP as a control. The rapid VLPs clearance into the lymphatics shortly after instillation may account for the reduced neutrophil recruitment following their instillation (Figure 1 figure supplement 2B, C).

‐ In Figure 1H, that do they mean by autofluorescence? Is this the cyan signal?

Is the green signal also autofluorescence as this is identified as the VLP?

We appreciate reviewer pointing out the typo regarding autofluorescence in the figure image. To provide clarity regarding the background in all lung section images, we have included additional supplemental data. During the fixation process of lung tissue, various endogenous elements in the tissue sample contribute to autofluorescence when exposed to lasers in the confocal microscope. Specifically, collagen and elastin present in the lung vasculature, including airways and blood vessels, are dominant structures that generate autofluorescence. To address this issue, we have implemented optimizations to distinguish between real signals and the noise caused by autofluorescence. We inadvertently failed to indicate the source of the strong cyan signal. The signal is due to Evans Blue dye delineating lung airway structures, which contain collagen and elastin—known binding materials for Evans Blue dye. This explains the strong fluorescence signals observed in the airways. We conjugated the recombinant spike protein with Alexa Fluor 488, and viral-like particles (VLPs) were visualized with gag-GFP. (Figure 1 figure supplement 2A, D)

‐ The control for SARS‐CoV2 spike trimer is PBS, but how can the authors distinguish patterns specific to the spike trimer from any other protein delivered by intranasal instillation. Could they use another channel with a control glycoprotein to determine if there is anything unique about the pattern for spike trimer?

Alveolar macrophages employ numerous receptors to capture glycoproteins that have mannose, Nacetylglucosamine, or glucose exposed. Galactose-terminal glycoproteins are typically not bound. We do not think that the Spike protein is unique in its propensity to target alveolar macrophages.

‐ What is the parameter measured in Figure S2B?

The percentage of the different cell types that have retained the instilled Spike protein at the three-hour time point. .

‐ The Spike trimer with high mannose oligosaccharides may gain binding to the mannose receptor. It may be helpful to state the distribution of this receptor and comment is it could be responsible for this having the largest effect size for some cell types.

We agree that the spike trimer with high mannose should target cells bearing the mannose receptor. We have modified the discussion to address this point and have mentioned some of the cell types likely to bind the high mannose bearing spike protein.

‐ A key experiment is the Evans Blue measure of lung injury in Figure 3A. A control with the HKU‐1 spike is also performed, but more details on the matching of this proteins production to the SARS‐CoV2 spike trimer and the quantification of these comparative result should be provided. To show that the SARSCoV2 spike trimer can cause tissue injury on its own seems like a very important result, but the impact is currently reduced by the inconsistent application of controls and quantification of key results. Furthermore, if these results can be repeated in the B6 and B6 K18‐hACE2 mouse model it might further increase the impact by demonstrating whether or not hACE2 contributes to this effect.

We repeated the lung permeability assay using the S1 subunit from the original SARS-CoV-2 and the S1 subunit from HCoV-HKU1. Both proteins were made by the same company using a similar expression system and purification protocol. Consistent with our original data, the instillation of the SARS-CoV-2 S1 subunit led to an increase in lung vasculature permeability, whereas the HCoV-HKU-1 S1 subunit had a minimal impact. (Figure 3 figure supplement 1A). This experiment suggests that it the S1 subunit that leads to the increase in vascular permeability. To address the contribution of hACE2 in this phenomenon, we conducted a lung permeability assay using K18-hACE2 transgenic mice. The K18-hACE2 transgenic mice exhibited a slight increase in lung vasculature permeability upon SARS-CoV-2 trimer instillation compared to the non-transgenic mice. This suggests that the hACE2-Spike protein interaction may contribute to an increase in lung vascular permeability during SARS-CoV-2 lung infection (Figure 3 figure supplement 1B).

‐ For Figure 4A, could they provide quantification. The neutrophil extravasation with Trimer appears quite robust, but the authors seem to down‐play this and it's not clear without quantification.

To address this issue, we analyzed and graphed the neutrophil numbers in each image. Injection of the trimer along with IL-1β significantly increased neutrophil infiltration. (Figure 4 figure supplement 1)

‐ In Figure 4B, there are no neutrophils at all in the BSA condition. Is this correct? Intravascular neutrophils were detected with PBS injection in Figure 4A.

We demonstrated that the neutrophil behaviors occur within the infiltrated tissue rather than within the blood vessels. Even when examining the blood vessels in all other images, it is challenging to identify neutrophils adhering to the endothelium of the blood vessels. Neutrophils observed in the PBS 3-hour control group are likely acute responders to the local injection, as a smaller number of neutrophils were observed in the 6-hour image.

‐ In Figure 5A the observation of neutrophil response in lung slices seems to be presented an anecdotal account. The neutrophil appears to polarize, but is this a consistent observation? How many such observations were made?

We have consistent observations across three different experiments. In addition, highly polarized and fragmented neutrophils were consistently observed in the fixed lung section images.

‐ The statement: "human Siglec‐5 and Siglec‐8 bound poorly despite being the structural and functional equivalents of Siglec F, respectively (37)". How can one Siglec be the structural and the other the functional equivalent of Siglec‐F? It might help to provide a little more detail as to how these should be seen.

Mouse Siglec-F has two distinct counterparts in the human Siglec system, both in terms of structure and function. In the context of domain structure, human Siglec-5 serves as the counterpart to mouse Siglec-F. However, it's important to note that while human Siglec-8 is not a genetic ortholog of mouse Siglec-F, it is expressed on similar cellular populations and functions as a functional paralog.

‐ The assay using purified proteins and proteins expressed in cells don't fully agree. For example, it's very surprising that recombinant Siglec 5 and 8 bind better to the non‐glycosylated form than to the glycosylated trimer. It appears from Figure S1 that the PNGaseF treated Spike contains at least partly glycosylated monomers and it also appears that the Kifunesine effect may be partial. PNGaseF may have a hard time removing some glycans from a native protein.

We were also surprised by the results using the PNGase F treated Spike protein in that it lost binding to Siglec-F and retained binding to human Siglec-5 and 8 in the bead assay, shown in Figure 7A. As explained above we used a purified fraction of the PNGase F treated protein that retained some functional activity as assessed in the ACE2 binding assay and in biacore assays not shown. The persistent binding of Siglec-5 and Siglec-8 suggests that removal of some of the complex glycans had revealed sites capable of binding Siglec-5 and 8. We would agree with the reviewer that the PNGase treatment we used only removed some of the glycans from the native protein. In data not shown the high mannose spike protein behaved as predicted in biacore assays, binding better to DC-SIGN and maltose binding lectin, but less well to PHA and less well to ACE2. The high mannose trimer also bound less to the HEK293 cells expressing ACE2, Siglec-5, or Siglec-8 as well as peripheral blood leukocytes.

Author Response

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

eLife assessment

This study presents valuable findings that examine both how Down syndrome (DS)-related physiological, behavioral, and phenotypic traits track across time, as well as how chronic treatment with green tea extracts 25 enriched in epigallocatechin-3-gallate (GTE-EGCG), administered in drinking water spanning prenatal through 5 months of age, impacts these measures in wild-type and Ts65Dn mice. However, the strength of the evidence is incomplete, due to high variability across measures, perhaps attributable to a failure to include sex as a factor for measures known to be sexually dimorphic. This study is of interest to scientists interested in Down Syndrome and its' treatment, as well as scientists who study disorders that impact multiple organ systems.

Public Reviews:

Using Ts65Dn - the most commonly used mouse model of Down syndrome (DS) - the goal of this study is two-pronged: 1) to conduct a thorough assessment of DS-related genotypic, physiological, behavioral, and phenotypic measures in a longitudinal manner; and 2) to measure the effects of chronic GTE-EGCG on these measures in the Ts65Dn mouse model. Corroborating results from several previous studies on Ts65Dn mice, findings of this study show confirm the Ts65Dn mouse model exhibits the suite of traits associated with DS. The findings also suggest that the mouse model might have experienced drift, given the milder phenotypes than those reported by earlier studies. Results of the GTE-EGCG treatment do not support its therapeutic use and instead show that the treatment exacerbated certain DS-related phenotypes.

Strengths:

The authors performed a rigorous assessment of treatment and examined treatment and genotypic alterations at multiple time points during growth and aging. Detailed analysis shows differences in genotype during aging as well as genotype with treatment. This study is solid in the overarching methodological approach (with the exception of RNAseq, described below). The biggest strength of the study is its approach and dataset, which corroborate results from a multitude of past studies on Ts65Dn mice, albeit on adult specimens. It would be beneficial for the dataset to be made available to other researchers using a public data repository.

We deeply appreciate the reviewers' positive feedback. Their acknowledgment of the solid methodological approach and the rigorous assessment of genotypic and treatment effects over various developmental stages resonates with our motivation. Their suggestion to make the dataset available in a public data repository for other researchers is well-taken. We are committed to data sharing and we are creating a dedicated platform to facilitate the accessibility of our research data to the scientific community. Given its size and complexity, we currently hold the dataset available upon reasonable request to the corresponding authors.

Weaknesses:

There are several primary weaknesses, described below:

Sex was not considered in the analyses.

The number of experimental animals of each sex are not clearly represented in the paper, but are buried in supplemental tables, and the Ns for the RNAseq are unclear. No analyses were done to examine sex differences in male/female DS or WT animals with or without treatment. Body measurements will greatly vary by sex, but this was not taken into consideration during assessments. As such, there is a high amount of variability within each cohort measured for body assessments (tibia, body weight, skeletal development etc.). Supplemental table 14 had the list of each animal, but not collated by sex, genotype or treatment, making it difficult to assess the strength of each measurement.

Our study primarily concentrated on providing a holistic understanding of the impact of trisomy and GTE-EGCG treatment on Down syndrome, and was not explicitly designed to investigate sexual dimorphism. However, instead of reporting on only one sex and thereby obviating sex as a source of variation, as in previously published studies, we decided to include both male and female mice within the study design to represent a more realistic portrayal of the nature of Down syndrome in a heterogeneous population. By encompassing both sexes, we aim to better capture the variability in Down syndrome.

As we do acknowledge the significance of sex bias in scientific research, we considered performing post-hoc analyses to test the effect of sexual dimorphism, but found that our dataset was underpowered to obtain reliable results, since our experiments were not a priori designed to investigate this question and sample sizes for each sex by separate were not large enough. Nevertheless, considering the reviewer’s comment, we have taken specific steps to improve the representation of sex-related information and to enhance the clarity of our manuscript.

First, we have redesigned all figures using empty and full symbols to distinguish male from female mice within each analysis, providing readers with an immediate sense of the sex distribution in each experimental group. Moreover, we have modified Supplementary Table 1 to offer a comprehensive breakdown of the number of male and female mice for each test, along with their respective genotypes and treatment groups. This table aims to make the sample size and sex distribution within our study as transparent as possible for our readers. While we acknowledge that our study lacked the statistical power to perform a detailed sex-based analysis, the visual representation of sex in our data shows which systems are mainly affected by sexual dysmorphism. This evidence can guide future investigations directly designed to investigate sexual effects in certain systems or structures.

Key results are not clearly depicted in the main figures

Rigorous assessment of each figure and the clarity of the figure to convey the results of the analysis needs to be performed. Many of the figures do not clearly represent the findings, with authors heavily relying on supplemental figures to present details to explain results. Figure legends do not adequately describe figures; rather, they are limited to describing how the analysis is performed. For example, LDA plots in Figure 4 do not clearly convey the results of metabolite analysis.

Overall, the amount of data presented here is overwhelming, making it difficult to interpret the findings. Some assessments that do not add to the overall paper need to be removed. Clarifying the text, figures and trimming the supplement to represent the data in a manner that is easily understood will improve the readability of the paper. For example, perhaps measures which are not strongly impacted by genotype could be moved to the supplement, because they are not directly relevant to the question of whether GTE-EGCG reverses the impact of trisomy on the measures.

As rightly pointed out by the reviewers, the vast amount of data generated by our holistic and longitudinal approach is one of the primary strengths, but also an important challenge in our study. Our dataset encompasses a comprehensive assessment of the effects of treatment and genotypic alterations at multiple time points during growth and aging. This multi-dimensional evaluation is pivotal to our research, and relegating data to supplementary material would restrict access to this holistic understanding. Our aim is to provide readers with a complete view of the complex interactions we have explored, and retaining this data in the main text is essential to uphold the integrity of our work.

Indeed, we specifically chose to submit or manuscript to eLife because this journal allows to access supplemental information directly from the text and figures in the main manuscript and best aligned with our approach to data presentation. The eLife format permits us to offer readers a quick and informative overview of all the data within the main figures employing multivariate techniques such as Linear Discriminant Analysis or Principal Component Analysis. Subsequently, we supply more detailed analyses in the supplementary figures for readers who wish to delve deeper into specific aspects. Furthermore, while certain figures may be categorized as supplementary, for us it is crucial, and we would like to emphasize, that every result is comprehensively described in the main text.

Acknowledging the concerns raised about the density of our paper and the potential challenges in interpreting the findings, we have conducted a thorough review of the text and figure legends. We have made revisions with the goal to enhance clarity and readability. We have made dedicated efforts to ensure that readers can readily grasp the significance of our results and appreciate the intricacies of our findings. We firmly believe that with these revisions, our chosen approach is the most effective means of presenting the richness of our data and maintaining the integrity of our findings.

Lack of clarity in the behavioral analyses

Behavioral assessments are not clearly written in the methods. For example, for the novel object recognition task, it isn't clear how preference was calculated. Is this simply the percent of time spent with the novel object, or is this a relative measure (novel:familiar ratio)? This matters because if it is simply the percent of time, the relevant measure is to compare each group to 50% (the absence of a preference). The key measures for each test need to be readily distinguished from the control measures.

There are also many dependent behavioral measures. For example, speed and distance are directly related to each other, but these are typically reported as control measures to help interpret the key measure, which is the anxiety-like behavior. Similarly, some behavioral tests were used to represent multiple behavioral dimensions, such as anxiety and arousal. In general, the measurements of arousal seem atypical (speed and distance are typically reported as control measures, not measures of arousal). Similarly, measures of latency during training would not typically be used as a measure of long-term memory but instead reported as a control measure to show learning occurred. LDA analysis requires independence of the measures, as well as normality. It does not appear that all of the measures fed into this analysis would have met these assumptions, but the methods also do not clearly describe which measures were actually used in the LDA.

We agree with the reviewers’ concerns about the clarity of our behavioral analyses and we have thus added information to the methods section to clarify the procedures. Specifically, for SPSN, social approach was recorded as time spent close to STR1, and a preference ratio was calculated as Pref= 100 Time close to STR1/(Time close to STR1 + Time close to Empty). Social recognition memory was scored as preference towards STR2 and calculated as Pref =100 (time close to STR2) / (Time close to STR1 + Time close to STR2). For NOR, preference for novel object was calculated as Pref=100* Time novel object / (Time familiar object + novel object).

With regards to the different variables reported for the behavioral protocols, we agree that some measures, such as path length and speed can be used as control measures. For example, in an open field test, path length is an important control measure to assess whether an animal is engaged in the task. However, if an animal is actively moving, the amount of distance covered can but does not have to correlate with the amount of time that a mouse spends in the center of the open field. Using the measure of distance covered as a measure for general arousal and time spent in the center as a measure for anxiety related behavior allows a more nuanced evaluation of animal behavior. For instance, two animals spending similar amounts of time in the center may exhibit differences in the distance they cover. In this scenario, we would argue that anxiety related behavior (defined as exploring the center of an open field) would not reflect well a behavioral difference between the two animals, while the aspect of arousal clearly is a differencing factor.

Regarding the PA task and the use of latency during training, we agree that typically latency during training can be used as control measure to show that learning occurred. However, our study involved testing animals at two distinct time points. Contextual fear conditioning creates very robust memory traces that can persist for weeks or even months, and therefore the starting premise is very different when repeating the test. Initially, the animals were experimentally naïve and had not yet experienced a foot shock, leading to a rapid entry into the dark box. However, after experiencing the first CS-US presentation, a robust and persistent contextual fear memory trace is formed. Therefore, the latency observed in the second training phase of the PA reflects in essence long-term contextual fear memory, that is robustly displayed in WT animals but less in treated WT and TS animals. We have included this clarification in the methods and results sections.

Finally, we want to thank the reviewer for noticing the error in the LDAs, as the analysis was indeed performed including dependent variables for some systems. We have re-evaluated the LDAs for the behavioral tests and tibia microarchitecture tests, excluding dependent variables. As a result, the text and significance levels have been adjusted accordingly. To enhance transparency and clarity, we have included Supplementary Table S21, which precisely outlines the variables included in each LDA.

Unclear value of RNAseq

RNAseq was performed in cerebellum, a relatively spared region in DS pathology at an early time point in disease. Further, the expression of 125 genes triplicated in DS was shown in a PCA plot to highly overlap with WT, indicating that there are minimal differences in gene expression in these genes. If these genes are not critical for cerebellar function, perhaps this could account for the lack of differences between WT and Ts65Dn mice. If the authors are interested in performing RNAseq, it would have made more sense to perform this in hippocampus (to compare with metabolites) and to perform more stringent bioinformatic analysis than assessment by PCA of a limited subset of genes. Supplementary Table S14, which shows the differentially expressed genes, appears to be missing from the manuscript and cannot be evaluated. Additionally, the methods of the RNAseq are not sufficiently described and lack critical details. For example, what was the normalization performed, and which groups were compared to identify differentially expressed genes? It would also be worthwhile to describe how animals were identified for RNAseq-were those animals representative of their groups across other measures?

We acknowledge the reviewers' comments on the RNAseq analysis and would like to provide additional insights into our rationale and choices for this analysis. The primary aim of our RNAseq analysis was to offer supplementary evidence in support of the broader context of our paper. Rather than focusing on specific genes, our aim was to assess potential alterations in transcription within genes triplicated in the mouse model and explore differentially expressed genes across the entire genome. Therefore, we conducted a global analysis of the triplicated genes using a PCA and analyzed the differentially expressed genes across the entire genome as shown in Supplementary Table S14. The table was originally included as a separate Excel file but apparently it was not received by the reviewers. We have contacted the eLife editorial to ensure its inclusion in the current version. Furthermore, we have modified the text to clarify that both the triplicated genes and the entire genome were analyzed.

Regarding the use of cerebellum instead of hippocampus, we agree with the reviewers that the hippocampus is a major tissue of interest in the study of Down Syndrome since it mostly relates to cognition. Trisomic patients, however, also display other typical features such as for example a delay in the acquisition of motor skills. Here we decided to focus on the cerebellum as it is primarily associated to the locomotor system but also plays a role in other cognitive functions such as language processing and memory. Furthermore, at the time of the RNAseq analysis, the mice were 8 months old, equivalent to the adult human stage, and previous studies have shown transcriptomic alterations in this tissue and mouse model (Olmos-Serrano et al., 2016; Saran et al., 2003).

The lack of observable differences between WT and Ts65Dn mice in our PCA analysis may be attributed to several factors as discussed in our article. First, the high variability within each group, inherent to the complexity of DS, may obscure inter-group differences. Additionally, the subtlety of gene expression differences between WT and trisomic mice in the set of triplicated genes, as suggested by other transcriptomics studies on DS (Aït Yahya-Graison et al., 2007; Lyle et al., 2004; Olmos-Serrano et al., 2016; Saran et al., 2003), may contribute to the limited distinctions observed. Furthermore, regarding treatment effects, the timing of the RNAseq analysis should be considered since it was conducted at the endpoint, three months after treatment cessation. This temporal aspect could imply that the effects of the drug are not persistent, and a molecular memory might not be formed and maintained.

Nevertheless, we appreciate the reviewers' constructive comments and acknowledge the potential for more stringent bioinformatic analyses. While our intention was to provide an initial, global perspective, we are eager to support further investigations that delve deeper into the complexities of DS-related molecular mechanisms. Consequently, the dataset is available for other researchers to explore more specific questions upon request.

Finally, we have updated the methods section of the article to offer more detailed information on RNAseq processing and analysis. We have also clarified that all the surviving mice were included in the analysis.

Recommendations for the authors:

(1) Please add power calculations for each of the assessments.

We would like to clarify that we had already conducted power calculations as part of the initial planning and design phase of our study. After data acquisition and analysis, we have utilized appropriate statistical methods to interpret the results based on the data we have collected. Given that we had conducted a priori power calculations prior to data collection and that our analysis is based on the acquired data, we do not see the added value in including post hoc power calculations. Our primary focus has been on performing the correct statistical analyses to accurately interpret the results and draw meaningful conclusions.

(2) Introduction has some excessive references for each statement, which are not necessary. For instance: lines 67-73 are only references for 1 statement and lines 74-76 are references for a 2nd statement in the same sentence.

We have removed redundant references.

(3) Introduction: Lines 136-146 Gene names need to be spelled out, not just the IDs. Were these studies done in human or mouse models of DS?

We have spelled out the names of the genes.

(4) Why was brain volume and brain structure size normalized to body weight, not clearly explained?

The choice to normalize brain volume and brain structure size to body weight was a deliberate decision made to address potential confounding factors in our study. In the case of trisomic (TS) mice, they are generally smaller in size compared to their wild-type (WT) counterparts. The same may hold true for sex-related size differences. Without normalization, assessing brain volume and structure size could be misleading, as it might reflect the differences in overall body size rather than providing insights into the specific aspects of brain structure that we aimed to investigate. We have clarified this in the methods section.

(5) In cognitive tests, some of the WT data represented in Figure 3 does not match supplemental findings. Again power calculations may indicate a higher number of WT mice are needed to clarify this discrepancy.

We appreciate the reviewers' observation regarding the disparities between the data presented in Figure 3 and the supplemental figures. We would like to clarify that these variations are a result of the distinct analytical approaches employed in the two sets of data.

In Figure 3 and all main figures, the data were analyzed using multivariate tests, which consider multiple variables simultaneously and are particularly suited for investigating the collective impact of multiple factors. Conversely, the results shown in the supplementary figures were derived from univariate tests, which focus on individual variables and are well-suited for addressing specific questions related to each variable in isolation. The discrepancies between the data in the main figures and the supplementary figures can be attributed to the differences in the analytical methods chosen.

As for the suggestion of conducting power calculations to address the observed differences, we believe that the differences in data are inherent to the distinct analytical strategies and the specific research questions each analysis intended to answer. Power calculations may not be the most suitable approach in this context, as they pertain to sample size planning for hypothesis testing and may not reconcile the inherent dissimilarity between multivariate and univariate analyses.

Aït Yahya-Graison, E., Aubert, J., Dauphinot, L., Rivals, I., Prieur, M., Golfier, G., . . . Potier, M. C. (2007). Classification of human chromosome 21 gene-expression variations in Down syndrome: impact on disease phenotypes. Am J Hum Genet, 81(3), 475-491. https://doi.org/10.1086/520000

Lyle, R., Gehrig, C., Neergaard-Henrichsen, C., Deutsch, S., & Antonarakis, S. E. (2004). Gene expression from the aneuploid chromosome in a trisomy mouse model of down syndrome. Genome Res, 14(7), 1268-1274. https://doi.org/10.1101/gr.2090904

Olmos-Serrano, J. L., Kang, H. J., Tyler, W. A., Silbereis, J. C., Cheng, F., Zhu, Y., . . . Sestan, N. (2016). Down Syndrome Developmental Brain Transcriptome Reveals Defective Oligodendrocyte Differentiation and Myelination. Neuron, 89(6), 1208-1222. https://doi.org/10.1016/j.neuron.2016.01.042

Saran, N. G., Pletcher, M. T., Natale, J. E., Cheng, Y., & Reeves, R. H. (2003). Global disruption of the cerebellar transcriptome in a Down syndrome mouse model. Hum Mol Genet, 12(16), 2013-2019. https://doi.org/10.1093/hmg/ddg217

Author Response

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

Public Reviews:

Reviewer #1:

Summary:

In this study, Yan et al. investigate the molecular bases underlying mating type recognition in Tetrahymena thermophila. This model protist possesses a total of 7 mating types/sexes and mating occurs only between individuals expressing different mating types. The authors aimed to characterize the function of mating type proteins (MTA and MTB) in the process of self- and non-self recognition, using a combination of elegant phenotypic assays, protein studies, and imaging. They showed that the presence of MTA and MTB in the same cell is required for the expression of concavalin-A receptors and for tip transformation - two processes that are characteristic of the costimulation phase that precedes cell fusion. Using protein studies, the authors identify a set of additional proteins of varied functions that interact with MTA and MTB and are likely responsible for the downstream signaling processes required for mating. This is a description of a fascinating self- and non-self-recognition system and, as the authors point out, it is a rare example of a system with numerous mating types/sexes. This work opens the door for the further understanding of the molecular bases and evolution of these complex recognition systems within and outside protists.

The results shown in this study point to the unequivocal requirement of MTA and MTB proteins for mating. Nevertheless, some of the conclusions regarding the mode of functioning of these proteins are not fully supported and require additional investigation.

Strengths:

(1) The authors have established a set of very useful knock-out and reporter lines for MT proteins and extensively used them in sophisticated and well-designed phenotypic assays that allowed them to test the role of these proteins in vivo.

(2) Despite their apparent low abundance, the authors took advantage of a varied set of protein isolation and characterization techniques to pinpoint the localization of MT proteins to the cell membrane, and their interaction with multiple other proteins that could be downstream effectors. This opens the door for the future characterization of these proteins and further elucidation of the mating type recognition cascade.

Weaknesses:

The manuscript is structured and written in a very clear and easy-to-follow manner. However, several conclusions and discussion points fall short of highlighting possible models and mechanisms through which MT proteins control mating type recognition:

(1) The authors dismiss the possibility of a "simple receptor-ligand system", even though the data does not exclude this possibility. The model presented in Figure 2 S1, and on which the authors based their hypothesis, assumes the independence of MTA and MTB proteins in the generation of the intracellular cascade. However, the results presented in Figure 2 show that both proteins are required to be active in the same cell. Coupled with the fact that MTA and MTB proteins interact, this is compatible with a model where MTA would be a ligand and MTB a receptor (or vice-versa), and could thus form a receptor-ligand complex that could potentially be activated by a non-cognate MTA-MTB receptor-ligand complex, leading to an intracellular cascade mediated by the identified MRC proteins. As it stands, it is not clear what is the proposed working model, and it would be very beneficial for the reader for this to be clarified by having the point of view of the authors on this or other types of models.

We are very grateful that Reviewer #1 proposed the possibility that MTA and MTB form a receptor-ligand complex in which one acting as the ligand and the other as the receptor. We considered this hypothesis when asking how dose MTRC function, too. However, our current results do not support this idea. For instance, if MTA were a ligand and MTB a receptor, we would expect a mating signal upon treatment with MTAxc protein, but not with MTBxc. Contrary to this expectation, our experiments revealed that both MTAxc and MTBxc exhibit very similar effects (Figure 5, green and blue), and their combined treatment produces a stronger effect (Figure 5, teal). This suggests a mixed function for both proteins. (We incorporated this discussion into the revised version [line 120-121, 240-244].) It is pity that our current knowledge does not provide a detailed molecular mechanism for this intricate system. We are actively investigating the protein structures of MTA, MTB, and the entire MTRC, hoping to gain deeper insights into the molecular functions of MTA and MTB.

Additionally, we also realized that the expression we used in the previous version, “simple receptor-ligand model”, is not clearly defined. As Reviewer #1 pointed out, in this section, we examined whether the individual proteins of MTA and MTB act as a couple of receptor and ligand. We think this is the simplest possibility as a null hypothesis for Tetrahymena mating-type recognition. We have clarified it in the revised version (line 90-91, 104-106). According to this section, we proposed that MTA and MTB may form a complex that serves as a recognizer (functioning as both ligand and receptor) (line 117-118).

(2) The presence of MTA/MTB proteins is required for costimulation (Figure 2), and supplementation with non-cognate extracellular fragments of these proteins (MTAxc, or MTBxc) is a positive stimulator of pairing. However, alone, these fragments do not have the ability to induce costimulation (Figure 5). Based on the results in Figures 5 and 6 the authors suggest that MT proteins mediate both self and non-self recognition. Why do MTAxc and MTBxc not induce costimulation alone? Are any other components required? How to reconcile this with the results of Figure 2? A more in-depth interpretation of these results would be very helpful, since these questions remain unanswered, making it difficult for the reader to extract a clear hypothesis on how MT proteins mediate self- and non-self-recognition.

Several factors could contribute to the inability of MTA/Bxc to induce costimulation. It is highly likely that additional components are necessary, given that MTA/B form a protein complex with other proteins. Moreover, the expression of MTA/Bxc in insect cells, compared with Tetrahymena, might result in differences in post-translational modifications. Additionally, there are variations in protein conditions; on the Tetrahymena membrane, these proteins are arranged regularly and concentrated in a small area, while MTA/Bxc is randomly dispersed in the medium. The former condition could be more efficient. If there is a threshold required to stimulate a costimulation marker, MTA/Bxc may fail to meet this requirement. Much more studies are needed to fully answer this question. We acknowledged this limitation in the revised version (line 244-248).

Reviewer #2:

This manuscript reports the discovery and analysis of a large protein complex that controls mating type and sexual reproduction of the model ciliate Tetrahymena thermophila. In contrast to many organisms that have two mating types or two sexes, Tetrahymena is multi-sexual with 7 distinct mating types. Previous studies identified the mating type locus, which encodes two transmembrane proteins called MTA and MTB that determine the specificity of mating type interactions. In this study, mutants are generated in the MTA and MTB genes and mutant isolates are studied for mating properties. Cells missing either MTA or MTB failed to co-stimulate wild-type cells of different mating types. Moreover, a mixture of mutants lacking MTA or MTB also failed to stimulate. These observations support the conclusion that MTA and MTB may form a complex that directs mating-type identity. To address this, the proteins were epitope-tagged and subjected to IP-MS analysis. This revealed that MTA and MTB are in a physical complex, and also revealed a series of 6 other proteins (MRC1-6) that together with MTA/B form the mating type recognition complex (MTRC). All 8 proteins feature predicted transmembrane domains, three feature GFR domains, and two are predicted to function as calcium transporters. The authors went on to demonstrate that components of the MTRC are localized on the cell surface but not in the cilia. They also presented findings that support the conclusion that the mating type-specific region of the MTA and MTB genes can influence both self- and non-self-recognition in mating.

Taken together, the findings presented are interesting and extend our understanding of how organisms with more than two mating types/sexes may be specified. The identification of the six-protein MRC complex is quite intriguing. It would seem important that the function of at least one of these subunits be analyzed by gene deletion and phenotyping, similar to the findings presented here for the MTA and MTB mutants. A straightforward prediction might be that a deletion of any subunit of the MRC complex would result in a sterile phenotype. The manuscript was very well written and a pleasure to read.

Thanks for the valuable comments and suggestions. We are currently in the process of constructing deletion strains for these genes. As of now, we have successfully obtained ΔMRC1-3 and MRC4-6 knockdown strains. Our preliminary observations indicate that ΔMRC1-3 strains are unable to undergo mating. However, we prefer not to include these results in the current manuscript, as we believe that more comprehensive studies are still needed.

Reviewer #3:

The authors describe the role, location, and function of the MTA and MTB mating type genes in the multi-mating-type species T. thermophila. The ciliate is an important group of organisms to study the evolution of mating types, as it is one of the few groups in which more than two mating types evolved independently. In the study, the authors use deletion strains of the species to show that both mating types genes located in each allele are required in both mating individuals for successful matings to occur. They show that the proteins are localized in the cell membrane, not the cilia, and that they interact in a complex (MTRC) with a set of 6 associated (non-mating type-allelic) genes. This complex is furthermore likely to interact with a cyclin-dependent kinase complex. It is intriguing that T. thermophila has two genes that are allelic and that are both required for successful mating. This coevolved double recognition has to my knowledge not been described for any other mating-type recognition system. I am not familiar with experimental research on ciliates, but as far as I can judge, the experiments appear well performed and mostly support the interpretation of the authors with appropriate controls and statistical analyses.

The results show clearly that the mating type genes regulate non-self-recognition, however, I am not convinced that self-recognition occurs leading to the suppression of mating. An alternative explanation could be that the MTA and MTB proteins form a complex and that the two extracellular regions together interact with the MTA+MTB proteins from different mating types. This alternative hypothesis fits with the coevolution of MTA and MTB genes observed in the phylogenetic subgroups as described by Yan et al. (2021 iScience). Adding MTAxc and/or MTBxc to the cells can lead to the occupation of the external parts of the full proteins thereby inhibiting the formation of the complex, which in turn reduces non-self interactions. Self-recognition as explained in Figure 2S1 suggests an active response, which should be measurable in expression data for example. This is in my opinion not essential, but a claim of self-recognition through the MTA and MTB should not be made.

We express our gratitude to Reviewer #3 for proposing the occupation model and have incorporated this possibility into the manuscript. We believe it is possible that occupation may serve as the molecular mechanism through which self-recognition negatively regulates mating. If there is a physical interaction between mating-type proteins of the same type, but this interaction blocks the recognition machinery rather than initiating mating, it can be considered a form of self-recognition. This aligns with the observation that strains expressing MTA/B6 and MTB2 mate normally with WT cells of all mating types except for VI and II (line 203-204). A concise discussion on this topic is included in the manuscript (line 288-293, 659-661). We are actively investigating the downstream aspects of mating-type recognition, and we hope to provide further insights into this question soon.

The authors discuss that T. thermophila has special mating-type proteins that are large, while those of other groups are generally small (lines 157-160 and discussion). The complex formed is very large and in the discussion, they argue that this might be due to the "highly complex process, given that there are seven mating types in all". There is no argument given why large is more complex, if this is complex, and whether more mating types require more complexity. In basidiomycete fungi, many more mating types than 7 exist, and the homeodomain genes involved in mating types are relatively small but highly diverse (Luo et al. 1994 PMID: 7914671). The mating types associated with GPCR receptors in fungi are arguably larger, but again their function is not that complex, and mating-type specific variations appear to evolve easily (Fowler et al 2004 PMID: 14643262; Seike et al. 2015 PMID: 25831518). The large protein complex formed is reminiscent of the fusion patches that develop in budding or fission yeasts. In these species, the mating type receptors are activated by ligand pheromones from the opposite mating type that induce polarity patch formation (see Sieber et al. 2023 PMID: 35148940 for a recent review). At these patches, growth (shmooing) and fusion occur, which is reminiscent (in a different order) of the tip transformation in T. thermophilia. The fusion of two cells is in all taxa a dangerous and complex event that requires the evolution of very strict regulation and the existence of a system like the MTRC and cyclin-dependent complex to regulate this process is therefore not unexpected. The existence of multiple mating types should not greatly complicate the process, as most of the machinery (except for the MTA and MTB) is identical among all mating types.

We are very grateful that Reviewer #3 provide this insightful view and relevant papers. In response to the feedback, we removed the sentences regarding “multiple mating types greatly complicate the process” in the revised version. Instead, we have introduced a discussion section comparing the mating systems of yeasts and Tetrahymena (line 279-286).

The Tetrahymena/ciliate genetics and lifecycle could be better explained. For a general audience, the system is not easy to follow. For example, the ploidy of the somatic nucleus with regards to the mating type is not clear to me. The MAC is generally considered "polyploid", but how does this work for the mating type? I assume only a single copy of the mating type locus is available in the MAC to avoid self-recognition in the cells. Is it known how the diploid origin reduces to a single mating type? This does not become apparent from Cervantes et al. 2013.

In T. thermophila, the MIC (diploid) contains several mating-type gene pairs (mtGP, i.e., MTA and MTB) organized in a tandem array at the mat locus on each chromosome. In sexual reproduction, the new MAC of the progeny develops from the fertilized MIC through a series of genome editing events, and its ploidy increases to ~90 by endoreduplication. During this process, mtGP loss occurs, resulting in only one mtGP remaining on the MAC chromosome. The mating-type specificity of mtGPs on each chromosome within one nucleus becomes relatively pure through intranuclear coordination. After multiple assortments (possibly caused by MAC amitosis during cell fission), only mtGPs of one mating-type specificity exist in each cell, determining the cell’s mating type.

It is pity that the exact mechanisms involved in this complicated process remain a black box. The loss of mating-type gene pairs is hypothesized to involve a series of homologous recombination events, but this has not been completely proven. Furthermore, there is no clear understanding of how intranuclear coordination and assortment are achieved. While we have made observations confirming these events, a breakthrough in understanding the molecular mechanism is yet to be achieved.

We included more information in the revised version (line 672-683). Given the complexity of these unusual processes, we recommend an excellent review by Prof. Eduardo Orias (PMID: 28715961), which offers detailed explanations of the process and related concepts (line 685-686).

Also, the explanation of co-stimulation is not completely clear (lines 49-60). Initially, direct cell-cell contact is mentioned, but later it is mentioned that "all cells become fully stimulated", even when unequal ratios are used. Is physical contact necessary? Or is this due to the "secrete mating-essential factors" (line 601)? These details are essential, for interpretation of the results and need to be explained better.

Sorry that we didn’t realize the term “contact” is not precise enough. In Tetrahymena, physical contact is indeed necessary, but it can refer to temporary interactions. Unlike yeast, Tetrahymena cells exhibit rapid movement, swimming randomly in the medium. Occasionally, two cells may come into contact, but they quickly separate instead of sticking together. Even newly formed loose pairs often become separated. As a result, one cell can come into contact with numerous others and stimulate them. We have clarified this aspect in the revised version (line 50-51, 57).

Abstract and introduction: Sexes are not mating types. In general, mating types refer to systems in which there is no obvious asymmetry between the gametes, beyond the compatibility system. When there is a physiological difference such as size or motility, sexes are used. This distinction is of importance because in many species mating types and sexes can occur together, with each sex being able to have either (when two) or multiple mating types. An example are SI in angiosperms as used as an example by the authors or mating types in filamentous fungi. See Billiard et al. 2011 [PMID: 21489122] for a good explanation and argumentation for the importance of making this distinction.

We have clarified the expression in the revised version (line 20, 38, 40, 45).

Recommendations for the authors:

Reviewer #1:

I really enjoyed reading this manuscript and I think a few tweaks in the writing/data presentation could greatly improve the experience for the reader:

(1) The information about your previous work in identifying downstream proteins CDK19, CYC9, and CIP1 (lines 170-173) could be directly presented in the introduction.

We have moved this information in the introduction in the revised version (line 74-77).

(2) For a reader who is not familiar with Tetrahymena, a few more details on how reporter and knock-out lines are generated would be beneficial.

We introduced the knock-out method in Figure 2 – figure supplement 1B, HA-tag method in Figure 3A, and MTB2-eGFP construction method in Figure 4E. In addition, we introduced how co-stimulation markers observed in Materials and Methods (line 404-410)

(3) Figures 5 and 6: clarify the types of pairing and treatments that were done directly in the figure (eg. adding additional labels). As of now, it is necessary to go through the text and legend to try and understand in detail what was done.

Cell types and treatments were directly introduced in the revised figure (Figure 5 and 6).

(4) The logical transition in lines 136-142 is hard to follow.

We rewrote this paragraph in the revised version (lines 143-156). Additionally, we added a figure to illustrate the theoretical mating-type recognition model between WT cells and ΔCDK19, ΔCYC9 cells, MTAxc, MTBxc proteins, and ΔMTA, ΔMTB cells (Figure 2 – figure supplement 1D-G).

(5) Lines 191-196: the fact that cells expressing multiple mating types can self goes against an active self-rejection system - if this is the case there should be self-rejection among all expressed mating types. Unless non-self recognition is an active process and self-recognition is simply the absence of non-self recognition. The authors briefly mention this in lines 263-265, but it would be interesting to expand and clarify this.

We appreciate that Reviewer #1 notice the interesting selfing phenotype of the MTB2-eGFP (MTVI background) strain. We further discussed it in the revised manuscript (line 298-306).

(6) The authors briefly mention the possibility of different mating types using different recognition mechanisms (lines 255-260), based on the big differences in the size of the mating-specific region of MT proteins. Following this and the weakness nr. 2, I think it would be pertinent to gather and present more information on the properties and structures of the mating-type specific regions of MT proteins. Simple in silico analysis of motifs, structure, etc. could help clarify the role of these regions. It seems more parsimonious that MT proteins would have variable mating type specific regions that account for the recognition of the different mating types, and conserved cytoplasmic functions that could trigger a single downstream signaling cascade. It would be interesting to know the authors' opinion on this.

We are very grateful for this suggestion. Actually, we are currently working on determining the 3D structure of MTRC. The Alphafold2 prediction indicates that the MT-specific region is comprised of seven global β-sheets, resembling the structure of immunoglobulins (Ig). Our most recent cryo-EM results have revealed a ~15Å structure, aligning well with the prediction. However, the main challenge lies in the low expression levels, both in Tetrahymena and insect/mammal cells. We anticipate obtaining more detailed results soon. Therefore, we prefer to present the MT recognition model with robust experimental evidence in the future, and didn’t discuss too much on this aspect in the current manuscript.

(7) Adding a figure including a proposed model, as well as expanding the discussion on the points presented as "weaknesses" would help clarify the ideas/hypothesis on how the mating recognition works. I think this would really elevate the paper and help highlight the results.

We added a figure to introduce the model and the weaknesses in the revised version (Figure 7, line 656-665).

(8) Line 202-203: It is far-fetched to infer subcellular localization based on the data presented here, couterstaining with other dyes and antibodies specific to certain cell components, as well as negative control images, are required.

Thanks for the suggestion. We attempted to stain cell components using various dyes and antibodies. Unfortunately, we found that cell surface and cilia (especially oral cilia) is very easy to give a false positive signal. We think this issue seriously affects the credibility of the results. It may seem like splitting hairs, but we are trying to be precise.

Meanwhile, we still believe the mating-type proteins localizes to cell surface because MTA-HA is identified in the isolated cell surface proteins.

Regarding negative control, as shown in Fig. 4G, where a MTB2-eGFP cell is pairing with a WT cell, no GFP signal is observed in the WT cell.

(9) Lines 131: clarify the sentence - expression of Con-A receptors requires both MTA and MTB (MTA to receive the signal).

We modified the sentence in the revised version (line 139-140).

Reviewer #2:

Minor points.

(1) Line 194-196. Why are these cells able to self?

These cells able to self may because the MTRC contain heterotypic mating-type proteins (MTA6 and MTB2), which activate mating when they interact with another heterotypic MTRC (line 207-208).

(2) Line 232. What do the authors mean by the term synergistic effect here? Definition and statistics?

Sorry about the confusion. The synergistic effect refers to the effect of MTAxc and MTBxc become stronger when using together. We clarified it in the revised version (line 232).

(3) For Figure 4 panel D, are there antibodies that are available as a control for cilia? If so, then blotting this membrane would show that cilia-associated proteins are in the cilia preparation, which is a standard control for sub-cellular fractionation.

Thanks for the suggestion. Unfortunately, we didn’t find a suitable cilia-specific antibody yet. Instead, we employed MS analysis to confirm the presence of cilia proteins in this sample (line 195-196, Figure 4–Source data 1). We also observed the sample under the microscope, which directly revealed the presence of cilia (Figure 4C).

(4) At least one reference cited in the text was not present in the reference list. The authors should go through the references cited to ensure that all have made it into the reference list.

We have checked all the references.

Some minor edits:

(1) MTA and MTB are presented in both roman and italics (e.g. line 209) in the manuscript. Maybe all should be in italics? Or is this a distinction between the gene and the protein?

The italics word (MTA) refers to gene, and non-italics word (MTA) refers to protein.

(2) Line 251. Change "achieving" to "achieve".

We have corrected this word (line 266).

Reviewer #3:

Line 101. It would help to explain this expectation earlier in this paragraph.

We explained the expectation in the revised version (line 92-97, 104-106).

Line 109. How is a co-receptor different from the MTRC complex?

We have rewritten the relevant sentences to enhance clarity (line 116-119). The molecular function of the MTRC complex could involve acting as a co-receptor or recognizer (functioning as both ligand and receptor). Based on the results presented in this section, we propose that MTA and MTB may function as a complex, but the confirmation of this hypothesis (MTRC) is provided in a later section. Therefore, we did not use the term “MTRC” here. These sentences briefly discuss the molecular function of this complex and explain why MTRC does not appear to function as a co-receptor.

Line 251: which "dual approach" is referred to?

Dual approach is referred to both self and non-self recognition. We explained it in the revised version (line 265-266).

Line 258: what "different mechanisms" do the authors have in mind? Why would a different mechanism be expected? The different sizes could have evolved for (coevolutionary?) selection on the same mechanism.

Sorry about the confusion. We clarified it in the revised version (line 269-278).

What we intended to express is that we are uncertain whether the mating-type recognition model we discovered in T. thermophila is applicable to all Tetrahymena species due to significant differences in the length of the mating-type-specific region. We believe it is important to highlight this distinction to avoid potential misinterpretations in future studies involving other Tetrahymena species. At the same time, we look forward to future research that may provide insights into this question.

Fig 2 C&D. Is it correct that these figures show the strains only after 'preincubation'? This is not apparent from the caption of the text. Additionally, the order of the images is very confusing. Write in the figures (so not just in the caption) what the sub-script means.

These panels are re-organized in the revised version (Fig. 2C&D). There are three kinds of pictures: “not incubated”, “WT pre-incubated by mutant” and “mutant pre-incubated by WT”.

The methods used to generate Figure 5 are not clearly described. I understand that the obtained xc proteins were added to the cells, and then washed, after which a test was performed mixing WT-VI and WT-VII cells. Were both cells treated? Or only one of the strains? The explanation for the reused washing medium is not clear and the method is not indicated.

Both cells are treated. More details are provided in the revised manuscript (line 230-231, 633-634, 637-639, Fig. 5). To prepare the starvation medium containing mating-essential factors, cells were starved in fresh starvation medium for ~16 hours. Subsequently, cells were removed by three rounds of centrifugation (1000 g, 3 min) (line 330-332).

In general, the figures are difficult to understand without repeated inquiries in the captions. Give more information in the figures themselves.

More information is introduced in the figure (Fig. 2C, Fig. 3B, Fig. 4A, B, D, Fig. 5 and Fig. 6).

Author Response

Reviewer #1 (Public Review):

Summary:

This paper suggests to apply intrinsically-motivated exploration for the discovery of robust goal states in gene regulatory networks.

Strengths:

The paper is well written. The biological motivation and the need for such methods are formulated extraordinarily well. The battery of experimental models is impressive.

We thank the reviewer for sharing interest in the research problem and for recognizing the strengths of our work.

Weaknesses:

(1) The proposed method is compared to the random search. That says little about the performance with regard to the true steady-state goal sets. The latter could be calculated at least for a few simple ODE (e.g., BIOMD0000000454, `Metabolic Control Analysis: Rereading Reder'). The experiment with 'oscillator circuits' may not be directly interpolated to the other models.

The lack of comparison to the ground truth goal set (attractors of ODE) from arbitrary initial conditions makes it hard to evaluate the true performance/contribution of the method. A part of the used models can be analyzed numerically using JAX, while there are models that can be analyzed analytically.

"...The true versatility of the GRN is unknown and can only be inferred through empirical exploration and proxy metrics....": one could perform a sensitivity analysis of the ODEs, identifying stable equilibria. That could provide a proxy for the ground truth 'versatility'.

We agree with the reviewer that one primary concern is to properly evaluate the effectiveness of the proposed method. However, as we move toward complex pathways, knowledge of the “true” steady-state goal sets is often unknown which is where the use of machine learning methods as the one we propose are particularly interesting (but challenging to evaluate).

For simple models whose true steady-state distribution can be derived numerically and/or analytically, it is very likely that their exploration will be much simpler and this is not where a lot of improvement over random search may be found, which explains our focus on more complex models. While we agree that it is still interesting to evaluate exploration methods on these simple models for checking their behavior, it is not clear how to scale this analysis to the targeted more complex systems.

For systems whose true steady state distribution cannot be derived analytically or numerically, we believe that random search is a pertinent baseline as it is commonly used in the literature to discover the attractors/trajectories of a biological network. For instance, Venkatachalapathy et al. [1] initialize stochastic simulations at multiple randomly sampled starting conditions (which is called a kinetic Monte Carlo-based method) to capture the steady states of a biological system. Similarly, Donzé et al. [29] use a Monte Carlo approach to compute the reachable set of a biological network «when the number of parameters is large and their uncertain range is not negligible».

(2) The proposed method is based on `Intrinsically Motivated Goal Exploration Processes with Automatic Curriculum Learning', which assumes state action trajectories [s_{t_0:t}, a_{t_0:t}], (2.1 Notations and Assumptions' in the IMGEP paper). However, the models used in the current work do not include external control actions, but rather only the initial conditions can be set. It is not clear from the methods whether IMGEP was adapted to this setting, and how the exploration policy was designed w/o actual time-dependent actions. What does "...generates candidate intervention parameters to achieve the current goal....", mean considering that interventions 'Sets the initial state...' as explained in Table 2?

We thank the reviewer for asking for clarification, as indeed the IMGEP methodology originates from developmental robotics scenarios which generally focus on the problem of robotic sequential decision-making, therefore assuming state action trajectories as presented in Forestier et al. [65]. However, in both cases, note that the IMGEP is responsible for sampling parameters which then govern the exploration of the dynamical system. In Forestier et al. [65], the IMGEP also only sets one vector at the start (denoted θ∈Θ) which was specifying parameters of a movement (like the initial state of the GRN), which was then actually produced with dynamic motion primitives which are dynamical system equations similar to GRN ODEs, so the two systems are mathematically equivalent. More generally, while in our case the “intervention” of the IMGEP (denoted i ∈I) only controls the initial state of the GRN, future work could consider more advanced sequential interventions simply by setting parameters of an action policy π_i at the start which could be called during the GRN’s trajectory to sample control actions π_i (a_(t+1) 〖|s〗_(t0:t+1),a_t) where s_t would be the state of the GRN. In practice this would also require setting only one vector at the start, so it would remain the same exploration algorithm and only the space of parameters would change, which illustrates the generality of the approach.

(3) Fig 2 shows the phase space for (ERK, RKIPP_RP) without mentioning the typical full scale of ERK, RKIPP_RP. It is unclear whether the path from (0, 0) to (~0.575, ~3.75) at t=1000 is significant on the typical scale of this phase space. is it significant on the typical scale of this phase space?

The purpose of Figure 2 is to illustrate an example of GRN trajectory in transcriptional space, and to illustrate what “interventions” and “perturbations” can be in that context. To that end we have used the fixed initial conditions provided in the BIOMD0000000647, replicating Figure 5 of Cho et al. [56]. While we are not sure of what the reviewer means with “typical” scale of this phase space, we would like to point reviewer toward Figure 8 which shows examples of certain paths that indeed reach further point in the same phase space (up to ~10μM in RKIPP_RP levels and ~300μM in ERK levels). However, while the paths displayed in Figure 8 are possible (and were discovered with the IMGEP), note that they may be “rarer” to occur naturally in the sense that a large portion of the tested initial conditions with random search tend to converge toward smaller (ERK, RKIPP_RP) steady-state values similar to the ones displayed in Figure 2.

(4) Table 2:

a) Where is 'effective intervention' used in the method?

b) in my opinion 'controllability', 'trainability', and 'versatility' are different terms. If their correspondence is important I would suggest to extend/enhance the column "Proposed Isomorphism". otherwise, it may be confusing.

a) We thank the reviewer for pointing out that “effective intervention” is not explicitly used in the method. The idea here is that as we are exploring a complex dynamical system (here the GRN), some of the sampled interventions will be particularly effective at revealing novel unseen outcomes whereas others will fail to produce a qualitative change to the distribution of discovered outcomes. What we show in this paper, for instance in Figure 3a and Figure 4, is that the IMGEP method is particularly sample-efficient in finding those “effective interventions”, at least more than a random exploration. However we agree that the term “effective intervention” is ambiguous (does not say effective in what) and propose to replace it with “salient intervention” in the revised version.

b) We thank the reviewer for highlighting some confusing terms in our chosen vocabulary, and we will try to clarify those terms in the revised version. We agree that controllability/trainability and versatility are not exactly equivalent concepts, as controllability/trainability typically refers to the amount to which a system is externally controllable/trainable whereas versatility typically refers to the inherent adaptability or diversity of behaviors that a system can exhibit in response to inputs or conditions. However, they are both measuring the extent of states that can be reached by the system under a distribution of stimuli/conditions, whether natural conditions or engineered ones, which is why we believe that their correspondence is relevant.

I don't see how this table generalizes "concepts from dynamical complex systems and behavioral sciences under a common navigation task perspective".

We propose to replace “generalize” with “investigate” in the revised version.

Reviewer #2 (Public Review):

Summary:

Etcheverry et al. present two computational frameworks for exploring the functional capabilities of gene regulatory networks (GRNs). The first is a framework based on intrinsically-motivated exploration, here used to reveal the set of steady states achievable by a given gene regulatory network as a function of initial conditions. The second is a behaviorist framework, here used to assess the robustness of steady states to dynamical perturbations experienced along typical trajectories to those steady states. In Figs. 1-5, the authors convincingly show how these frameworks can explore and quantify the diversity of behaviors that can be displayed by GRNs. In Figs. 6-9, the authors present applications of their framework to the analysis and control of GRNs, but the support presented for their case studies is often incomplete.

Strengths:

Overall, the paper presents an important development for exploring and understanding GRNs/dynamical systems broadly, with solid evidence supporting the first half of their paper in a narratively clear way.

The behaviorist point of view for robustness is potentially of interest to a broad community, and to my knowledge introduces novel considerations for defining robustness in the GRN context.

We thank the reviewer for recognizing the strengths and novelty of the proposed experimental framework for exploring and understanding GRNs, and complex dynamical systems more generally. We agree that the results presented in the section “Possible Reuses of the Behavioral Catalog and Framework” (Fig 6-9) can be seen as incomplete along certain aspects, which we tried to make as explicit as possible throughout the paper, and why we explicitly state that these are “preliminary experiments”. Despite the discussed limitations, we believe that these experiments are still very useful to illustrate the variety of potential use-cases in which the community could benefit from such computational methods and experimental framework, and build on for future work.

Some specific weaknesses, mostly concerning incomplete analyses in the second half of the paper:

(1) The analysis presented in Fig. 6 is exciting but preliminary. Are there other appropriate methods for constructing energy landscapes from dynamical trajectories in gene regulatory networks? How do the results in this particular case study compare to other GRNs studied in the paper?

We are not aware of other methods than the one proposed by Venkatachalapathy et al. [1] for constructing an energy landscape given an input set of recorded dynamical trajectories, although it might indeed be the case. We want to emphasize that any of such methods would anyway depend on the input set of trajectories, and should therefore benefit from a set that is more representative of the diversity of behaviors that can be achieved by the GRN, which is why we believe the results presented in Figure 6 are interesting. As the IMGEP was able to find a higher diversity of reachable goal states (and corresponding trajectories) for many of the studied GRNs, we believe that similar effects should be observable when constructing the energy landscapes for these GRN models, with the discovery of additional or wider “valleys” of reachable steady states. We could indeed add other case studies in the supplementary to support the argument for the revised version.

Additionally, it is unclear whether the analysis presented in Fig. 6C is appropriate. In particular, if the pseudopotential landscapes are constructed from statistics of visited states along trajectories to the steady state, then the trajectories derived from dynamical perturbations do not only reflect the underlying pseudo-landscape of the GRN. Instead, they also include contributions from the perturbations themselves.

We agree that the landscape displayed Fig. 6C integrates contributions from the perturbations on the GRN’s behavior, and that it can shape the landscape in various ways, for instance affecting the paths that are accessible, the shape/depth of certain valleys, etc. But we believe that qualitatively or quantitatively analyzing the effect of these perturbations on the landscape is precisely what is interesting here: it might help 1) understand how a system respond to a range of perturbations and to visualize which behaviors are robust to those perturbations, 2) design better strategies for manipulating those systems to produce certain behaviors

(2) In Fig. 7, I'm not sure how much is possible to take away from the results as given here, as they depend sensitively on the cohort of 432 (GRN, Z) pairs used. The comparison against random networks is well-motivated. However, as the authors note, comparison between organismal categories is more difficult due to low sample size; for instance, the "plant" and "slime mold" categories each only have 1 associated GRN. Additionally, the "n/a" category is difficult to interpret.

We acknowledge that this part is speculative as stated in the paper: “the surveyed database is relatively small with respect to the wealth of available models and biological pathways, so we can hardly claim that these results represent the true distribution of competencies across these organism categories”. However, when further data is available, the same methodology can be reused and we believe that the resulting statistical analyses could be very informative to compare organismal (or other) categories.

(3) In Fig. 8, it is unclear whether the behavioral catalog generated is important to the intervention design problem of moving a system from one attractor basin to another. The authors note that evolutionary searches or SGD could also be used to solve the problem. Is the analysis somehow enabled by the behavioral catalog in a way that is complementary to those methods? If not, comparison against those methods (or others e.g. optimal control) would strengthen the paper.

We thank the reviewer for asking to clarify this point, which might not be clearly explained in the paper. Here the behavioral catalog is indeed used in a complementary way to the optimization method, by identifying a representative set of reachable attractors which are then used to define the optimization problem. For instance here, thanks to the catalog, we 1) were able to identify a “disease” region and several possible reachable states in that region and 2) use several of these states as starting points of our optimization problem, where we want to find a single intervention that can successfully and robustly reset all those points, as illustrated in Figure 8. Please note that given this problem formulation, a simple random search was used as an optimization strategy. When we mention more advanced techniques such as EA or SGD, it is to say that they might be more efficient optimizers than random search. However, we agree that in many cases optimizing directly will not work if starting from random or bad initial guess, and this even with EA or SGD. In that case the discovered behavioral catalog can be useful to better initialize this local search and make it more efficient/useful, akin to what is done in Figure 9.

(4) The analysis presented in Fig. 9 also is preliminary. The authors note that there exist many algorithms for choosing/identifying the parameter values of a dynamical system that give rise to a desired time-series. It would be a stronger result to compare their approach to more sophisticated methods, as opposed to random search and SGD. Other options from the recent literature include Bayesian techniques, sparse nonlinear regression techniques (e.g. SINDy), and evolutionary searches. The authors note that some methods require fine-tuning in order to be successful, but even so, it would be good to know the degree of fine-tuning which is necessary compared to their method.

We agree that the analysis presented in Figure 9 is preliminary, and thank the reviewer for the suggestion. We would first like to refer to other papers from the ML literature that have more thoroughly analyzed this issue, such as Colas et al. [74] and Pugh et al. [34], and shown the interest of diversity-driven strategies as promising alternatives. Additionally, as suggested by the reviewer, we added an additional comparison to the CMA-ES algorithm in order to complete our analysis. CMA-ES is an evolutionary algorithm which is self-adaptive in the optimization steps and that is known to be better suited than SGD to escape local minimas when the number of parameters is not too high (here we only have 15 parameters). However, our results showed that while CMA-ES explores more the solution space at the beginning of optimization than SGD does, it also ultimately converges into a local minima similarly to SGD. The best solution converges toward a constant signal (of the target b) but fails to maintain the target oscillations, similar to the solutions discovered by gradient descent. We tried this for a few hyperparameters (init mean and std) but always found similar results. We report the novel results at https://developmentalsystems.org/curious-exploration-of-grn-competencies/tuto2.html (bottom cell, Figure 4). We suggest including the updated figure and caption in the revised version.

Author Response

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

Reviewer #1 (Recommendations For The Authors):

This is significant work, and you should certainly make the best case you can on the weaknesses discussed.

We thank reviewer for this positive comment on the significance of our work. The referee indicates as weaknesses (i) that the force involving the bent or straight αI-helix is not readily apparent, (ii) the residue types were not varied in the helix mutations, and (iii) that the chemical shift perturbations are indirect observations.

We think we have tried to address a large part of these questions by being very careful in our analysis and by the discussion in the manuscript. The following remarks may help to clarify this further:

(i) The force emanating from the helix is e.g. visualized in the PC2 loadings in Figure 6E of the PCA carried on all observed SH3-SH2-KD resonances for all apo forms of the helix mutants. The SH2 residues identified by these loadings are in direct vicinity to the αI-helix. The respective PC2 scores correlate to 98% with the vmax of the catalytic reaction and to 94 % with the PC1 scores found for imatinib-induced opening. Importantly, the structure of the KD with the straight αI-helix indicates that mostly residues F516, Q517, S520, and I521 would clash with the SH2 domain in a closed core (Figure 6F). Thus, the expected clashes are in direct vicinity of the SH2 residues identified by the PC2 loadings as correlated to vmax and imatinib-induced opening. These data are completely orthogonal and show that most of the force is coming from residues F516, Q517, S520, and I521 in the αI-αI’ turn.

(ii) We agree that we mainly used truncations of the αI-helix to study its involvement in activation. Point (i) makes it clear that a larger part of the αI-helix effects is caused by steric clashes of the residues in the αI-αI’ turn. In the latter region, we don’t expect strong amino acid type-specific effects besides excluded volume. Due to expression problems, we could not vary the helix length between residues 519 and 534. However, in this region we introduced the amino acid type mutation E528K. The latter showed a clear specific effect. Further amino acid type-specific effects may be possible in this region. However, we expect that the identified electrostatic E528-R479 interaction is one of the most important interactions in this region.

(iii) We agree that chemical shift changes of individual resonances are often hard to interpret. However, we want to stress that our conclusions are all drawn from principal component analyses, which in all cases had as input well over 100 if not over 200 1H-15H resonances. The first two principal components of these analyses are robust averages over many residues, which reveal general correlated structural trends.

We assume that chemical shift deposition etc will be pursued.

We are currently depositing a larger collection of our Abl data to the “Biological Magnetic Resonance Data Bank (BMRB)”, which includes the NMR chemical shift data of the present work. A ‘collection’ will be a new feature of the BMRB, and we are in discussion with their staff. We will provide the accession codes as soon as possible (probably within the next month) to be included into the final version of the manuscript. We have amended the Data Availability Section accordingly.

Reviewer #2 (Recommendations For The Authors):

1) The overall discussion of the implications of the described allostery on kinase activation is provided through lenses of imatinib binding, which is used as an experimental trigger to disassemble the autoinhibited core. Can the authors elaborate in the Discussion on what event would play this role in the kinase catalytic cycle, communicating to helix I? Would dissociation of the myristate from the active site be hypothesized to be the first step in kinase activation? While I understand that certainty may be challenging to attain, it would be good to introduce some ideas into the Discussion.

We appreciate the reviewer’s suggestions for the discussion and added the following text to the Conclusion section:

"We have used here imatinib binding to the ATP-pocket as an experimental tool to disassemble the Abl regulatory core. Our previous analysis (Sonti et al., 2018) of the high-resolution Abl transition-state structure (Levinson et al., 2006) indicated that due to the extremely tight packing of the catalytic pocket, binding and release of the ATP and tyrosine peptide substrates is only possible if the P-loop and thereby the N-lobe move towards the SH3 domain by about 1–2 Å. This motion is of similar size and direction as the motion of the N-lobe observed in complexes with imatinib and other type II inhibitors (Sonti et al., 2018). From this we concluded that substrate binding opens the Abl core in a similar way as imatinib. The present NMR and activity data now clearly establish the essential role of the αI-helix both in the imatinib- and substrate-induced opening of the core, thereby further corroborating the similarity of both disassembly processes.

Notably, the used regulatory core construct Abl83-534 lacks the myristoylated N-cap. Although we have previously demonstrated that the latter construct is predominantly assembled (Skora et al., 2013), the addition of the myristoyl moiety is expected to further stabilize the assembled conformation in a similar way as asciminib.

Considering this mechanism, dissociation of myristoyl from the native Abl 1b core may be a first step during activation. However, it should be kept in mind that the Abl 1a isoform lacks the N-terminal myristoylation, and it is presently unclear whether other moieties bind to the myristoyl pocket of Abl 1a during cellular processes."

2) Can the authors comment more on the differentiation between assembled conformations induced by type I inhibitor binding vs apo forms (or AMP-PNP and allosteric inhibitor) reported in Figure 3B? The differences are clearly identified by PCA but not sufficiently discussed.

As indicated in the text, we think two structural effects are intermingled within PC2. Due to this admixture, it is hard to draw strong conclusions and we don’t want to expand on this too much. We have slightly modified the respective paragraph (p.7) as follows):

"As the affected residues react differently to perturbations by type I inhibitors and truncation of the αI’-helix (Figure 3A, right), we attribute this behavior to two effects intermixed into the PC2 detection: (i) a minor rearrangement of the SH3/KD N-lobe interface caused by filling of the ATP pocket with type I inhibitors, which in contrast to the stronger N-lobe motion induced by type II inhibitors does not yet lead to core disassembly and (ii) a small rearrangement of the SH2/KD C-lobe interface caused by shortening and mutations of the αI-helix."

3) The allosteric connection between active site inhibitor binding and the myristate/allosteric inhibitor binding has been observed in the past and noted before, in papers such as Zhang et al, Nature 2010. While the authors reference this paper, they do not acknowledge its specific findings or engage in a broader discussion of how their conclusions relate to this work.

We have modified the beginning of the Conclusion section:

"The allosteric connection between Abl ATP site and myristate site inhibitor binding has been noted before, albeit specific settings such as construct boundaries and the control of phosphorylation vary in published experiments. Positive and negative binding cooperativity of certain ATP-pocket and allosteric inhibitors has been observed in cellular assays and in vitro (Kim et al., 2023; Zhang et al., 2010). Furthermore, hydrogen exchange mass spectrometry has indicated changes around the unliganded ATP pocket upon binding of the allosteric inhibitor GNF-5 (Zhang et al., 2010). Here, we present a detailed high-resolution explanation of these allosteric effects via a mechanical connection between the kinase domain N- and C-lobes that is mediated by the regulatory SH2 and SH3 domains and involves the αI helix as a crucial element.

Specifically, we have established a firm correlation between the kinase activity of the Abl regulatory core, the imatinib (type II inhibitor)-induced disassembly of the core, which is caused by a force FKD–N,SH3 between the KD N-lobe and the SH3 domain, and a force FαI,SH2 exerted by the αI-helix towards the SH2 domain. The FαI,SH2 force is mainly caused by a clash of the αI-αI’ loop with the SH2 domain. Both the FKD–N,SH3 and FαI,SH2 force act on the KD/SH2SH3 interface and may lead to the disassembly of the core, which is in a delicate equilibrium between assembled and disassembled forms. As disassembly is required for kinase activity, the modulation of both forces constitutes a very sensitive regulation mechanism. Allosteric inhibitors such as asciminib and also myristoyl, the natural allosteric pocket binder, pull the αI-αI’ loop away from the SH2 interface, and thereby reduce the FαI,SH2 force and activity. Notably, all observations described here were obtained under nonphosphorylated conditions, as phosphorylation will lead to additional strong activating effects."

4) Figure 6 could do a better job of providing an illustration of steric clashes.

We have revised Figure 6, panel F, in order to better illustrate the steric clashes, and modified the legend accordingly.

5) There is a typo in line 5 from the top on page 11 (dash missing from "83534" superscript).

Thank you. This was fixed.

Author Response

Many thanks for handling our manuscript (eLife-RP-RA-2023-93968) entitled "Allosteric modulation of the CXCR4:CXCL12 axis by targeting receptor nanoclustering via the TMV-TMVI domain", by García-Cuesta et al. We are delighted to hear your willingness to consider our manuscript following appropriate revision. We have carefully read the referees' commentaries and have organized new experiments to address their specific queries.

Reviewer #1 (Public Review)

The computational methodology is going to be carefully reviewed. In particular to justify the software and techniques used in this manuscript. We will also describe the method for identifying the pocket on the CXCR4 structure as well as the workflow used to explain the transition from docking evaluation to MD analyses. Additionally, we will conduct experiments to enhance the results and address the specific feedback provided, ultimately improving the overall reliability.

Reviewer #2 (Public Review)

Although the paper was initiated by titrating the compounds in migration experiments, we are going to add new kinetics and titration of concentrations in these experiments. In addition, we are going to change the way in which we present the data from the singlemolecule tracking experiments. We will add a representative video of each experimental condition, and include some of the mean square displacement curves to support our data on the analysis of the diffusion coefficient (D1-4) to give a more conclusive view of receptor clustering. Regarding the tumorigenesis experiments we will include the individual data points and we will try to perform kinetics with distinct concentrations of the drug.

Author Response

Reviewer #1 (Public Review):

This manuscript from Kavanjoo et al examines the role of macrophages within the fetal liver beyond erythrocyte maturation. Using single-cell sequencing, high-resolution imaging, and inducible genetic deletion of yolk-sac (YS) derived macrophages, the authors demonstrate that heterogeneous fetal liver macrophages regulate erythrocyte enucleation, interact physically with fetal HSCs, and may regulate neutrophil accumulation in the fetal liver. The data as presented do not strongly support the authors’ conclusion that fetal macrophages in the liver regulate the HSC niche or granulopoiesis from HSCs.

Fetal-derived resident tissue macrophages are increasingly implicated in regulation of adult tissue function and homeostasis, but considerably less is known regarding the function of fetal macrophages during development. Macrophages in the fetal liver have been shown to form erythroblastic islands, where they regulate erythrocyte maturation. Here, the authors performed single-cell sequencing on fetal liver macrophages (Cd11b-lo) to gain insight into heterogeneity and utilized previously published pre-Mac signatures from the YS to focus on YS-derived macrophages. These clusters were then further cross-referenced with surface protein expression as determined by multidimensional flow cytometry to hone in on a very specific subset of three groups of F4/80hi macrophages defined by multiple surface markers. Fate-mapping with three models (Tnfrsf11a-Cre - YS pMAC derived; Ms4a3Cre - FL monocyte derived; CXCR4-Cre-ERT2 - definitive HSC derived) revealed that three major subsets are all derived from YS pMACs.

We thank the reviewer for the comments and have addressed all points below. If certain points were mentioned twice, we responded at the position where the point was raised the first time.

However, the relative frequencies of these specific populations are not shown, and because the single sequencing analysis goes through so many iterations of re-clustering that initiates by focusing specifically on pMAC signatures, this result is not surprising.

Probing gene expression within each of the three clusters revealed ligand expression suggesting cell-cell interactions, and cross-referencing with a fetal LT-HSC gene expression dataset revealed potential receptor-ligand interactions. Microscopic investigation of physical interactions between specific macrophage subsets and HSCs was not particularly convincing. In Figure 3C, for example, Cluster C is very difficult to visualize. It would again be helpful to know what the ratios are within the FL for each cluster. Data in Figure 3F are not well represented by Data in Figure 3E.

We showed frequencies after CODEX in the original manuscript (Fig. S3A, now Figure 4 - figure supplement 1A) since isolation of cells often induces an artifact, and relative frequencies after scRNA-seq experiments never represent the actual cell numbers present in situ. However, also the CODEX analysis has its weakness, especially in dense tissues, as the automated gating method may not catch every macrophage due to its star-shaped structure. Thus, we have now included the absolute numbers of macrophage subpopulations in Figure 7C. We have tried to improve the visualization of the clusters in Figure 3C (now Figure 4C) by zooming into a specific region. The Voronoi diagram is a powerful method that allows for an overall spatial visualization of cell distribution in large tissue pieces. In the high-resolution PDF that we provide, zooming into the PDF file should allow the reader to see each cluster in great detail.

To improve the data of macrophage-HSC interaction we have performed 3D reconstructions and quantified the distance of CD150+ and Iba1+ cells in 3D (new Figure 3C-E) as the thin cryosectioning used for CODEX is not suitable to reconstruct these interactions properly (see also lines 328-331). Thus, Figure 3E was not able and also not meant to represent data shown in Figure 3F (now Figure 4E and 4F). Figure 3E is just meant to show examples of all clusters sitting in proximity to CD150+ HSCs.

Furthermore, deletion of YS pMAC-derived macrophages the Tnfrsf11a-Cre X Spi1fl/fl resulted in broad macrophage depletion - although the authors did not demonstrate this using the carefully refined phenotypes they had defined earlier in the manuscript. Nonetheless, the authors demonstrate that macrophage depletion did affect erythroid enucleation, as expected, and the authors also showed some effect of macrophage deletion on LT-HSC gene expression by bulk transcription analysis. These effects were relatively small, however, and this was clear in the absence of effects on hematopoiesis in vivo or HSC proliferation ex vivo. To further investigate the effects of macrophage deletion on downstream hematopoieisis, the authors re-assessed the myeloid compartment following macrophage deletion, and identified and specifically focused on an observed increase in neutrophils in response to macrophage depletion. Based on this increase, they tested HSC differentiation using a colony-forming assay, which shows a slight increase in GM colonies that is also reflective of a slight but insignificant increase in total colony forming capability. The authors concluded that loss of fetal macrophages causes a reprogramming of HSCs to the granulocytic lineage. However, the colony-forming assay and subtle differences in gene expression are not sufficient to conclude that fetal HSCs have been reprogrammed towards granulocytic lineage by macrophage deletion.

We thank the reviewer for this comment and have improved the manuscript accordingly: We have performed the colony-forming assay again with n=5 embryos per genotype that were harvested on the same day, which resulted in a similar phenotype as before, with the differences of GM colonies now being significant. Further, we quantified the depletion of all macrophage subpopulations in the Tnfrsf11a-Cre X Spi1fl/fl model (Fig. 7C). To strengthen the point that the transient lack of macrophages when HSCs arrive in the fetal liver leads to their reprograming, we included flow cytometry data from E16.5 and E18.5 where we still see an increase of neutrophils in the fetal liver, despite the fact that macrophages are repopulating the empty niche (Fig. 7E, F). To show that this is a cell-intrinsic effect, we have performed adoptive transfer experiments supporting our claim that loss of macrophages reprograms HSCs toward the granulocytic lineage (Fig. 7H, I)

Overall, there are some interesting pieces of data in this manuscript, including the classification of new subsets of macrophages in the liver, their fate-mapping to the YS, and gene expression analysis. However, the data as presented do not strongly support a role for these particular macrophage subsets in regulating HSCs or fetal hematopoiesis within the fetal liver niche. Although there may be specific subsets of fetal liver macrophages that more closely physically interact with HSCs, deletion of what appeared to be a vast majority of macrophages in the FL did not appear to affect cellularity of hematopoietic stem and progenitor cells in vivo, and was not shown to convincingly affect HSC function. The mechanism by which macrophage deletion affected granulopoiesis could be independent from HSCs, and would be interesting to further explore.

We hope that with new set of experiments we were able to convince the reviewer of the importance of macrophages in the HSC niche.

Reviewer #2 (Public Review):

Using a single-cell omics approach combined with spatial proteomics and genetic fate mapping, Kayvanjoo et al found that fetal liver (FL) macrophages cluster into distinct yolk sac-derived subpopulations and that some of the HSCs in FL preferentially associate with one of the identified macrophage subpopulations. FLs lacking macrophages show a delay in erythropoiesis. The authors also try to identify a role of macrophages for HSCs function in FL, and claim that macrophages affect myeloid differentiation of HSCs. Experimental support for the function of macrophages on HSCs remains weak. Taken together, their data provide a precise map of FL macrophage subpopulations, which is novel and will serve the field well.

We thank the reviewer for the positive assessment. We have now strengthened the data regarding the impact of granulopoiesis by performing additional CFU assays and adoptive transfers.

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

In this study, the researchers aimed to investigate the cellular landscape and cell-cell interactions in cavernous tissues under diabetic conditions, specifically focusing on erectile dysfunction (ED). They employed single-cell RNA sequencing to analyze gene expression patterns in various cell types within the cavernous tissues of diabetic individuals. The researchers identified decreased expression of genes associated with collagen or extracellular matrix organization and angiogenesis in several cell types, including fibroblasts, chondrocytes, myofibroblasts, valve-related lymphatic endothelial cells, and pericytes. They also discovered a newly identified marker, LBH, that distinguishes pericytes from smooth muscle cells in mouse and human cavernous tissues. Furthermore, the study revealed that pericytes play a role in angiogenesis, adhesion, and migration by communicating with other cell types within the corpus cavernosum. However, these interactions were found to be significantly reduced under diabetic conditions. The study also investigated the role of LBH and its interactions with other proteins (CRYAB and VIM) in maintaining pericyte function and highlighted their potential involvement in regulating neurovascular regeneration. Overall, the manuscript is well-written and the study provides novel insights into the pathogenesis of ED in patients with diabetes and identifies potential therapeutic targets for further investigation.

Reviewer #2 (Public Review):

Summary: In this manuscript, the authors performed single cell RNA-sequencing of cells from the penises of healthy and diabetes mellitus model (STZ injection-based) mice, identified Lbh as a marker of penis pericytes, and report that penis-specific overexpression of Lbh is sufficient to rescue erectile function in diabetic animals. In public human single cell RNA-sea datasets, the authors report that LBH is similarly specific to pericytes and down regulated in diabetic patients. Additionally, the authors report discovery of CRYAB and VIM1 as protein interacting partners with LBH.

The authors contributions are of interest to the erectile dysfunction community and their Lbh overexpression experiments are especially interesting and well-conducted. However, claims in the manuscript regarding the specificity of Lbh as a pericyte marker, the mechanism by which Lbh overexpression rescues erectile function, cell-cell interactions impaired by diabetes, and protein-interaction partners require qualification or further evidence to justify.

Major claims and evidence:

1) Marker gene specificity and quantification: One of the authors' major contributions is the identification of Lbh as a marker of pericytes in their data. The authors present qualitative evidence for this marker gene relationship, but it is unclear from the data presented if Lbh is truly a specific marker gene for the pericyte lineage (either based on gene expression or IF presented in Fig. 2D, E). Prior results (see Tabula Muris Consortium, 2018) suggest that Lbh is widely expressed in non-pericyte cell types, so the claims presented in the manuscript may be overly broad. Even if Lbh is not a globally specific marker, the authors' subsequent intervention experiments argue that it is still an important gene worth studying.

Answer: We appreciate this comment. In our scRNAseq data for the mouse cavernosum tissues, previously known markers such as Rgs5, Pdgfrb, Cspg4, Kcnj8, Higd1b, and Cox4i2 were found to be expressed not exclusively in pericytes, while Lbh exhibited specific expression patterns in pericytes (Fig. 2 and Supplementary Fig. 5). LBH expression was easily distinguishable from α-SMA, not only in mouse cavernosum but also in dorsal artery and dorsal vein tissues within penile tissues. This distinctive expression pattern of LBH was also observed in the human cavernous pericytes (Fig. 5). Then, we examined Lbh expression patterns in various mouse tissues using the mouse single-cell atlas (Tabula Muris), although endothelial and pericyte clusters were not subclustered in most tissues from Tabula Muris. To identify pericytes, we relied on the expression pattern of known marker genes (Pecam1 for endothelial cells, Rgs5, Pdgfrb, and Cspg4 for pericytes). Lbh was expressed in pericytes of the bladder, heart and aorta, kidney, and trachea but not as specifically in penile pericytes (Supplementary Fig. 6A-D). However, it is worth noting that other known pericyte markers were also did not exhibit exclusive expression in pericytes across all the tissues we analyzed. Therefore, in certain tissues, particularly in mouse penile tissues, Lbh may be a valuable marker in conjunction with other established pericyte marker genes for distinguishing pericytes.

2) Cell-cell communication and regulon activity changes in the diabetic penis: The authors present cell-cell communication analysis and TF regulon analysis in Fig 3 and report differential activities in healthy and DM mice. These results are certainly interesting, however, no statistical analyses are performed to justify claimed changes in the disease state and no validations are performed. It is therefore challenging to interpret these results, and the relevant claims do not seem well supported.

Answer: In response to these helpful suggestions, we calculated statistical significance and performed experimental validation. CellphoneDB permutes the cluster labels of all cells 1000 times and calculates the mean(mean(molecule 1 in cluster X), mean(molecule 2 in cluster Y)) at each time for each interaction pair, for each pairwise comparison between two cell types. We only considered interactions in which the difference in means calculated by these permutations were greater than 0.25-fold between diabetes and normal. Also, we considered that the interactions with P-value < 0.05 were significant.

To assess differential regulon activities of transcription factor (SCENIC) between diabetic and normal pericytes, we utilized a generalized linear model with scaled activity scores for each cell as input. These scaled regulon activity values for angiogenesis-related TFs exhibited differences between diabetic and normal pericytes. The results of the generalized linear model revealed that Klf5, Egr1, and Junb were TFs with significantly altered regulon activities in diabetic pericytes. Experimental data indicated that the expression level of Lmo2, Junb, Elk1, and Hoxd10 was higher (Hoxd10) or lower (Lmo2, Junb, Elk1) in diabetic pericytes compared to normal pericytes (Supplementary Fig. 9). We have added the scaled regulon activity values and statistical significance in Fig. 3E.

3) Rescue of ED by Lbh overexpression: This is a striking and very interesting result that warrants attention. By simple overexpression of the pericyte marker gene Lbh, the authors report rescue of erectile function in diabetic animals. While mechanistic details are lacking, the phenomenon appears to have a large effect size and the experiments appear sophisticated and well conducted. If anything, the authors appear to underplay the magnitude of this result.

Answer: We appreciate this comment. Therefore, we have added relevant clarification in the revised manuscript discussion section to emphasize the importance of LBH overexpression on rescuing ED as follows: “To test our hypothesis, we utilized the diabetes-induced ED mouse model, commonly employed in various studies focusing on microvascular complications associated with type 1 diabetes. We observed that the overexpression of LBH in diabetic mice led to the restoration of reduced erectile function by enhancing neurovascular regeneration. However, this study primarily demonstrated the observed phenomenon without delving into the detailed mechanisms. Nonetheless, these results of LBH on erections provide us with new strategies for treating ED and should be of considerable concern.” (Please see revised ‘Discussion’)

4) Mechanistic claims for rescue of ED by Lbh overexpression: The authors claim that cell type-specific effects on MPCs are responsible for the rescue of erectile function induced by Lbh overexpression. This causal claim is unsupported by the data, which only show that Lbh overexpression influences MPC performance. In vivo, it's likely that Lbh is being over expressed by diverse cell types, any of which could be the causal driver of ED rescue. In fact, the authors report rescue of cell type abundance in endothelial cells and neuronal cells. Therefore, it cannot be concluded that MPC effects alone or in principal are responsible for ED rescue.

Answer: We agree with these claims. Therefore, we have added relevant clarifications in the discussion section of the revised manuscript. Our findings suggest that LBH can affect the function of cavernous pericytes, although we cannot definitively specify which particular cavernous cell types are affected by the overexpressed LBH, whether it be cavernous endothelial cells, smooth muscle cells, or others. Subsequent research will be required to conduct more comprehensive mechanistic investigations, such as in vitro studies using cavernous endothelial cells, smooth muscle cells, and fibroblasts to address these knowledge gaps. (Please see revised ‘Discussion’)

5) Protein interaction data: The authors claim that CRYAB and VIM1 are novel interacting partners of LBH. However, the evidence presented (2 blots in Fig. 6A,B) lack the relevant controls. It is possible that CRYAB and VIM1 are cross-reactive with the anti-LBH antibody or were not washed out completely. The abundance of bands on the Coomassie stain in Fig. 6A suggests that either event is plausible. Therefore, the evidence presented is insufficient to support the claim that CRYAB and VIM1 are protein interacting partners of LBH.

Answer: We agree with these claims. Therefore, we have added the relevant controls(Input) and performed Co-IP (IP: CRYAB or VIM, WB: LBH) to demonstrate CRYAB and VIM1 are not simply cross-reactive antigens to their LBH antibody. Our results show that we can detect the expression of CRYAB and VIM after LBH IP, and we also detect the expression of LBH after CRYAB and VIM IP. In addition, it can be seen from our results that the binding of LBH to VIM is higher than that of CRYAB. Regardless, these results indicate that the binding of CRYAB or VIM to LBH is not a random phenomenon. (Please see revised ‘Result’ and ‘Figure 6B’)

Impact: These data will trigger interest in Lbh as a target gene within the erectile dysfunction community.

Reviewer #3 (Public Review):

Bae et al. described the key roles of pericytes in cavernous tissues in diabetic erectile dysfunction using both mouse and human single-cell transcriptomic analysis. Erectile dysfunction (ED) is caused by dysfunction of the cavernous tissue and affects a significant proportion of men aged 40-70. The most common treatment for ED is phosphodiesterase 5 inhibitors; however, these are less effective in patients with diabetic ED. Therefore, there is an unmet need for a better understanding of the cavernous microenvironment, cell-cell communications in patients with diabetic ED, and the development of new therapeutic treatments to improve the quality of life.

Pericytes are mesenchymal-derived mural cells that directly interact with capillary endothelial cells (ECs). They play a vital role in the pathogenesis of erectile function as their interactions with ECs are essential for penile erection. Loss of pericytes has been associated with diabetic retinopathy, cancer, and Alzheimer's disease and has been investigated in relation to the permeability of cavernous blood vessels and neurovascular regeneration in the authors' previous studies. This manuscript explores the mechanisms underlying the effect of diabetes on pericyte dysfunction in ED. Additionally, the cellular landscape of cavernous tissues and cell type-specific transcriptional changes were carefully examined using both mouse and human single-cell RNA sequencing in diabetic ED. The novelty of this work lies in the identification of a newly identified pericyte (PC)-specific marker, LBH, in mouse and human cavernous tissues, which distinguishes pericytes from smooth muscle cells. LBH not only serves as a cavernous pericyte marker, but its expression level is also reduced in diabetic conditions. The LBH-interacting proteins (Cryab and Vim) were further identified in mouse cavernous pericytes, indicating that these signaling interactions are critical for maintaining normal pericyte function. Overall, this study demonstrates the novel marker of pericytes and highlights the critical role of pericytes in diabetic ED.

Reviewer #1 (Recommendations For The Authors):

1) The methods are poorly written. It lacks specific information on the sample size, experimental design, and data analysis methods employed. The absence of these crucial details makes it difficult to evaluate the robustness and reliability of the findings.

Answer: We agree with the reviewer’s suggestion, now we revised the methods of our manuscript, and added detailed information or references. For sample size we have added detailed information in Figure legend (Please see revised ‘Method’ , Figure Legend, and Supplementary information.)

2) The cell number in the scRNA-seq analysis is small (~12000) and some minor cell types are probably underrepresented. It is not clear whether the authors pooled the cells from different mice as one sample, or replicates in different groups have been included. It will be helpful to label different samples in the UMAP. The authors should repeat the experiments with more replicates to increase the cell number and validate the findings.

Answer: We understand the reviewer's concern, but due to the small size of mouse penile tissue, we had to pool 5 corpus cavernosum tissues for each group (using pooled samples) for scRNA-seq analysis. Moreover, owing to the unique nature of mouse penile tissue, which is highly resistant, it posed challenges for the dissolution and isolation of single cells using conventional single-cell separation methods. Consequently, we had to increase the concentration of the enzyme to finally obtain 12,894 cells. Rather than conducting a repetitive scRNAseq analysis on the same mouse model, we validated our findings in human cavernous single-cell transcriptome data. This analysis allowed us to confirm the presence of pericyte in human corpus cavernosum, specific expression of LBH in human cavernous pericytes, and the identification of relevant GO terms associated with pericyte functions (Figure 5). We have add these information in ‘Method’ (Please see revised ‘Method’).

3) Functional studies are lacking to justify how manipulating LBH expression or its interacting proteins might lead to effective therapeutic approaches for diabetic ED.

Answer: We have performed the functional study to evaluate LBH expression might lead to effective therapeutic approaches for diabetic ED as showed in Figure 4G. Assessment of intracavernous pressure (ICP) is the most representative test for evaluating erectile function. Therefore, we modulated LBH expression in the penis of diabetic mice and assessed the erectile function of the mice by intracavernous pressure. However, we have not performed ICP studies and relative in vitro studies (migration, survival experiment) to assess whether LBH-interacting proteins have the same effect.

4) Although the abstract identifies novel targets for potential interventions, such as LBH and its interacting proteins, the clinical relevance of these findings remains uncertain. The authors should include a discussion regarding the translation of these discoveries into therapeutic strategies or their potential impact on patients with diabetes and ED.

Answer: We appreciate the reviewer's suggestion and have added a discussion as per the reviewer’s recommendation (Please see revised ‘Discussion’).

5) While the study highlights the importance of pericytes in penile erection, it fails to mention the broader context of other cell types involved in the pathogenesis of ED. Neglecting to discuss potential contributions from endothelial cells, smooth muscle cells, or neural elements limits the comprehensive understanding of the cellular interactions underlying diabetic ED.

Answer: We agree with the reviewer's suggestion and have added a discussion regarding the significance of other cell populations in penile tissues, such as endothelial cells, smooth muscle cells fibroblasts, and neural elements, along with the rationale for our focus on pericytes. (Please see revised ‘Discussion’).

Reviewer #2 (Recommendations For The Authors):

We congratulate the authors on an interesting study. We were especially excited to see their Lbh overexpression results. However, we felt other claims in the paper could benefit from additional investigation, analysis, and statistical rigor. We have provided a set of suggestions for improvement below.

Major points:

1) Pericyte marker gene proposal: See public review for commentary on the following suggested experiments. The authors should perform binary classification analysis using Lbh and report the performance of this gene as a marker (e.g. using the area under the receiver operating characteristic, accuracy, precision and recall). Further, they should consider performing this analysis for all other genes in their data to determine whether Lbh is the best marker gene.

Answer: We appreciate this comment. AUC scores of Rgs5, Pln, Ednra, Npylr, Atp1b2, and Gpc3 for ability of a binary classifier to distinguish between pericyte and the other cell types in mouse penile tissues were measured by using FindMarkers function. Rgs5 had the highest AUC, but Rgs5 was also expressed in SMCs in our data. Pln, Ednra, Gpc3, and Npy1r also seemed to be candidate markers, but the literature search excluded these genes as they are also expressed in the SMCs of other tissues or different cell types. The AUC score of Lbh was over 0.7, and expression in SMC was not identified in previous studies, and ultimately, we experimentally identified that Lbh is penis pericyte specific. We have added this to the manuscript.

Author response table 1.

Robust differential expression analysis should also be performed for this gene (if not all) and the statistics should be reported, given known issues with the statistical approach used by the authors for differential expression (see: Squair 2021, 10.1038/s41467-021-25960-2). The authors' should also report the number of cells involved in these comparisons, as the number of pericytes in the data (Fig 1B) appears quite small.

Answer: We appreciate this comment. We used “MAST” to identify differentially expressed genes. This test is often used to find DEGs in single-cell RNA data. However, because the pseudobulk method has advantages over the single cell DEG method (Squair 2021, 10.1038/s41467-021-25960-2), we additionally performed DEG analysis with DESeq2 to confirm whether Lbh can distinguish pericytes from other cell types in the penile. As a result, even when tested with DESeq2, Lbh expression was significantly higher in pericytes than in other cell types in penile (adjusted p-value = 2.694475e-07 in Pericyte vs SMC, adjusted P-value = 3.700118e-58 in Pericyte vs the other cell types). Mouse penile tissue is small in size, and the number of pericytes in mouse penile tissue is relatively smaller compared to fibroblasts and chondrocytes. In our mouse penile scRNAseq data, the number of pericytes is as follows: normal: 58, diabetes: 116. Despite the limited number of cells, we were able to establish statistical significance in our analyses.

Immunostaining results in Fig. 2D, E should likewise be quantified. At present, it's unclear that LBH and aSMA are mutually exclusive as claimed. The authors should also investigate Lbh expression in public single cell genomics data, rather than performing candidate gene literature searches. For example, the Tabula Muris suggests Lbh is expressed widely outside pericytes.

Answer: For Figure 2D and E, the aim of these analyses was to assess the distribution of LBH and other cellular markers to see if they overlap and if they can be distinguished. We think that some of the overlapping staining in the tissue may be caused by multilayered cellular structures, so staining within cells would be more convincing. Therefore, we quantified the percentage of LBH- or α-SMA-expressed pericytes and relative expression in smooth muscle cells in cell staining (Supplementary Fig. 5E). We found that only 3% of smooth muscle cells expressed LBH, 67% of mouse cavernous pericytes (MCPs) expressed α-SMA, and more than 97% of MCPs expressed LBH. Therefore, these results may illustrate the specific expression of LBH in MCPs. These information was added as ‘Supplementary Fig. 5E’ (Please see revised ‘Supplementary information’). We also examined Lbh expression patterns in various mouse tissues using the public mouse single-cell atlas (Tabula Muris), and provided a detailed response in reviewer 2’s public review 1.

Even if Lbh is not the best marker, the authors' intervention experiment still motivates study of the gene, but these analyses would help contextualize the result for readers.

2) Statistical anslyses for cell-cell communication and TF regulon analysis: See public review for context on these comments. The authors should perform statistical tests to evaluate the significance of differences detected for each of these analysis. For example, generalized linear models can be used to assess the significance of TF regulon activity scores from SCENIC, and permutation tests can be used to measure the significance of cell-cell interaction score changes. Without these statistical tests, it's challenging for a reader to interpret whether the results reported are meaningful or within the realm of experimental noise.

Answer: We appreciate this comment. We calculated statistical significance TF regulon analyses as suggested by the reviewer and described a detailed statistical calculation method for cell-cell communication. We provided a detailed response in reviewer 2’s public review 2.

3) Mechanism of ED rescue by Lbh overexpression: To support this claim, the authors would need to perform an experiment where Lbh is over expressed specifically in MPCs (using e.g. a specific promoter on their LTV construct, or a transgenic line with a cell type-specific Cre-Lox system). Absent these data, the claim should be removed.

Answer: We agree with the reviewer's suggestion and we have reworked the claim that ‘LBH overexpression is affected by pericytes during ED recovery’ and have added relevant clarification in the Discussion section to clearly state that LBH overexpression may affect many cavernosum cells, such as cavernous endothelial cells, smooth muscle cells, fibroblasts, and pericytes (Please see revised ‘Result’ and ‘Discussion’)

4) Protein interaction claims: This experiment would require that the authors perform a similar pull-down with LBH KO cells and or a reciprocal Co-IP (e.g. IP: CRYAB or VIM1, WB: LBH) to demonstrate CRYAB and VIM1 are not simply cross-reactive antigens to their LBH antibody. Further, these experiments appear to only have a single replicate for each condition. The authors should either remove associated claims, or perform a Co-IP experiment with the relevant controls with sufficient replication.

Answer: We agree with the claims. Therefore, we have included the necessary controls (Input) and performed Co-IP (IP: CRYAB or VIM1, WB: LBH) to demonstrate that CRYAB and VIM1 are not simply cross-reactive antigens to their LBH antibody. Our results show that we can detect the expression of CRYAB and VIM after LBH IP, and we also detect the expression of LBH after CRYAB and VIM IP. In addition, it can be seen from our results that the binding of LBH to VIM is higher than that of CRYAB. Regardless, these results indicate that the binding of CRYAB or VIM to LBH is not a random phenomenon. Additionally, all IP experiments were replicated at least three times. (Please see revised ‘Result’ and ‘Figure 6B’)

Minor Points:

• The reference "especially in men" on line 56 seems odd given that only males can experience penile erectile dysfunction.

Answer: We agree with the reviewer's suggestion and have removed the description 'especially male' (Please see revised ‘Introduction’)

• Line 109, it's unclear what genes showed altered expression in Schwann cells.

Answer: We apologize for the confusion. There was no significant differentially expressed genes between normal and diabetes in Schwann cells. We revised this part in the manuscript. (Schwann cells showed an increased expression compared to normal cells in diabetes, though not significant. In Schwann cells, there were no significant DEGs between diabetic and normal cells.)

• It would be helpful for readers to see an analysis of the cell types that are transduced in the Lbh overexpression experiment in vivo. At present, some pericyte specificity is implied, but not demonstrated.

Answer: We appreciate this comment. Our findings suggest that LBH can affect the function of cavernous pericytes, although we cannot definitively conclude which specific-cavernous cell types are affected by the overexpressed LBH, whether it be cavernous endothelial cells, smooth muscle cells, or others. Subsequent research will be required to conduct more comprehensive mechanistic investigations, such as in vitro studies using cavernous endothelial cells, smooth muscle cells, and fibroblasts to address these knowledge gaps. These were also mentioned in the manuscript.

• To improve clarity and enhance readability, define abbreviations before their initial usage in the text. For instance, in the second paragraph of the Introduction, the abbreviation 'ECs' is used without prior definition. It can be inferred that it is referring to endothelial cells, mentioned in parentheses in the subsequent sentence.

Answer: We agree with the reviewer's suggestion to expand acronyms and ensure that all acronyms are defined in the revised manuscript before they are used for the first time in the text (Please see revised Manuscript).

• It is important to include relevant references that align with the content being discussed. For example, in the Introduction, pericytes are described as being involved in various processes such as angiogenesis, vasoconstriction, and permeability. The text refers to a single reverence, a review by Gerhardt and Besholtz, which primarily focuses on pericyte's role in regulating angiogenesis. Adding additional sources, such as the review by Bergers and Song (Neuro Oncol., 2005) is recommended.

Answer: We agree with the reviewer's suggestion, and have added the reference as reviewer recommended (Please see revised Manuscript and reference).

• Figure 3E: it is stated that a panel of 53 angiogenesis factors were tested, it is stated that only MMP3 showed increased expression. However, various unlabeled spots appear to show changed expression patterns. It would be helpful to show a summary graph with the relative intensities of the full array of factors tested.

Answer: We agree with the reviewer’s suggestion, now we showed all spots density in angiogenesis array as Supplementary Table 1. The condition of the spots we selected was that the expression density was at least above 1500, and the change ratio was greater than 1.2. (Please see revised ‘Supplementary information’)

Reviewer #3 (Recommendations For The Authors):

Detailed statistical power calculation

Data availability statement( were both mouse and human scRNA deposited in GEO with a taken and when will they be released to the public?)

Answer: Human scRNA data have been deposited in GEO under accession number GSE206528. Our mouse scRNA dataset has been uploaded to KoNA and is available for download (https://www.kobic.re.kr/kona/review?encrypt_url=amlod2FucGFya3xLQUQyMzAxMDEz)

Major concerns about this work

1) The single cell RNAseq data collected for mouse diabetic ED(Fig 1B), FB are the most abundant cell population compared to PC, EC, SMC and other clusters. The rationale for studying FB clusters (in Figure 1, D-F) instead of PC cluster is unclear. Which cluster DEG did the authors annotate for Fig 1G-H?

Answer: We understand the reviewer's suggestion and confusion. Although other major cell populations in penile tissue such as smooth muscle cells, endothelial cell, and fibroblasts have been extensively studied, pericytes have mainly been investigated in the context of the central nervous system (CNS). For example, in the CNS, pericytes are involved in maintaining the integrity of the brain's blood-brain barrier (BBB) [PMID: 27916653], regulating blood flow at capillary junctions [PMID: 33051294], and promoting neuroinflammatory processes [PMID: 31316352], whose dysfunction is considered an important factor in the progression of vascular diseases such as Alzheimer's disease [PMID: 24946075]. But little is known about the role of pericytes in penile tissue [PMID: 35865945; PMID: 36009395; PMID: 26044953]. In order to explore the role of pericytes in repairing the corpus cavernosum vascular and neural tissues damaged by DM, we focused on pericytes, which are multipotent perivascular cells that contribute to the generation and repair of various tissues in response to injury. Although recent studies have shown that pericytes are involved in physiological mechanisms of erection, little is known about their detailed mechanisms. We have also added this rationale in discussion.

Single cell level study has not been conducted in mouse penile tissues. Therefore, before delving into pericytes, we aimed to identify overall transcriptome differences between normal and diabetic conditions in mouse penile tissues. We presented the analyses of FB, which make up the largest proportion among the cell types in the mouse penis, in Fig. 1D-F. The analysis of other cell types is provided in Supplementary Fig. 1-4. Fig. 1G-H are GO terms for Fibroblasts clusters. We added this information in the figure.

2) Fig 2 is the critical data to show Lbh is a cavernous PC specific marker. More PC violin plots to identify PC cluster such as Cspg4, Kcnj8, Higd1b, Cox4i2 and more SMC violin plots to identify SMC cluster such as Acta2, Myh11, Tagln, Actg2 should be used for inclusion and exclusion of PC( the same concern applied to human scRNAseq in Fig 5B).

Answer: We appreciate this comment. We examined the expression of other marker genes of pericytes and SMCs. Although some marker genes were rarely expressed in the mouse penis data (Kcnj8, Higd1b), the expression of marker genes tended to be relatively high in each cluster. The expression of Cspg4 and Cox4i2 was higher in pericytes than in SMCs, while the expression of Acta2, Myh11,and Tagln was higher in SMCs than in pericytes. Actag2 was specifically expressed in SMCs. Through the gene set enrichment test as well as the expression of known cell type marker genes, we identified that the annotation of pericyte and SMC was appropriate (Fig. 2B and Fig. 5C). We added the violin plots of these marker genes in Supplementary Fig. 5.

Author response image 1.

(Mouse)

In human penis data, ACTA2 and MYH11 were expressed in SMCs, pericytes, and myofibroblasts, as in the previous paper [PMID: 35879305]. Among pericyte markers, the number of cells expressing KCNJ8 and HIGD1B was small. The cluster we annotated as pericyte was double positive for pericyte markers CSPG4 and COX4I2. ACTG2, a marker for SMC, was expressed more highly in SMC than in pericytes and myofibroblasts. As in the mouse penis data, we identified that the annotation of each cell type was appropriate through the gene set enrichment test in the human penis data. We added the violin plots of CSPG4, COX4I2, and ACTG2 in Supplementary Fig. 11.

Author response image 2.

(Human)

When exploring Lbh expression levels in "Database of gene expression in adult mouse brain and lung vascular and perivascular cells" from https://betsholtzlab.org/VascularSingleCells/database.html, Lbh is not uniquely expressed in PC, suggesting its tissue-specific expression level. This difference should be discussed in the Discussion section.

Answer: We appreciate this valuable comment. For the answer to this comment, we extensively analyzed Lbh expression patterns in various mouse tissues using the public mouse single-cell atlas (Tabula Muris) as also suggested by Reviewer 2. Please see our detailed response in reviewer 2’s public review 1.

3) In prior studies on PC morphology and location (PMID: 21839917), they reside in capillaries (diameter less than 10um) or distal vessels (diameter less than 25um) and have oval cell body and long processes. Due to the non-specificity of Pdgfrb, SMC are positive for Pdgfrb staining (this has been shown in many publications that SMC are Pdgfrb+; unfortunately, NG2 antibody also stains for both PC and SMC). Therefore, the LBH immunostaining (in Fig 2D and 2E of large-sized vessels) are very likely for SMC identity, not PC. PC should be in close contact with CD31+ ECs in healthy conditions. The LBH immunostaining of PC in both mouse and human tissues (Fig 4) must be replaced and better characterized.

Answer: We agree with the reviewer's suggestion. As it is widely known, peicytes are primarily located in capillaries, where they surround endothelial cells of blood vessels. However, recent discoveries have identified cells with pericyte-like characteristics in the walls of large blood vessels, challenging the traditional concept [PMID: 27268036]. In our study, we observed minimal overlap in staining between LBH and α-SMA, suggesting that the cells expressing LBH were not smooth muscle cells but possibly pericyte-like cells in large vessels. In small vessels within the bladder, kidney, and even the aorta, we found LBH-expressing cells surrounding CD31-expressing vessels, consistent with the known characteristics of pericytes. Further research is needed to comprehend the differences in LBH expression and its characteristics in both large and small blood vessels. We have added discussions and references for this issue (Please see revised ‘Discussion’ and ‘Reference’)

4) How do mouse cavernous pericytes isolate? How is purity?

Answer: As the reviewer points out, we isolated mouse spongiform pericytes following our and other previously published methods. We used pigment epithelium-derived factor (PEDF), which removes non-pericytic cells [PMID: 30929324, 23493068]. Although there are no purity study results such as FACS, other staining results thoroughly support the notion that this method yields pericytes with a notably high level of purity. (Please see ‘Method’ section).

5) Can mouse scRNAseq cell-cell communication in Fig 3 be reproducible in human scRNAseq cell-cell communication? The results in human ED are more clinically significant than in mouse data.

Answer: In human scRNAseq data, the difference between angiogenesis-related interactions between normal and diabetes was not as significant as that in mouse data. Because the cell type composition of the human and mouse penis is not completely identical, there are limitations in comparing cell-cell interactions. However, in the human penis data, some interactions related to angiogenesis between pericytes and other cell types were decreased in diabetes compared to normal (boxed parts).

Author response image 3.

6) Fibroblasts also express Vim. Murine PC VIM/CRYAB( should be written as Vim/Cryab as mouse proteins) direct interaction with Lbh is unclear from Lbh IP as Fig 6A red boxes showed a wide range of sizes. Where is the band for Lbh? Do human PC LBH interact with VIM/CRYAB?

Answer: We agree with the reviewer's comment. VIM is a type III intermediate filament protein expressed in many cell types. We have added the relevant controls (Input) and performed Co-IP (IP: CRYAB or VIM, WB: LBH) to demonstrate CRYAB and VIM are not simply cross-reactive antigens to their LBH antibody. In western blot study, the LBH band was expressed between 35 kDa-48 kDa. From Figure 6A, we detected CRYAB in band 1 and VIM in bands 2 and 3. This may be due to the formation of dimers or multimers by VIM. We did not use human PCs for IP studies because IP requires large amounts of protein, making IP studies using human pericyte challenging. Nevertheless, the interaction between LBH and CRYAB in humans has been reported through fluorescent resonance energy transfer assay and affinity chromatography technology assay [PMID:34000384, PMID:20587334].

7) In Fig 6H and I, why does CRYAB expression significantly reduce in vitro and in vivo under diabetic conditions, whereas VIM expression significantly increases?

Answer: As the reviewer pointed out, and we have discussed on this issue in the manuscript, CRYAB is known to promote angiogenesis. Diabetes reduces CRYAB expression, so angiogenesis may be impaired. Furthermore, since VIM is a multifunctional protein, it interacts with several other proteins with multiple functions under various pathophysiological conditions. There are many relevant literatures showing that VIM expression is increased under diabetic conditions [PMID: 28348116 and PMID: 32557212]. And VIM deficiency protects against obesity and insulin resistance in patients with type 2 diabetes. Therefore, we hypothesize that exogenous LBH may have the ability to bind to the increased VIM in diabetic conditions and inactivate the effects of VIM. Thereby achieving the protective effect. This needs to be proved in further studies.

8) The therapeutic strategies targeting (Lbh-Cryab-Vim) on mouse diabetic ED model is not investigated and need to be further validated and discussed.

Answer: As the reviewers pointed out, in this study, we did not evaluate the targeted therapeutic strategy for LBH-CRYAB-VIM in a mouse diabetic ED model. We only identified the binding potential of these three proteins. Evaluation of this treatment strategy requires further study. For example, we can employ shRNA lentivirus, either alone or in combination, to downregulate CRYABexpression [PMID: 31612679] in normal mice, utilize a lentiviral vector CMV-GFP-puro-vimentin to overexpress Vimentin [PMID: 36912679], and then treat it with LBH to evaluate whether the LBH effect still exists (in vivo erectile function study and in vitro angiogenesis assay). We include this information in the Discussion section as a limitation of this study (Please see revised ‘Discussion’).

9) The Discussion of current knowledge of pericytes in diabetic ED and other diseases and the significance of this study as well as clinical implications, should be expanded.

Answer: As the reviewers pointed out, we have expanded the current knowledge of pericytes in diabetic ED and other diseases (CNS disease) and clinical implications as follows: “Although other major cell populations in penile tissue such as smooth muscle cells, endothelial cell, and fibroblasts have been extensively studied, pericytes have mainly been investigated in the context of the central nervous system (CNS). For example, in the CNS, pericytes are involved in maintaining the integrity of the brain's blood-brain barrier (BBB), regulating blood flow at capillary junctions, and promoting neuroinflammatory processes, whose dysfunction is considered an important factor in the progression of vascular diseases such as Alzheimer's disease. But little is known about the role of pericytes in penile tissue.” (Please see revised ‘Discussion’).

10) How many clinical samples were used? How many times did each experiment repeat?

Answer: As the reviewers pointed out, the clinical samples’ information was added in ‘method’ section. A total four human samples were used in this study (‘human corpus cavernosum tissues were obtained from two patients with congenital penile curvature (59-year-old and 47-year-old) who had normal erectile function during reconstructive penile surgery and two patients with diabetic ED (69-year-old and 56-year-old) during penile prosthesis implantation.’). For in vivo study, we quantified four different fields from human samples.

Minor concerns

1) Fig 1A, why normal mouse's body size is the same as DM?

Answer: As the reviewer pointed out, in Figure 1A, while the size of normal mice and DM mice may not appear significantly different, there are indeed notable difference in body weight and size. The normal mice body weigh we used was about 30 grams, while DM mice body weigh was generally less than 24 grams. We found that we missed information on physiological and metabolic parameters from in vivo studies (ICP function study). Therefore, we have added it in Supplementary Table 2 (Please see revised ‘Supplementary information’)

2) The label and negative, and positive controls for Fig 6B are missing.

Answer: We thank for pointing out this. We have added the relevant controls (Input) and performed Co-IP (IP: CRYAB or VIM1, WB: LBH) to demonstrate CRYAB and VIM1 are not simply cross-reactive antigens to their LBH antibody and all IP was replicated for at least 3 times. (Please see revised ‘Result’ and ‘Figure 6B’)

3) The limitation of this study and future work should be discussed.

Answer: As the reviewer pointed out, we have added the limitation of this study and future direction in the discussion section (Please see revised ‘Discussion’).

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.

Public Reviews:

We thank the reviewers for their insightful comments on our manuscript. We have addressed the reviewers’ comments below and in the revised manuscript.

Reviewer #1:

Comment #1: The authors found differences in the initial spike doublet of action potentials between cortical neurons in experimental and control conditions (Figure 2e). The action potential firing frequency of the first two APs (instant firing frequency) of recorded neurons shall be quantified to investigate whether there are statistical differences between the action potential firing frequency in cortical neurons in different experimental groups versus control conditions.

Response: As suggested by the reviewer, we have quantified the first interspike interval (ISI; time between the 1st and 2nd action potential). The data is included in Fig. 2h as well as in Fig. S3e and Table 1. The Results and Methods have also been updated accordingly.

Comment #2: The mTORS12215Y induced the largest changes in Ih current amplitudes in cortical neurons compared with other experimental conditions. Whether the HCN4 channel expression is regulated by mTOR pathway activation, or could there be possible interactions between the HCN channel and mTORS12215Y mutant protein?

Response: Our previous findings using the RhebS16H mutation support the idea that increased expression of HCN4 channels is regulated by mTOR pathway activation. This is evidenced by its sensitivity to rapamycin (a mTOR inhibitor) and expression of constitutively active 4E-BP1 (a translational repressor downstream of mTORC1). Since mTORS2215Y directly hyperactivates mTORC1 and there are no known interactions between HCN channels and mTORS2215Y, our data strongly suggests that abnormal HCN4 channel expression occurs via mTORC1 hyperactivation in this condition. We have revised our Discussion to make this point clearer.

Comment #3: A comparison of the electrophysiological characteristics of cortical neurons in different experimental conditions in the present study and pathological neurons in human FCD reported in previous literature could be interesting. Inducing pathological gene mutations or knocking out key genes in mTOR pathway in the rodent cortex - which approach could better model human FCD?

Response: We agree with the reviewer and have added a new paragraph in the Discussion to compare our electrophysiology results to those of previous studies done on human FCDII and TSC cytomegalic neurons. With regards to the reviewer’s question about which of the two approaches in the rodent cortex – inducing pathological gene mutations or knocking out key genes in the mTOR pathway – would better model human FCD, our study emphasizes the importance of considering gene-specific mechanisms in FCDII. Thus, modeling the genetically distinct FCDIIs will require using gene-specific manipulations. We have revised our Discussion to include this point. With that said, for some phenotypes that are generalized across FCDII independent of the mTOR pathway genes, using pathogenic mutations of mTOR activators or knockout of negative mTOR regulators would likely both be appropriate models. Of note, as discussed in the manuscript, there are also technical factors to be considered when choosing to use a pathogenic gene mutation versus knocking out a gene (the latter which would depend on the half-life of the proteins).

Reviewer #2:

Comment #1: The authors postulate that all the findings are dependent on mTORC1-related effects but don't assess whether some of the differences could be due to effects on mTORC2 signaling. mTORC2 is an important and poorly understood alternative isoform of mTOR (due to rictor binding) that has effects on distinct cell signaling pathways and in particular actin polymerization. This doesn't diminish the effects of the current analysis of mTORC1 but could explain genotypic differences in each variable. A few prior studies have assessed the role of mTORC2 in epileptogenesis and cortical malformations (Chen et al., 2019).

Response: We agree with the reviewer and have revised our Discussion to include the possibility of mTORC2 contribution to the gene-specific phenotypic differences.

Comment #2: The slice recordings were performed in the usual recording aCSF buffer conditions but there is no assessment of the role of amino acids or nutrients in the bath. While it is clear that valuable and viable acute slice recordings can be made in aCSF, the role of the mTOR pathway is to modulate cell growth in response to nutrient conditions. Thus, one variable that could be manipulated and assessed currently in this study is the levels of amino acids i.e., leucine and arginine added to the bath since DEPDC5 and TSC1 are responsive to ambient amino acid levels.

Response: We thank the reviewer for this great suggestion, and we intend to pursue this as part of another study.

Comment #3: The analysis concedes that the role of somatic mutations in cortical malformations may depend not only on genotypic effects but also on allelic load and cellular subtype affected by the mutation. Thus, it would be interesting to see if electroporation either at E14 or E16, thereby affecting a distinct pool of progenitors, would mitigate or accentuate differences between mTOR pathway genes.

Response: We agree with the reviewer. This is a crucial experiment that we hope to perform in the future. We have also added a paragraph in our Discussion to address this important point.

Comment #4: Treatment with rapamycin and zatebradine in each condition would have added to the strength of the findings to determine the mTOR-dependence and reversibility of HCN4 effects.

Response: We previously demonstrated the mTORC1 dependence of HCN4 expression in the RhebS16H condition using rapamycin and expression of constitutively active 4E-BP1. 4E-BP1 is a translational repressor downstream of mTORC1. In the 4E-BP1 study, we used a conditional system to express 4EBP1F113A (mutation that resists inactivation by mTORC1) in adolescent mice while RhebS16H (and thus mTORC1 activation) was expressed embryonically. 4E-BP1F113A expression suppressed Ih current and HCN4 expression, suggesting that aberrant HCN4 expression can be reversed by decreasing mTORC1regulated translation. Based on these data and the findings that rapamycin suppressed abnormal HCN4 expression, we postulate that increased HCN4 expression in the different gene conditions examined in the present study occurs via the mTORC1 pathway. However, we agree with the reviewer that treating each of the conditions with rapamycin would provide direct evidence of their mTORC1 dependence. Additionally, treating each condition with the HCN channel blocker zatebradine would also add strength to the findings. We have added a comment in the Discussion to acknowledge this point.

Reviewer #1 (Recommendations For The Authors):

Comment #1: The authors found increased frequency or amplitudes of spontaneous postsynaptic currents in different experimental cohorts. These data may not be sufficient to conclude increased synaptic excitability, because there are no pharmacological experiments to verify whether the recorded inward currents are excitatory or inhibitory postsynaptic currents. An alternative approach could be analyzing the decay time of spontaneous postsynaptic currents, the excitatory postsynaptic currents had relatively faster decay time compared with inhibitory postsynaptic currents.

Response: Thank you for the comment. We apologize for the lack of clarity and have added the following text in the Results to clarify: “To separate sEPSCs from spontaneous inhibitory postsynaptic currents (sIPSCs), we used an intracellular solution rich in K-gluconate to impose a low intracellular Cl- concentration and recorded at a holding potential of -70 mV, which is near the Cl- reversal potential. The 90%-10% decay time of the measured synaptic currents ranged between 4-8 ms in all conditions (mean ± SD: control: 4.9 ± 1.6; RhebY35L: 5.2 ± 1.4; mTORS2215Y: 7.4 ± 1.4; control: 6.8 ± 0.7; Depdc5KO: 7.4 ± 1.0; PtenKO: 8.1 ± 0.9; Tsc1KO: 7.4 ± 0.9), consistent with the expected decay time for sEPSCs and shorter than the decay time for sIPSCs (Kroon et al, 2019). The recorded synaptic currents were therefore considered to be sEPSCs.”

Comment #2: There are typos of Depdc5 in the text and figure legends.

Response: Thank you for noticing this error. We have corrected the typos in the manuscript.

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

The manuscript by Zhu and colleagues aimed to clarify the importance of isoform diversity of PCDHg in establishing cortical synapse specificity. The authors optimized 5' single-cell sequencing to detect cPCDHg isoforms and showed that the pyramidal cells express distinct combinations of PCDHg isoforms. Then, the authors conducted patch-clamp recordings from cortical neurons whose PCDHg diversity was disrupted. In the elegant experiment in Figure 3, the authors demonstrated that the neurons expressing the same sets of cPCDHg isoforms are less likely to form synapses with each other, suggesting that identical cPCDHg isoforms may have a repulsive effect on synapse formation. Importantly, this phenomenon was dependent on the similarity of the isoforms present in neurons but not on the amount of proteins expressed.

One of the major concerns in an earlier version was whether PCDHg isoforms, which are expressed at a much lower level than C-type isoforms, have true physiological significance. The authors conducted additional experiments to address this point by using PCDHg cKO and provided convincing data supporting their conclusion. The results from PCDHg C4 overexpression, showing no impact on synaptic connectivity, further clarified the importance of isoforms. I have no further concerns, however, I would like to point out that the evidence for the necessity of the PCDHg isoform is still lacking because most experiments were done by overexpression. It would be helpful for the readers if the authors could add this point to the discussion.

Thank you for the positive feedback on our work. We have now incorporated a discussion of the limitations associated with overexpression.

Reviewer #2 (Public Review):

This short manuscript by Zhu et al. describes an investigation into the role of gamma protocadherins in synaptic connectivity in the mouse cerebral cortex. First, the authors conduct a single-cell RNA-seq survey of postnatal day 11 mouse cortical neurons, using an adapted 10X Genomics method to capture the 5' sequences that are necessary to identify individual gamma protocadherin isoforms (all 22 transcripts share the same three 3' "constant" exons, so standard 3'biased methods can't distinguish them). This method adaptation is an advance for examining individual gamma transcripts, and it is helpful to publish the method, the characterization of which is improved in this revised manuscript. The results largely confirm what was known from other approaches, which is that a few of the 19 A and B subtype gamma protocadherins are expressed in an apparently stochastic and combinatorial fashion in each cortical neuron, while the 3 C subtype genes are expressed ubiquitously. Second, using elegant paired electrophysiological recordings, the authors show that in gamma protocadherin cortical slices, the likelihood of two neurons on layers 2/3 being synaptically connected is increased. That suggests that gamma protocadherins generally inhibit synaptic connectivity in the cortex; again, this has been reported previously using morphological assays, but it is important to see it confirmed here with physiology. Finally, the authors use an impressive sequential in utero electroporation method to provide evidence that the degree of isoform matching between two neurons negatively regulates their reciprocal synaptic connectivity. These are difficult experiments to do, and while some caveats remain, the main result is consistent. Strengths include the impressive methodology and improved demonstration of the previously-reported finding that gamma protocadherins work via homophilic matching to put a brake on synapse formation in the cortex. Weaknesses include the writing, which even in the revision fails to completely put the new results in context with prior work, which together has largely shown similar results; a still-incomplete characterization of a new alpha protocadherin KO mouse (a minor point but it should still be addressed); and a lack of demonstration of protein levels in electroporated brains. Because of the unique organization and expression pattern of the gamma protocadherins, it is unlikely that these results will be directly applicable to the broader understanding of the role of cell adhesion molecules in synapse development. However, the methodology, which is now better described, should be applicable more broadly and the improved demonstration of the role of gamma protocadherin's negative role in cortical synaptogenesis is helpful.

Thank you for the positive comments on our work. We have taken your suggestion into account and expanded our discussion to contextualize our research within the broader field of PCDH. Additionally, we have included more data to further illustrate the decrease in αPCDH expression in Pcdha conditional knockout mice. Your feedback has been invaluable in enhancing our manuscript.

Reviewer #3 (Public Review):

In this study, Zhu and authors investigate the expression and function of the clustered Protocadherins (cPcdhs) in synaptic connectivity in the mouse cortex. The cPcdhs encode a large family of cadherin-related transmembrane molecules hypothesized to regulate synaptic specificity through combinatorial expression and homophilic binding between neurons expressing matching cPcdh isoforms. But the evidence for combinatorial expression has been limited to a few cell types, and causal functions between cPcdh diversity and wiring specificity have been difficult to test experimentally. This study addresses two important but technically challenging questions in the mouse cortex: 1) Do single neurons in the cortex express different cPcdh isoform combinations? and 2) Does Pcdh isoform diversity or particular combinations among pyramidal neurons influence their connectivity patterns? Focusing on the Pcdh-gamma subcluster of 22 isoforms, the group performed 5'end-directed single-cell RNA sequencing from dissociated postnatal (P11) cortex. To address the functional role of Pcdhg diversity in cortical connectivity, they asked whether the Pcdhgs and isoform matching influence the likelihood of synaptic pairing between 2 nearby pyramidal neurons. They performed simultaneous whole-cell recordings of 6 pyramidal neurons in cortical slices, and measured paired connections by evoked monosynaptic responses. In these experiments, they measured synaptic connectivity between pyramidal neurons lacking the Pcdhgs, or overexpressing dissimilar or matching sets of Pcdhg isoforms introduced by electroporation of plasmids encoding Pcdhg cDNAs.

Overall, the study applies elegant methods that demonstrate that single cortical neurons express different combinations of Pcdh-gamma isoforms, including the upper layer Pyramidal cells that are assayed in paired recordings. The electrophysiology data demonstrate that nearby Pyramidal neurons lacking the entire Pcdhg cluster are more likely to be synaptically connected compared to the control neurons, and that overexpression of matching isoforms between pairs decreases the likelihood to be synaptically connected. These are important and compelling findings that advance the idea that the Pcdhgs are important for cortical synaptic connectivity, and that the repertoire of isoforms expressed by neurons influence their connectivity patterns potentially through a self/nonself discrimination mechanism. However, the findings are limited to probability in connectivity and do they do not support the authors' conclusions that Pcdhg isoforms regulate synaptic specificity, 'by preventing synapse formation with specific cells' or to 'unwanted partners'. Characterizations of the cellular basis of these defects are needed to determine whether they are secondary to other roles in cell positioning, axon/dendrite branching and synaptic pruning, and overall synaptic formation. Claims that Pcdh-alpha and Pcdhg C-type isoforms are not functionally required are premature, due to limitations of the experiments. Moreover, claims that 'similarity level of γPCDH isoforms between neurons regulate the synaptic formation' are not supported due to weak statistical analyses presented in Fig4. The overstatements should be corrected. There was also missed opportunity to clearly discuss these results in the context of other published work, including recent publications focused on the cortex.

Thank you for your feedback on the strengths and weaknesses of our work. In terms of the cellular basis of affected synaptic connectivity caused by γ-PCDH isoforms, we have compared the probability of connectivity for neuronal pairs with similar range of distance. Our findings indicate that the manipulation primarily affects pairs within the 50-150 micrometer range, suggesting that cell positioning might be a critical factor for the impact of γ-PCDH on synapse formation. However, we acknowledge that we couldn't definitively determine whether the negative effect on synaptic connectivity stems directly from impaired synapse formation or indirectly from synaptic pruning or the influence of PCDHγ on axon/dendritic branching. We've added these limitations to our discussion to provide a more comprehensive view of our research. Furthermore, we've adjusted our statements to better reflect the significance of our findings. Your feedback has been instrumental in improving the clarity and depth of our manuscript.

Strengths:

• The 5' end sequencing with a Pcdhg-amplified library is a technical feat and addresses the pitfall of conventional scRNA-Seq methods due to the identical 3'sequences shared by all Pcdhg isoform and the low abundance of the variable exons. New figures with annotated cell types confirm that several pyramidal and inhibitory cortical subpopulations were captured.

Statistical assessment of co-occurrence of isoform expression within clusters is also a strength.

• By establishing the combinatorial expression of Pcdhgs by maturing pyramidal cells, the study further substantiates the 'single neuron combinatorial code for cPcdhs' model. Although combinatorial expression is not universal (ie. serotonergic neurons), there was limited evidence. The findings that individual pyramidal neurons express ~1-3 variable Pcdhg transcripts plus the Ctype transcripts aligns with single RT-PCR studies of single Purkinje cells (Esumi et al 2005; Toyoda et al 2014). They differ from the findings by Lv et al 2022, where C-type expression was lower among pyramidal neurons. OSNs also do not substantially express C-type isoforms (Mountoufaris et al 2017; Kiefer et al 2023). Differences, and the advantages of the 5'end -directed sequencing (vs. SmartSeq) could be raised in the discussion.

• Simultaneous whole-cell recordings and pairwise comparisons of pyramidal neurons is a technically outstanding approach. They assess the effects of Pcdhg OE isoform on the probability of paired connections.

• The connectivity assay between nearby pairs proved to be sensitive to quantify differences in probability in Pcdhg-cKO and overexpression mutants. The comparisons of connectivity across vertical vs lateral arrangement are also strengths. Overexpressing identical Pcdhg isoform (whether 1 or 6) reduces the probability of connectivity, but there are caveats to the interpretations (see below).

Weaknesses:

n earby pairs but are not sufficient evidence for synapse specificity. The cPcdhs play multiple roles in neurite arborization, synaptic density, and cell positioning. Kostadinov 2015 also showed that starburst cells lacking the Pcdhgs maintained increased % connectivity at maturity, suggesting a lack of refinement in the absence of Pcdhgs. The known roles raise questions on how these manipulations might have primary effects in these processes and then subsequently impact the probability of connectivity. Investigations of morphological aspects of pyramidal development would strengthen the study and potentially refine the findings. The authors should more clearly relate their findings to the body of cPcdh studies in the discussion.

Previous studies revealed the adverse effects of γ-PCDHs on dendritic spines, demonstrating that their absence results in increased dendritic spines density, while overexpression leads to a reduction. In our study, we consistently observed that γ-PCDHs exert a negative influence on synaptic connectivity. This consistency strengthens the overall body of evidence in support of the role of γ-PCDHs in synaptic connectivity and dendritic spine regulation. While we have previously mentioned this point in our discussion to highlight the concordance between our findings and prior research, your input is greatly appreciated in reinforcing the scientific context of our work.

• Pcdhg cKO-dependent effects on connectivity occur between closely spaced soma (50-100um - Figure 2E), highlighting the importance of spatial arrangement to connectivity (also noted by Tarusawa 2016). Was distance considered for the overexpression (OE) assays, and did the authors note changes in cell distribution which might diminish the connectivity? Recent work by Lv et al 2022 reported that manipulating Pcdhgs influences the dispersion of clonally-related pyramidal neurons, which also impacts the likelihood of connections. Overexpression of Pcdhgc3 increased cell dispersion and decreased the rate of connectivity between pairs. Though these papers are mentioned, they should be discussed in more detail and related to this work.

Our data indicated that variable γ-PCDH isoforms primarily influence synaptic connectivity in neuronal pairs within the 50-150 micrometer range. Notably, as the distance between neurons increases, we observed a corresponding reduction in synaptic connectivity, as illustrated in Figure 2E. We have also included additional discussion regarding potential variances among different C-type isoforms.

• Though the authors added suggested citations and improved the contextualization of the study, several statements do not accurately represent the cited literature. It is at the expense of crystalizing the novelty and importance of this present work. For instance, Garrett et al 2012 PMID: 22542181 was the first to describe roles for Pcdhgs in cortical pyramidal cells and dendrite arborization, and that pyramidal cell migration and survival are intact. Line 52 cited Wang et al 2002, but this was limited to gross inspection. Garrett et al is the correct citation for: 'The absence of γ-PCDH does not cause general abnormality in the development of the cerebral cortex, such as cell differentiation, migration, and survival (Wang et al., 2002).' Second, single cell cPcdh diversity is introduced very generally, as though all neuron types are expected to show combinatorial variable expression with ubiquitous C-Type expression. But those initial studies were limited to Purkinje cells (Esumi 2005 and Toyoda 2014). Profiling of serotonergic neurons and OSN reveals different patterns (citations needed for Chen 2017 PMID: 28450636; Mountofaris et al PMID: 2845063; Canzio 2023 PMID: 37347873), raising the idea that cPcdh diversity and ubiquitous Ctype expression is not universal. Thus, the authors missed the opportunity to emphasize the gap regarding cPcdh diversity in the cortex.

We would like to extend our gratitude to the reviewer for pointing out the citation related to the roles of γ-PCDHs in the neocortex. After a thorough review of both papers, Wang et al., 2002 and Garrett et al., 2012, we concur that it would be more appropriate to cite both of these papers here. Your suggestion to underscore the diverse expression patterns of γPCDHs in neocortical neurons is well-received, and we have integrated this aspect of our findings with previous observations into a new paragraph within the discussion section. Your insights have greatly enriched the depth of our paper, and we genuinely appreciate your contribution.

• They have not shown rigorously and statistically that the rate of connectivity changes with% isoform matching. In Figure 4D, comparisons of % isoform matching in OE assays show a single statistical comparison between the control and 100% groups, but not between the 0%, 11% and 33% groups. Is there a significant difference between the other groups? Significant differences are claimed in the results section, but statistical tests are not provided. The regression analysis in 4E suggests a correlation between % isoform similarity and connectivity probability, but this is not sound as it is based on a mere 4 data points from 4D. The authors previously explained that they cannot evaluate the variance in these recordings as they must pool data together. However, there should be some treatment of variability, especially given the low baseline rate of connectivity. Or at the very least, they should acknowledge the limitations that prevent them from assessing this relationship. Claims in lines 230+ are not supported: ' Overall, our findings demonstrate a negative correlation between the probability of forming synaptic connections and the similarity level of γPCDH isoforms expressed in neuron pairs (Fig. 4E)".

We employed a bootstrap method to estimate the potential variance in the analysis presented in Fig. 4E. It's important to note that due to methodological limitations, a comprehensive assessment of variance based solely on recordings from a single animal is challenging. As such, we have adjusted our claims to be more aligned with our observations.

• Figure 4 provides connectivity probability, but this result might be affected by overall synapse density. Did connection probability change with directionality (e.g between red to green cells, or green to red cells).

As suggested by the reviewer, we have conducted an analysis to assess the directionality of connections under different conditions. This analysis involved comparing the directionalities of connections following the overexpression of six variable isoforms, as depicted in Fig. 3E. Upon examining 33 connected OE-Ctrl pairs following the electroporation of these 6 isoforms, we observed 3 pairs with bidirectional connections, 19 pairs with connections from OE to Ctrl, and 11 with connections from Ctrl to OE. To assess the statistical significance of these observations, we applied a Chi-square test. The results from this analysis indicated that there was no significant difference in the directionality of connections. These findings offer further support for the idea that overexpressing multiple γ-PCDH isoforms within a single neuron might not be sufficient to alter its connections with other neurons.

• Generally, the statistical approaches were not sufficiently described in the methods nor in the figure legends, making it difficult to assess the findings. They do not report on how they calculated FDR for connectivity data, when this is typically used for larger multivariate datasets.

We employed the False Discovery Rate (FDR) correction, specifically the BenjaminiHochberg method, to determine which values remained statistically significant. This method is widely accepted and involves inputting all the p-values and the total number, 'n.' Additional details about this correction are now provided in the Method section for clarity.

• The possibility that the OE effects are driven by total Pcdhg levels, rather isoform matching, should be examined. As shown by qRT-PCR in Fig. 3, expression of individual isoforms can vary. It is reasonable that protein levels cannot be measured by IHC, although epitope tags could be considered as C-terminal tagging of cPcdhs preserves the function in mice (see Lefebvre 2008). Quantification of constant Pcdhg RNA levels by qRT-PCR or sc-RT-PCR would directly address the potential caveat that OE levels vary with isoform combinations.

Through a series of multiple whole-cell recordings, we examined neuronal pairs within the 0% group, where both neurons exhibited overexpression of different combinations of γPCDH isoforms. What we discovered is that the connectivity level within pairs of neurons where both neurons overexpressed γ-PCDH isoforms, pairs with only one neuron overexpressing these isoforms, and pairs with two control neurons (lacking overexpression) was remarkably similar. However, as we incrementally raised the similarity level between the recorded neurons by increasing the overlap in the combinatorial expression of γ-PCDH isoforms, we observed a gradual decrease in the connectivity probability between these neurons. Notably, the connectivity probability reached its minimum when the recorded cells had the exact same combinatorial expression of γ-PCDH isoforms at the 100% similarity level. These findings suggest that the similarity level between neurons, rather than the absolute expression level of γ-PCDH isoforms, plays a critical role in affecting synapse formation.

-A caveat for the relative plasmid expression quantifications in Figure 3-S1 is that IHC was used to amplify the RFP-tagged isoform, and thus does not likely preserve the relationship between quantities and detection.

We attempted to enhance the mNeongreen signal, known for its exceptional signal-tonoise ratio, by utilizing the 32f6-100 antibody from Chromotek. However, our observations did not reveal any additional cells through immunostaining compared to the images obtained solely based on the mNeongreen signal. This indicates that the application of the available antibody did not yield a significant improvement in cell detection.<br /> It's important to emphasize that if the RFP signal is overvalued, it would result in an increase in both the "red only" and "red in total" categories. However, it's worth noting that the "red only" category is more sensitive to the outcome than the "red in total" category. Therefore, an overvaluation of the RFP signal would lead to an underestimation of the total estimated plasmid content in electroporated neurons. Consequently, this would result in a lower estimate for the proportion of co-expression cells rather than a higher estimate. We have updated the calculation method in the "Estimating the numbers of overexpressed γPCDH isoform" section to reflect these considerations.

• Figure 1 didn't change in response to reviews to improve clarity. New panels relating to the scRNASeq analyses were added to supplementary data but many are central and should be included in Figure 1 (ie. S1-Fig6D). In the Results, the authors state that neuronal subpopulations generally show a combinatorial expression of some variable RNA isoforms and near ubiquitous C-type expression. But they only show data for the Layer 2/3 neuron-specific cluster in S1-Fig-6D, and so it is not clear if this pattern applies to other clusters. Fig. S1-5 show a low number of expressed isoforms per cell, but specific descriptions on whether these include C-type isoforms would be helpful. Figure 1F showing isoform profile in all neurons is not particularly meaningful. There is a lot of interest in neuron-type specific differences in cPcdh diversity, and the authors could highlight their data from S1-5 accordingly.

In addition to the layer 2/3 cluster, we observed a diverse combinatorial expression of various variable γ-PCDH isoforms alongside nearly ubiquitous C-type expression in all other clusters of cells. We have now explicitly mentioned this observation in the main text. To underscore this point further, we have included a new figure, Fig. 1-S6, which provides information on the similarity analysis for all other clusters. It's important to note that the data in previous Fig. S1-5 (now renumbered as S1-7) were solely related to "variable" isoforms. We apologize for any confusion and have made this clarification by including it in the title of the figure.

• The concept of co-occurrence and results should be explained within the results section, to more clearly relate this concept to data and interpretations. Explanations are now found in the methods, but this did not improve the clarity of this otherwise very interesting aspect of the study.

Thanks for your suggestion. We have incorporated some of the explanations from the methods section into the main text t, mainly for the concept of “co-occurence”.

• The claim that C-type Pcdhgs do not functionally influence connectivity is premature. Tests were limited to PcdhgC4, which has unique properties compared to the other 2 C-type isoforms (Garrett et al 2019 PMID: 31877124; Mancia et al PMID: 36778455). The text should be corrected to limit the conclusion to PcdhgC4, and not generally to C-type. The authors should test PcdhgC3 and PcdhgC5 isoforms.

We have changed the claim for PcdhgC4, but not generally for C-type to better reflect our observation.

• The group generated a novel conditional Pcdh-alpha mouse allele using CRISPR methods, and state that there were no changes in synaptic connectivity in these Pcdh-alpha mutants. But this claim is premature. The Southern blots validate the targeting of the allele. But further validations are required to establish that this floxed allele can be efficiently recombined, disrupting Pcdha protein levels and function. Pcdha alleles have been validated by western blots and by demonstration of the prominent serotonergic axonal phenotype of Pcdha-KO (ie. Chen 2017 PMID: 28450636; IngEsteves 2018 PMID: 29439167).

We have obtained a new set of qRT-PCR data that confirms the decreased expression of α-PCDH in Pcdha CKO mice. These data have been integrated into Figure 2-S2D.

• The Discussion would be strengthened by a deeper discussion of the findings to other cPcdh roles and studies, and of the limitations of the study. The idea that the Pcdhgs are influencing the rate of connectivity through a repulsion mechanism or synaptic formation (ie through negative interactions with synaptic organizers such as Nlgn - Molumby 2018, Steffen 2022) could be presented in a model, and supported by other literature.

I would like to express my sincere appreciation to the reviewer for their invaluable comments and suggestions, which have led to extended discussions within our work. We have incorporated these suggestions into our paper to establish stronger connections between our observations and prior research findings.

Reviewer #1 (Recommendations For The Authors):

1) In Figure S6, the authors measured Euclidean distance from the single cell data to take account of the isoform expression levels in explaining diversity. However, it is hard to interpret the data without any control. The authors could measure the same value from a shuffled /randomized dataset for comparison (similarly to Fig 1F).

We understand the reviewer's concern about the significance of the Euclidean distance analysis without an appropriate control. The inclusion of the Euclidean distance metric was initially a response to suggestions from other reviewers who recommended incorporating diverse methods for analyzing expression patterns among neurons.

In response to your valuable feedback, we have taken measures to address these concerns. We have introduced shuffled data for comparison, thus enhancing the meaningful context for interpreting the results derived from the Euclidean distance analysis.

2) The authors need to clarify which cortical regions were used for electrophysiological experiments.

Apologies for any confusion. To clarify, all recordings were conducted on neurons located in layer 2/3 of the neocortex without further discrimination. We have reinstated this information in both the main text and the methods section to ensure its clarity.

Reviewer #2 (Recommendations For The Authors):

There are still some issues that must be addressed.

1) The references to gamma protocadherin repulsion are not correct in context. A repulsive role of homophilic interaction has been inferred from certain knockout phenotypes in a subset of neurons (not in cortical neurons). However, repulsion has never been shown to follow gamma protocadherin engagement. The authors present no new evidence that their results are attributable to cellular repulsion at nascent synaptic contacts. The mechanism is unknown. The references to repulsion to explain their results should make it clear that this is one possible explanation, but it is not shown. Also some references in the text are not correct. For example, line 63/64: the results of Molumby and Steffen are not involving homophilic adhesion or repulsion, but rather a cis interaction with neuroligins. Those papers should not be discussed as involving repulsion as in the reference to Lefebvre 2012. Also line 268/269 "Together with previous findings (Molumby,,,Tarusawa), our observations solidify repulsion effect of g-PCDH on synapse formation. . .". This is not the case. Neither Molumby nor Tarusawa demonstrated any such repulsion.

Thank you to the reviewer for pointing out the errors in our citations. We have made the necessary corrections to the citations and have also refined the descriptions of our observations to improve clarity and accuracy.

2) The discussion of the results when C4 is overexpressed must also be greatly toned down. C4 is a strange C-type protein--it cannot get to the cell surface alone but relies on other cPCDHs for this, and its primary role is in preventing cell death. It is odd that the authors used this isoform to represent C-types. They should have used C3, which two recent papers showed have specific roles at some synapses (Meltzer et al 2023, Ginty lab) and in dendrite branching (Steffen et al 2023, Weiner lab) , or C5. It is entirely possible that just C4 has no role in synaptic matching--but C3 and C5 might. They should not conclude that the C-types have no such role and only A and B types do. That must be toned down (e.g., line 198/199, line 281).

We acknowledge that using C4 to represent all three C-types (C3, C4, and C5) is not accurate. We have now modified the statement in the main text to rectify this.

3) For the citation of Pcdhg flox/flox mice (line 126), Prasad et al., Development, 2008, Weiner lab, should also be cited as it fully characterized that line that was also used in Lefebvre et al 2008. They were co-published.

Thank you for highlighting the missing citation, and we have now included it in the relevant section.

4) the Pcdh alpha KO Mouse characterization is still insufficient. The authors must show that alpha expression is gone following introduction of Cre, either by RT-PCR using alpha constant domain primers, or an alpha antibody on Western. blot. The southern and off-target sequencing do not confirm that all alpha gene expression is gone.

Thank you for your feedback. We have conducted the qRT-PCR analysis as per your suggestion. The results clearly indicate a substantial reduction in α-PCDH expression within the neocortex of Pcdha cKO mice. We have thoughtfully incorporated this data into the manuscript, and it is visually represented in the new panel of Figure 2-S2D. Your valuable input has contributed to enhancing the quality of our work, and we sincerely appreciate the opportunity to address this important aspect.

5) I do not understand something in Figure 4-S1A. Why with 0% matching is synaptic connectivity so low? This is not the same as in Figure 3E. This has to be explained because it does suggest that overexpression of ANY isoforms can inhibit synapse formation, which is consistent with Molumby 2017, even though this paper says it is not just the levels but the isoform specificity.

The panel of Fig.4-S1A illustrates the connection rate between neurons with the same color (icons in upper left), representing cells that express the same combination of γ-PCDHs (100% of similarity). The X-axis (0%, 11%, 33%, and 100%) reflects the similarity level between the 2 populations of cells (GFP and RFP).

6) There are still issues with the English grammar in the paper. It is not too bad in the main text but someone should re-edit it. However, the figure legends are indeed much worse and truly must be edited professionally before they are acceptable.

We apologize for our English writings in the paper. We have now polished most part of the manuscript, especially the parts for figure legends.

Reviewer #3 (Recommendations For The Authors):

• This study has many strengths and innovative findings. Most comments above included suggestions to strengthen the paper. The overall message that Pcdhgs influence the rate of synaptic connectivity between nearby cells is compelling. How this Pcdhg-isoform-dependent process could influence synaptic specificity can be explored in a model in the discussion. But this study did not test a role in 'synaptic specificity'; this term should be removed from the title and line 81 in the intro.

Thank you for your invaluable comments aimed at improving our paper. Regarding the title, we believe that "synaptic connectivity" might be a more suitable choice than "synaptic specificity." However, we're open to considering other alternatives as well.

• The manuscript and overall quality of the science will be improved by removing those sections that are not adequately investigated (ie.Pcdh-a cKO; PcdhgC4 is assessed but findings can't be extended to other C-type isoforms) and by outlining limitations of the study.

We have modified the related claim mentioned in the main text.

• The studies negatively correlating between isoform matching and connectivity are not robust. Additional approaches are needed if the authors want to make this claim.

In Figure 4E, we have implemented a bootstrapping method. Bootstrapping is a statistical technique falling under the broader category of resampling methods. It involves random sampling from the observed data with replacement, enabling the calculation of standard errors, confidence intervals, and supporting hypothesis testing.

• Statistical approaches should be described in methods, figure legends.

More information about statistical approaches has been added in the figure legends.

• The discussion should elaborate on the limitations of the study, and relate to other studies, including Lv et al 2022.

We have added more discussion to relate our observations to previous findings.

Author Response

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

Reviewer 1

R1.1) Although very robust and capable of handling several situations, the researcher has to keep in mind that processing has to follow some basic rules in order for this pipeline to work properly. For instance, fiducials and scales need to be included in the photograph, and the slabs must be photographed against a contrasting background.

Our pipeline does indeed have some prerequisites in terms of data acquisition – at the very least, a ruler must be present in the photographs. A contrasting background is not strictly needed, but does definitely facilitate segmentation. We have edited the Introduction and Discussion to emphasize these prerequisites.

R1.2) Also, only coronal slices can be used, which can be limiting for certain situations.

While the 3D reconstruction based on Eq. 1 is quite general, the segmentation is indeed tailored to coronal slices of the cerebrum. As explained in the paper, this orientation is standard when slicing the cerebrum, but axial or sagittal slicing may also be of interest – particularly when dissecting the brainstem or cerebellum. We acknowledge this limitation in the Discussion of the revised manuscript.

R1.3) In the future, segmentation of the histological slices could be developed and histological structures added (such as small brainstem nuclei, for instance). Also, dealing with axial and sagittal planes can be useful to some labs.

While outside the scope of this paper, these are good ideas for future directions, and are considered in the Discussion of the revised version.

Reviewer 2

R2.1) The current method could only perform accurate segmentation on subcortical tissues. It is of more interest to accurately segment cortical tissues, whose morphometrics are more predictive of neuropathology. The authors also mentioned that they would extend the toolset to allow for cortical tissue segmentation in the future.

We agree with the reviewer that cortical parcellation has high value. We have included a new option in Photo-SynthSeg to parcellate the cortex using a machine learning block already existing in SynthSeg 2.0 (Billot et al, PNAS, 2023); see example in Figure 2 of the revised manuscript. This parcellation is volumetric; more accurate methods based on surfaces are out of the scope of this article and remain as future work. The manuscript has been edited to reflect these changes.

R2.2) Brain tissues are not rigid bodies, so dissected slices could be stretched or squeezed to some extent. Also, dissected slices that contain temporal poles may have several disjoined tissues. Therefore, each pixel in dissected photographs may go through slightly diFerent transformations. The authors constrain that all pixels in each dissected photograph go through the same aFine transform in the reconstruction step probably due to concerns of computational complexity. But ideally, dissected photographs should be transformed with some non-linear warping or locally linear transformations. Or maybe the authors could advise how to place diFerent parts of dissected slices when taking dissection photographs to reduce such non-linearity of transforms.

The reviewer is totally right. The problem with nonlinear warps is that, albeit trivial to implement, they compromise the robustness of the registration pipeline. This is because the nonlinear model introduces huge ambiguity in the space of solutions: for example, if one adds identical small nonlinear deformations to every slice, the objective function barely changes. The revised manuscript: (i) more thoroughly discussed this limitation; (ii) discusses nonlinear models for 3D reconstruction as future work; and (iii) makes recommendation about the tissue placement to minimize errors around the temporal pole.

R2.3) For the quantitative evaluation of the segmentation on UW-ARDC, the authors calculated 2D Dice scores on a single slice for each subject. Could the authors specify how this single slice is chosen for each subject? Is it randomly chosen or determined by some landmarks? It's possible that the chosen slice is between dissected slices so SAMSEG cannot segment accurately.

The slice is chosen to be close to the mid-coronal plane, while maximizing visibility of subcortical structures. The chosen slice is always a “real” dissected slice (rather than a digital “virtual” slice) and cannot be located in a gap between slices. This is clarified in the Quantitative Evaluation section of the revised manuscript.

R2.4) Also from Figure 3, it seems that SAMSEG outperforms Photo-SynthSeg on large tissues, WM/Cortex/Ventricle. Is there an explanation for this observation?

Since we use a single central coronal slice when computing Dice, SAMSEG yields very high Dice scores for large structures with strong contrast (e.g., the lateral ventricles). However, Photo-SynthSeg provides better results across the board, particularly when considering 3D analysis (see Figure 2 and results on volume correlations). We have added a comment on this issue to the revised manuscript.

R2.5) In the third experiment, quantitative evaluation of 3D reconstruction, each digital slice went through random aFine transformations and illumination fields only. However, it's better to deform digital slices using random non-linear warping due to the non-rigidity of the brain as mentioned in R2.2. So, the reconstruction errors estimated here are quite optimistic. It would be more realistic if digital slices were deformed using random nonlinear warping.

We agree with the reviewer and, as we acknowledge in the manuscript, the validation of the reconstruction error with synthetic data is indeed optimistic. The problem with adding nonlinear warps is that the results will depend heavily on the strength of the simulated deformation. We keep the warps linear as we believe that the value of this experiment lies in the trends that the errors reflect, as a function of slice thickness and its variability (“jitter”). This has been clarified in the revised manuscript.

Reviewer 2 (recommendations for the authors)

AR2.1) In the abstract, the authors mentioned that the segmentations of the 3D reconstructed stack deal with 11 brain regions, however, in most sections, only 9 tissue masks were compared, such as in Table 1, 2, and Figure 3. Also in the supplementary video, there are only 10 rendered tissues. So, what are these 11 regions? Is the background nonbrain region also counted as a region? And how these 11 regions were derived from the original 36 annotated tissues in T1-39?

We particularly thank the reviewer for noticing this.

The 11 regions are white matter, cortex, ventricle, thalamus, caudate, putamen, pallidum, hippocampus, amygdala, accumbens area, and ventral diencephalon. These are all bilateral labels, i.e., 22 regions in total. The original 36 labels include these 22 and: four labels for the cerebellum (left and right cortex and white matter); the brainstem; five labels for cerebrospinal fluid regions that we do not consider; the left and right choroid plexus; and two labels for white matter hypo intensities in the left and right hemisphere.

As in many other papers, we leave “ventral diencephalon” and “accumbens area” out of the validation as they are not very well defined.

We note that all regions except the accumbens are visible in Figure 1d. The ventral diencephalon is easy to miss as only a small portion of it is visible (when picking a slice, one needs to compromise in terms of how much of each structure is visible). Moreover, it has a very similar color to the cortex in the FreeSurfer convention (see picture below).

Author response image 1.

The accumbens is visible at 1m45s in the, segmented in orange (see capture below).

Author response image 2.

We have clarified these issues in the reviewed version of the manuscript.

RA2.2) In Figure 1(f), why are the hippocampal volumes of confirmed AD subjects larger than those of the healthy controls? Is this a typo or is there any explanation for this?

Yes, it is a typo. Again, thank you very much for noticing this.

RA2.3) Typo on P3, "sex and gender were corrected" should be "age and gender were corrected".

This has been corrected in the revised version.

RA2.4) In the MADRC dataset, the authors mentioned that there are 18 full brains and 58 hemispheres, however, the total data size is 78. Is this a typo?

Yes, it is. It has been corrected in the revised version.

RA2.5) Comparing the binary masks in Figure 5(d) and the photographs in Figure 5(c), some tissues below the ventricles with high intensities are also removed from masks. Is this done by manual editing? If so, how long does it usually take to edit a clean mask for each subject?

We used a combination of thresholding, morphological operations (erosion/dilation), and minor manual edits when needed – particularly to remove chunks of pial surface when they are visible, in the most anterior slices. The average is a couple of minutes per photograph. In the future, we plan to use these manually curated images to train a supervised convolutional neural network to perform the task automatically. These details are provided in the revised manuscript.

RA2.6) In the method of 3d reconstruction, there are four weights for the optimization function. How did the authors determine such weights and do these weights have some impact on the reconstruction performance?

The parameters were set by visual inspection of the output on a small pilot dataset, and do not have a strong impact on the reconstruction. The crucial aspect is to increase 𝜈 (the affine regularizer) and decrease 𝛼 (compliance with the external reference) when using a soft reference. These details have been added to the revised version.

RA2.7) Finally for the deep learning-based segmentation, a U-Net was trained on GMM generated single-channel intensity synthetic images while the dissected photographs are color images with three channels. So, did the authors only input the grayscale photographs to the segmentation network? Are there any other preprocessing steps for color photographs, such as normalization? Is it possible to use GMM to generate color images as training data to better suit dissection photography?

We did try simulating three channels during training, but the performance was actually worse than when simulating one channel and converting the RGB input to grayscale. This information has been added to the revised version.

Author Response

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

We thank the reviewers for their time and insightful and constructive comments. We are pleased that reviewers found this study “opens the way for novel future work” and the findings “interesting”. We have experimentally addressed the points raised by the reviewers and have substantially revised the manuscript by modifying 30 figures panels. The reviewers’ points are specifically addressed below.

1) The authors concluded that an accumulation of Ly6Clo monocytes occurred in the Rbpjfl/fl Lyz2cre/cre mouse by examining the percentage of cells among CD45+ cells in Figure 1. It would be helpful if the authors could give an account of the total cell count numbers of monocyte subsets per ml of blood and in the bone marrow to give the readers a better idea of the extent of increase as cell percentages among CD45+ cells may be influenced by the number of other immune subsets.

We thank the reviewer for raising these points. In this research, we crossed Rbpjfl/fl mice with Lyz2-Cre mice carrying the Cre recombinase inserted in the Lysozyme-M (Lyz2) gene locus results in the selective deletion of RBP-J in myeloid cells, such as monocytes, macrophages and granulocytes. We then proceeded to examine the neutrophil levels in the bone marrow and blood. The percentage of neutrophils observed was found to be similar to that of control mice, which was in line with the findings reported in the literature (Metzemaekers et al. 2020). Furthermore, the proportion of Ly6Chi monocytes in RBP-J deficient mice was found to be similar to that of control mice, which is consistent with the literature (Ginhoux et al. 2014). Based on these results, we thought that the changes observed in the proportion of Ly6Clo monocytes could reliably indicate the alterations occurring in Ly6Clo monocytes within the Rbpjfl/flLyz2cre/cre mice.

2) The authors demonstrated no significant differences in bone marrow progenitor and monocyte numbers, therefore concluding that monocyte egress from the bone marrow did not contribute to the increase in Ly6Clo monocyte numbers in the blood (Figure 1B-D). As it is unclear what is the exact cell number increase in the blood, the changes in bone marrow monocyte numbers might be too small to be reflected in their percentage calculations. In light that CCR2 was also found to play a role in Ly6Clo monocyte homeostasis in Rbpjfl/fl Lyz2cre/cre mice, could the authors demonstrate if Rbpj-deficient Ly6Clo monocytes might be more responsive to CCL2 through transwell experiments? This would also provide readers a more in-depth mechanism of how an increase in CCR2 on Rbpj-deficient Ly6Clo monocytes leads to their accumulation in the periphery.

The experimental results regarding the proportion of monocytes and precursor cells in the bone marrow were derived from multiple experiments. The data obtained from individual experiments as well as the final integrated data did not reveal significant differences between the control mice and Rbpjfl/flLyz2cre/cre mice. Therefore, we believed that even if there were small changes in cell numbers, these differences could still be reflected through alterations in their proportions. We attempted transwell experiments, but unfortunately, they were not technically successful. Nearly all sorted Ly6Clo monocytes attached to the transwell membrane, making it challenging to draw a conclusion regarding the responsiveness of RBP-J deficient Ly6Clo monocytes to CCL2.

3) In the parabiosis experiment conducted in Figure 3C-E, the authors provide conclusive evidence that the accumulation of Rbpj-deficient Ly6Clo monocytes was cell intrinsic as Rbpj-deficient Ly6Clo monocytes continued to accumulate in the blood of control counterparts. Monocytes have also been shown to accumulate in the spleen and re-enter or home back to the bone marrow. Assessing if there is a change in monocyte homing abilities in Rbpj-deficient Ly6Clo monocytes by examining their numbers in the spleen and bone marrow of control parabiotic mice would substantiate their claims that the defect was cell intrinsic and provide further understanding for the readers of why Rbpj-deficient Ly6Clo monocytes accumulate in the blood.

We thank the reviewer for bringing out this interesting point. We also analyzed the proportions of GFP- Ly6Chi monocytes and Ly6Clo monocytes in the bone marrow of parabiotic mice. The experimental results revealed that there were no significant differences in the proportion of GFP- monocytes between the control mice and the KO animals (see the figure A below). We also detected the expression of CXCR4 in bone marrow Ly6Clo monocytes. Rbpjfl/flLyz2cre/cre mice exhibited normal expression of CXCR4 (see Author response image 1 below), which participates in the homing of classical and nonclassical monocytes to bone marrow and spleen monocyte reservoirs (Chong et al. 2016). The homing abilities of RBP-J deficient Ly6Clo monocytes may not have changed.

Author response image 1.

4) Authors should provide cell counts for Figure 5B to demonstrate the extent CCR2 depletion affects the number of Ly6Clo monocytes in Rbpjfl/fl Lyz2cre/cre mice as explained in point 1.

As mentioned before, we believed that the proportion of circulating monocytes could, to some extent, provide evidence of the impact of CCR2 deficiency on Ly6Clo monocytes.

Reviewer #2

1) The confirmation of knockout in supplemental figure 1A shows only a two third knockdown when this should be almost totally gone. Perhaps poor primer design, cell sorting error or low Cre penetrance is to blame, but this is below the standard one would expect from a knockout.

Kang et al (PMID: 31944217) evaluated the knockout efficiency of Rbpj in sorted colonic macrophages of Rbp-jfl/flLyz2cre/cre mice using qPCR and immunoblotting. The qPCR result indicated a two-third knockdown, while the immunoblotting results demonstrated efficient deletion of RBP-J protein in Rbp-jfl/flLyz2cre/cre mice. As pointed out by the reviewer, the observed two-third knockdown, which is lower than the expected complete knockout, may be attributed to primer design.

2) Many figures (e.g. 1A) only show proportional data (%) when the addition of cell numbers would also be informative

We appreciate the reviewer for bringing up these points. Indeed, multiple articles studying monocytes only show changes in cell proportions. As mentioned above, we believed that analyzing the proportion of circulating monocytes could offer valuable evidence of the influence of RBP-J deficiency on Ly6Clo monocytes.

3) Many figures only have an n of 1 or 2 (e.g. 2B, 2C)

Here, we employed annexin V (AnnV) and propidium iodide (PI) staining to evaluate apoptosis and cell death in Ly6Chi and Ly6Clo blood monocytes from control and RBPJ deficient mice. The results showed no significant difference in the levels of apoptosis and cell death between the two groups (see Author response image 2 below). The statistical data for Ki-67 expression obtained from multiple experiments, and the expression of Ki-67 showed no significant difference between the control and RBP-J deficient mice (see the figure B below). In Figure 2C, each dot represents 2-3 mice, and there were no differences observed between control and RBP-J deficient mice at multiple time points during the repeated measurements.

Author response image 2.

4) Sometimes strong statements were based on the lack of statistical significance, when more n number could have changed the interpretation (e.g. 2G, 3E)

We have derived the corresponding conclusions based on the observed experimental results.

5) There is incomplete analysis (e.g. Network analysis) and interpretation of RNAsequencing results (figure 4), the difference between the genotypes in both monocyte subsets would provide a more complete picture and potentially reveal mechanisms

We thank the reviewer for bringing out this point. We agreed that a more comprehensive analysis, including a comparison between the genotypes in both monocyte subsets, would provide a deeper understanding and potentially uncover underlying mechanisms. Having observed alterations in blood Ly6Clo monocytes in RBP-J deficient mice, our primary focus had been on analyzing the differentially expressed genes within this subset of monocytes to gain further insights into its specific characteristics and behavior. We also uploaded sequencing data sets in the Genome Expression Omnibus with assigned accession numbers GSE208772 to facilitate interested researchers in accessing and downloading the data.

6) The experiments in Figures 5 and 7 are missing a control (Lyz2cre/cre Ccr2RFP/RFP or the Rbpj+/+ versions) and may have been misinterpreted. For example if the control (RBP-J WT, CCR2 KO) was used then it would almost certainly show falling Ly6C low numbers compared to RBP-J WT CCR2 WT, but RBP-J KO CCR2 KO would still have more Ly6c low monocytes than RBP-J WT, CCR2 KO - meaning that the RBP-J function is independent of CCR2. I.e. Ly6c low numbers are mostly dependent on CCR2 but this is irrespective of RBP-J.

The diminished Ly6Clo monocytes in Rbpjfl/flLyz2cre/creCcr2RFP/RFP (DKO) mice can be divided into two distinct subpopulations: one portion originates from Ly6Chi monocytes, while the other comprises Ly6Clo monocytes characterized by heightened CCR2 expression. The Ly6Clo monocytes that remain in DKO mice exhibit CCR2 expression levels within the normal range when compared to Lyz2cre/cre mice, but lower levels compared to RBP-J deficient mice (Figure 5A). These findings suggest that RBP-J exerts regulatory influence over Ly6Clo monocytes, at least in part, through CCR2.

7) Figure 6 was difficult to interpret because of the lack of shown gating strategy. This reviewer assumes that alveolar macrophages were gated out of analysis

The gating strategy of lung interstitial macrophage in the manuscript Figure 6 was consistent with the published work (Schyns et al, cited in the manuscript). We also measured alveolar macrophages (AM) from control and RBP-J deficient mice bronchoalveolar lavage fluid. At the resting state, RBP-J deficient mice exhibited normal AM frequency and number (see Author response image 3 below).

Author response image 3.

8) The statements around Figure 7 are not completely supported by the evidence, i) a significant proportion of CD16.2+ cells were CCR2 independent and therefore potentially not all recently derived from monocytes, and ii) there is nothing to suggest that the source was not Ly6C high monocytes that differentiated - the manuscript in general seems to miss the point that the source of the Ly6C low cells is almost certainly the Ly6C high monocytes - which further emphasises the importance of both cells in the sequencing analysis

Schyns et al and Sabatel at al showed that the numbers of IM and CD16.2+ were similar in Ccr2 sufficient and Ccr2-/- mice, demonstrating that CD16.2+ cells were Ccr2 independent. The number of CD16.2+ cells was significantly reduced in Rbpjfl/flLyz2cre/creCcr2RFP/RFP mice as compared to Rbpjfl/flLyz2cre/cre mice, in line with decreased number of lung Ly6Clo monocytes and blood Ly6Clo monocytes, showing that CD16.2+ cells depended on Ccr2 for their presence in Rbpjfl/flLyz2cre/cre mice.

9) The authors did not refer to or cite a similar 2020 study that also investigated myeloid deletion of Rbpj (Qin et al. 2020 - https://doi.org/10.1096/fj.201903086RR). Qin et al identified that Ly6Clo alveolar macrophages were decreased in this model - it is intriguing to synthesise these two studies and hypothesise that the ly6c low monocytes steal the lung niche, but this was not discussed

We thank the reviewer for bringing this study to our attention. According to their findings, myeloid-specific RBP-J deficiency resulted in a decrease in Ly6CloCD11bhi alveolar macrophages but an increase in Ly6CloCD11blo alveolar macrophages after bleomycin treatment, while the total number of alveolar macrophages showed no significant difference. These results suggest that RBP-J may play a role in regulating the balance between these specific alveolar macrophage subsets in response to bleomycin-induced injury, without affecting the overall population of alveolar macrophages. This may be different from what we observe in interstitial macrophages under resting conditions.

Reviewer #3

1) It is curious that the authors do not see the increase in circulating monocytes reflected in the spleen however, the n-number is 2. Increasing the n-number would enable the author to understand the data which is not interpretable at the moment. There are multiple other places in which a low n-number makes it hard to fully understand the biology (eg Figure 2C&E)

Although we only counted the number of splenic monocyte subsets in two mice, the proportion of splenic monocyte subsets was calculated based on additional quantity of mice in our study.

2) Given that Ly6Clow monocytes are thought to be longer lived than Ly6C+ and there is still considerable labelling of Ly6Clow monocytes at the end of the 96 hours analysed in the EdU experiment, it is not possible to determine from the data here whether RBPJ deficiency increases life span. Could it be that differences in %EdU+ cells would only be seen at later time points? If the timeline was extended, could it be that differences in %EdU+ become apparent

Based on the latex bead experiment, we observed that the presence of latex+ Ly6Clo monocytes at 7 days in control and RBP-J deficient mice did not differ, indicating that the lifespan of Ly6Clo monocytes did not increase.

3) Similarly for the latex bead experiment. Given that there is only n=2 at the first time point and only ~30% of Ly6Clow monocytes are Latex+, it is very hard to conclusively claim that RBP-J does not influence monocyte survival or proliferation. An interesting experiment to assess whether RBP-J is increasing monocyte survival could be an adoptive transfer model in which Ly6Clow monocytes are injected into a congenic mouse and tracked over time.

In RBP-J deficient mice, there was an increase in the proportion of Ly6Clo monocytes. We hypothesized that this lower proportion of latex+ cells might make it easier to observe differences, but clearly, in our experiment, no differences were observed between control and RBP-J deficient mice.

4) RNA-seq: Ccr2 and Itgax are not the top hits. The authors do not investigate the top hits which may provide very interesting insight into how RBP-J influences monocyte biology.

We thank the reviewer for raising these points. We also analyzed some top changed genes. The top two gene in the downregulated gene list are Hes1 and Nrarp, which are regulated by the Notch pathway (Krebs et al 2001 and Radtke et al 2010). We tested blood monocytes, but the population of monocyte subsets displayed no differences between Hes1fl/flRbp-jfl/flLyz2cre/cre and Rbp-jfl/flLyz2cre/cre mice (data not shown). As shown in Figure 2- figure supplement 1A, expression of Nr4a1 showed no significant differences between control and RBP-J deficient mice. The top gene in the upregulated gene list is Erdr1, which has been reported to play a role in cellular survival (Soto et al 2017), while blood monocyte subsets in RBP-J deficient mice displayed normal survival.

5) The PCA plot in figure 4C- it would be interesting to see where all the biological replicates fall.

We agree with the reviewer’s assessment that observing the positions of all biological replicates on the PCA plot may indeed yield valuable insights. However, it is worth noting that the upregulated and downregulated genes also offer suggestive hints.

6) Based on CCR2 expression and CD11c expression, monocytes from RBP-J deficient mice look more like Ly6C+ monocytes - could it be that RBP-J is increasing conversion from Ly6C+ monocytes to Ly6Clow? Or could it be that Ly6Clow monocytes are heterogeneous and RBP-J is increasing survival or conversion of one subtype of Ly6Clow monocytes but looking at all Ly6Clow monocytes together is masking this?

Ly6Clo monocyte can be subdivided into different subpopulations depending on surface makers, such as CD43, MHC-II, CD11c and CCR2 (Jakubzick et al 2013 and Ginhoux et al. 2014). Carlin et al founded that a subset of blood Ly6Clow cells was independent of both Ccr2 and Nr4a1. As said by the reviewer, Ly6Clo monocytes are heterogeneous. Therefore, there is a possibility of altered survival in a certain group of Ly6Clo monocytes.

7) The data presented here suggest that lung CD16.2+ interstitial macrophages are derived from Ly6Clow monocytes which are increased via CCR2. Although the data are suggestive, they are not conclusive, lineage tracing and CCR2 blockade or better, conditional CCR2 deficiency would help to strengthen the claim.

Schyns et al showed that the number of CD16.2+ was similar in Ccr2 sufficient and Ccr2-/- mice, demonstrating that CD16.2+ cells were Ccr2 independent. While number of CD16.2+ cells was significantly reduced in Rbpjfl/flLyz2cre/creCcr2RFP/RFP mice as compared to Rbpjfl/flLyz2cre/cre mice, in line with decreased number of lung Ly6Clo monocytes and blood Ly6Clo monocytes. Moreover, the turnover of lung Ly6Chi and Ly6Clo monocytes was normal. These results implicated that CD16.2+ cells depended on Ccr2 for their presence in Rbpjfl/flLyz2cre/cre mice.

8) The figures could do with more headings/ more detailed legends to help the reader, for example including what is BM, what is blood, what is spleen. Figure 2E needs the days labelled on or above the histograms.

We thank the reviewer for raising this important point. We have now added additional detailed legends to the figure.

9) Gating strategies should be included to help the reader understand which cells you are looking at, especially for Figure 6&7.

The gating strategy for Figures 6 and 7 followed the method reported in the literature, which included the identification of alveolar macrophages. Additionally, we labeled the markers for cell populations in the figure.

Author Response

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

Reviewer #1 (Recommendations For The Authors):

1) Line 99-100 The authors claimed that IQCH is a novel IQ motif-containing protein, which is essential for spermiogenesis and fertilization. However, it is not clear if the currently published paper named an ancient testis-specific IQ motif containing H gene that regulates specific transcript isoform expression during spermatogenesis.

Response: Thanks to the reviewer’s comment. Yes, IQCH is the ancient testis-specific IQ motif containing H gene. According to the reviewer’s suggestion, we have revised the statement “Here, we revealed a testis-specific IQ motif containing H gene, IQCH, which is essential for spermiogenesis and fertilization” in Introduction part of revised manuscript.

2) Line 154-159 Immunofluorescence staining for the marker of the acrosome (peanut agglutinin: PNA) as well as the mitochondrial marker (Transcription Factor A, Mitochondrial: TFAM) was performed to confirm the deficiency of the acrosomes and mitochondria in the proband's spermatozoa. It seems that the spermatozoa acrosomes and mitochondria were severely defective in the proband. The authors should indicate IQCH's role in mitochondrial and acrosome function and IQCH's role in mitochondrial and acrosome function these points by explaining how IQCH is related to mitochondrial and acrosome deficiency. In addition to staining, other functional analyses should be performed to strengthen the claim of acrosome and mitochondrial defects.

Response: We appreciate the reviewer's valuable suggestion. Indeed, in our study, the results of multiomics analysis on WT and Iqch KO testes, including LC-MS/MS analysis, proteomic analysis, and RNA-seq analysis, found a potential role of IQCH in mitochondrial and acrosome function. GO analysis of these analysis indicated a significant enrichment in mitochondrial and acrosomal functions, including acrosomal vesicle, acrosome assembly, vesicle fusion with Golgi apparatus, mitochondrion organization, mitochondrial matrix, and so on. Among the enriched molecules, in particular, HNRNPK mainly expresses at Golgi phase and Cap phase (Biggiogera et al. 1993). ANXA7 is a calcium-dependent phospholipid-binding protein that is a negative regulator of mitochondrial apoptosis (Du et al. 2015). Loss of SLC25A4 results in mitochondrial energy metabolism defects in mice (Graham et al. 1997). Furthermore, we confirmed that IQCH interacted with HNRNPK, ANXA7, and SLC25A4 through Co-IP, and exhibited downregulation in the sperm of the Iqch KO mice by immunofluorescence and western blotting. Moreover, IQCH can bind to HNRPAB, which could influence the mRNAs level of Catsper-family, such as Catsper1, Catsper2, and Catsper3, which are crucial for acrosome development (Jin ZR et al). In addition, we also detected HNRPAB binding to Dnhd1, which affects mitochondria development (Tan C et al). Therefore, in addition to staining, the other functional analyses also have provided the evidence of acrosome and mitochondrial defects caused by IQCH absence.

3) Line 180-182 IQCH knockout mice were generated. It is not clear why Mut-IQCH mice were not generated to be consistent with the human sequencing data.

Response: Thanks for reviewer’s comments. To understand IQCH's impact on fecundity in mice, we employed CRISPR-Cas9 to generate mice encoding the orthologous variant of IQCH387+1_387+10del detected in humans. Regrettably, due to sequence complexity, the designed sgRNA's specificity and efficiency were low, hindering successful Iqch knock-in mouse construction. Considering IQCH387+1_387+10del results in absent expression, we pursued Iqch knockout mice to explore IQCH's role in spermatogenesis.

4) Line 241.Figure 5A Gene Ontology (GO) analysis of the IQCH-bound proteins revealed a particular enrichment in fertilization, sperm axoneme assembly, mitochondrial organization, calcium channel, and RNA processing. But these GO functions are not shown in Figure 5A. The entire Figure 5 should be revised to enhance readability.

Response: We sincerely apologize for the oversight. These GO functions were indeed identified during the analysis of IQCH-bound proteins. Regrettably, we unintentionally omitted these GO functions when creating the plots. We have revised the plots in Figure 5 in revised manuscript to enhance readability.

5) Line 242 "33 ribosomal proteins were identified (Fig. 5B), indicating that IQCH might be involved in protein synthesis". The authors should perform an analysis to support the claim of protein synthesis defects.

Response: Thanks to reviewer’s suggestions. Initially, we have supplemented Co-IP experiments to confirm the interaction between IQCH and three ribosomal proteins (RPL4, RPS3, and RPS7), chosen from a pool of 33 ribosomal proteins based on different protein scores (Figure R1). In addition, the proteomic analysis revealed 807 upregulated proteins and 1,186 downregulated proteins in KO mice compared to WT mice. We confirmed the key downregulated proteins by western blotting and immunofluorescence staining in the previous manuscript. These results indicated that IQCH might interact with ribosomal proteins to regulate protein expression. Naturally, the regulation of protein synthesis by IQCH requires further experiments for confirmation in future studies.

Author response image 1.

The interaction between IQCH and ribosomal proteins. Co-IP assays confirmed that IQCH interacted with RPL4, RPS3, and RPS7 in WT mouse sperm.

6) Line 244 The authors mentioned too many GO functions without focus.

Response: Following reviewer’s suggestions, we have simplified IQCH-associated GO functions in the revised manuscript.

7) Figure 6, there are no negative controls in all co-IP experiments. Band sizes are not marked. Thus, all data can't be evaluated. This also raises concern about whether the LC-MS/MS experiment to identify IQCH interacting protein was well-controlled? All co-IP experiments were poorly designed to draw any conclusion.

Response: Thanks to reviewer’s comments. We have supplemented negative controls in all Co-IP experiments and provided band sizes in Figure 6 in revised manuscript.

8) The authors mentioned that IQCH can bind to CaM. But they didn't detect CaM protein in Figure 5. Did the LC-MS/MS experiment really work?

Response: Thanks to reviewer’s comments. We detected the interaction of CaM protein with IQCH in the LC-MS/MS experiment analysis, which has been submitted as new Data S1 in the revised manuscript. We also confirmed their binding in mouse sperm by Co-IP experiment and immunofluorescence staining, which results were shown in Figure 6 and Figure S10 in the previous study.

9) Figure 6D. Because IQCH is lost in Iqch KO sperm, what is the point of showing in the Co-IP assay that CaM does not bind to IQCH in Iqch KO sperm?

Response: Following reviewer’s suggestions, we have deleted the results of Co-IP assay that CaM could not bind to IQCH in Iqch KO sperm.

10) Figure 6E. The Co-IP assay does not support the authors' claim that the decreased expression of HNRPAB was due to the reduced binding of IQCH and CaM by the knockout of IQCH or CaM.

Response: Thanks to reviewer’s expert comments. Indeed, the results of Figure 6E confirmed the interaction of IQCH and CaM in K562 cells, and also showed that the expression of HNRPAB was reduced when IQCH or CaM was knocked down, suggesting that IQCH or CaM might regulate HNRPAB expression. While in Figure 6F, the downregulation of HNRPAB caused by knocking down IQCH (or CaM) cannot be rescued when overexpressed CaM (or IQCH), indicating that CaM (or IQCH) cannot mediate HNRPAB expression alone. Therefore, the reduced expression of HNRPAB in Figure 6E might result from the weakened interaction between IQCH and CaM, but not a superficial downregulation of IQCH or CaM expression. To avoid the confusion, we have modified the relevant description in the revied manuscript.

Reviewer #2 (Recommendations For The Authors):

Major comments:

1) Lines 117 and 129: Please provide the reference number (NM_xxx.x) for the IQCH isoform that was used to interpret this variant. This is key information. Also, please provide the predicted truncation consequence caused by this splicing variant to IQCH protein.

Response: Thanks to reviewer’s suggestions. We have added reference number (NM_0010317152) of IQCH in manuscript. We employed splice site prediction tools, such as SpliceAI, RDDC, and varSEAK, to assess the expression consequences of this IQCH splicing variant. These tools couldn't anticipate the outcome of this splicing variant. However, the results of minigene splicing assay showed that the IQCH c.387+1_387+10del resulted in degradation of IQCH.

2) Figure 1A: The deleted sequence indicated by the red box does not match IQCH c.387+1_387+10del. Please show a plot of the exon-intron boundary under the Sanger sequencing results of the WT allele.

Response: Thanks to reviewer’s suggestions. We are sorry for the use of non-standard descriptions about the results of Sanger sequencing. According to the HGVS nomenclature (Figure R2), we have modified the red box to match IQCH c.387+1_387+10del and have added the exon-intron boundary in Figure 1A accordingly.

Author response image 2.

HGVS nomenclature description of the IQCH variant. The picture showed a detailed HGVS nomenclature description of IQCH c.387+1_387+10del.

Minor comments:

a) Manuscript title: It is suggested to change the title to "IQCH regulates spermatogenesis by interacting with CaM to promote the expression of RNA-binding proteins".

Response: According to reviewer’s suggestions, we have modified the title as “IQCH regulates spermatogenesis by interacting with CaM to promote the expression of RNA-binding proteins”.

b) Line 116: Please introduce the abbreviation WES. Also, please introduce the other abbreviations (such as WT, SEM, TEM, etc.) the first time they appear.

Response: Thanks to reviewer’s suggestions. We have provided the full explanations for all abbreviations upon their initial appearance.

c) Line 140, "Nonfunctional IQCH": Due to "the lack of IQCH expression" in Line 137, should "Nonfunctional IQCH" be changed into "IQCH deficiency"?

Response: Thanks for reviewer’s the detailed review. We have modified this title in Results part of the revised manuscript as followed: “IQCH deficiency leads to sperm with cracked axoneme structures accompanied by defects in the acrosome and mitochondria”

d) The information on the following references is incomplete: Sechi et al., Tian et al., Wang et al., and Xu et al. Please provide issue/page/article numbers.

Response: We are sorry for our oversight. We have provided the missing issue/page/article numbers for the references.

e) The title of Figure 1: Please emphasize that the male infertile-associated variant is "homozygous".

Response: Thanks to reviewer’s suggestions. We have revised the title of Figure 1 to emphasize the homozygous variant as follows: “Identification of a homozygous splicing mutation in IQCH in a consanguineous family with male infertility”.

f) Table 1: Please provide the reference paper for the normal values. Response: We appreciate the reviewer's detailed checks. We have provided the reference paper for the normal values in Table 1.

g) Figure 5F is distorted. Please make sure that it is a perfect circle.

Response: Thanks to reviewer’s suggestions. We have revised both the graphical representation and layout of Figure 5 in revised manuscript to make sure the readability.

Reviewer #3 (Recommendations For The Authors):

While the writing is generally clear, there are multiple examples of where the writing could be improved for clarity.

1) While some terms are defined throughout the manuscript, many abbreviations are not defined upon their first mention, such as WES, RT-PCR, TYH, HTF, KSOM, KEGG, RIPA, PMSE, SDS-PAGE, H&L, and HRP.

Response: Thanks to reviewer’s suggestions. We have provided the full explanations for all abbreviations upon their initial appearance.

2) On line 44, the claim that spermatogenesis is the "most complex biological process" is rather subjective and hard to support with concrete data.

Response: Thanks to reviewer’s suggestions. We have modified this description in the Introduction section as follow: “Spermatogenesis is one of the most complex biological process in male organisms and functions to produce mature spermatozoa from spermatogonia in three phases: (i) spermatocytogenesis (mitosis), (ii) meiosis, and (iii) spermiogenesis.”

3) On line 54, I think the authors meant "heterogeneous," not "heterologous."

Response: Thanks to reviewer’s comment. We have changed “heterologous” into “heterogeneous”.

4) On line 156, I think the authors meant "deficiency," not "deficient."

Response: Thanks to reviewer’s comment. We are sorry to make this mistake. We have made the correction in the revised version of the manuscript.

5) On line 300, K562 cells are mentioned, but neither in the Methods nor the Results are any details about the biological origin of these cells (or rationale for their use other than co-expression of IQCH and CaM) provided.

Response: Thanks to reviewer’s suggestion. K562 cell line is a human leukemia cell line and is enriched in the expression of IQCH and CaM, we thus opted to use this cell line for an easier knockdown of IQCH and CaM. We have supplemented the details about the biological origin of these cells in Method section of revised manuscript.

6) For the Results section describing Figure 6H, it would be nice to provide some explanation of the results of ICHQ overexpression alone relative to control situations and not just relative to the delta-IQ version or relative to simultaneous CaM manipulation.

Response: According to the reviewer’s suggestion, we have supplemented the co-transfection of control and CaM plasmids in HEK293T cells, and the results showed that the expression of HNRPAB in cells co-transfected with control and CaM plasmids was similar to that of co-transfected with IQCH (△IQ) /CaM plasmids, but was lower than that in the cells overexpressing the WT-IQCH and CaM plasmids, confirming the nonfunction of IQCH (△IQ) plasmids. We have shown the results in Figure 6H in the revised manuscript.

7) The sentence on lines 352-354 is confusing.

Response: We apologize for any confusion caused by the sentence in question. We have revisited the sentence and made appropriate revisions to enhance its clarity as follows: “Our findings suggest that the fertilization function is the main action of IQ motif-containing proteins, while each specific IQ motif-containing protein also has its own distinct role in spermatogenesis.”

8) The use of "employee" on line 371 is awkward and not very scientific.

Response: Thanks to reviewer’s comment. We have changed “employee” in to “downstream effector protein” on line 376

Author Response

Thanks to all the reviewers for their insightful and constructive comments, which are very helpful in improving the manuscript. We are encouraged by the many positive comments regarding the significance of our findings and the value of our data. Regarding the reviews’ concern on cell classification, we used several additional marker genes to explain the identification of cell clusters and subclusters. We have further analyzed and rewrote part of the text to address the concerns raised. Here is a point-by-point response to the reviewers’ comments and concerns. Figures R1-R9 were provided only for additional information for reviewers and were not included in the revised manuscript.

Reviewer #1 (Public Review):

In the article "Temporal transcriptomic dynamics in developing macaque neocortex", Xu et al. analyze the cellular composition and transcriptomic profiles of the developing macaque parietal cortex using single-cell RNA sequencing. The authors profiled eight prenatal rhesus macaque brains at five timepoints (E40, E50, E70, E80, and E90) and obtained a total of around 53,000 high-quality cells for downstream analysis. The dataset provides a high-resolution view into the developmental processes of early and mid-fetal macaque cortical development and will potentially be a valuable resource for future comparative studies of primate neurogenesis and neural stem cell fate specification. Their analysis of this dataset focused on the temporal gene expression profiles of outer and ventricular radial glia and utilized pesudotime trajectory analysis to characterize the genes associated with radial glial and neuronal differentiation. The rhesus macaque dataset presented in this study was then integrated with prenatal mouse and human scRNA-seq datasets to probe species differences in ventricular radial glia to intermediate progenitor cell trajectories. Additionally, the expression profile of macaque radial glia across time was compared to those of mouse apical progenitors to identify conserved and divergent expression patterns of transcription factors.

The main findings of this paper corroborate many previously reported and fundamental features of primate neurogenesis: deep layer neurons are generated before upper layer excitatory neurons, the expansion of outer radial glia in the primate lineage, conserved molecular markers of outer radial glia, and the early specification of progenitors. Furthermore, the authors show some interesting divergent features of macaque radial glial gene regulatory networks as compared to mouse. Overall, despite some uncertainties surrounding the clustering and annotations of certain cell types, the manuscript provides a valuable scRNA-seq dataset of early prenatal rhesus macaque brain development. The dynamic expression patterns and trajectory analysis of ventricular and outer radial glia provide valuable data and lists of differentially expressed genes (some consistent with previous studies, others reported for the first time here) for future studies.

The major weaknesses of this study are the inconsistent dissection of the targeted brain region and the loss of more mature excitatory neurons in samples from later developmental timepoint due to the use of single-cell RNA-seq. The authors mention that they could observe ventral progenitors and even midbrain neurons in their analyses. Ventral progenitors should not be present if the authors had properly dissected the parietal cortex. The fact that they obtained even midbrain cells point to an inadequate dissection or poor cell classification. If this is the result of poor classification, it could be easily fixed by using more markers with higher specificity. However, if it is the result of a poor dissection, some of the cells in other clusters could potentially be from midbrain as well. The loss of more mature excitatory neurons is also problematic because on top of hindering the analysis of these neurons in later developmental periods, it also affects the cell proportions the authors use to support some of their claims. The study could also benefit from the validation of some of the genes the authors uncovered to be specifically expressed in different populations of radial glia.

We thank the Reviewer’s comments and apologize for the shortcomings of tissue dissection and cell capture.

We used more marker genes for major cell classification, such as SHOX2, IGFBP5, TAC1, PNYN, FLT1, and CYP1B, in new Figure 1D, to improve the cell type annotation results. We improved the cell type annotation results by fixing cluster 20 from C20 as Ventral LGE-derived interneuron precursor and cluster by the expression of IGFBP5, TAC1, and PDYN; fixing cluster 23 from meningeal cells to thalamus cells by the expression of ZIC2, ZIC4, and SHOX2. These cell types were excluded in the follow-up analysis. Due to EN8 being previously incorrectly defined as midbrain neurons, it resulted in a misunderstanding of the dissection result as a poor dissection. After carefully reviewing the data analysis process, we determined that EN8 was a small group of cells in cluster 23 mistakenly selected during excitatory neuron analysis, as shown in Figure R5(A), which was corrected after revision. In the revised manuscript, we deleted the previous EN8 subcluster and renumbered the rest of the excitatory neuron subclusters in the new Figure 2.

In addition, we also improved the description of sample collection as follows: “We collected eight pregnancy-derived fetal brains of rhesus macaque (Macaca mulatta) at five prenatal developmental stages (E40, E50, E70, E80, E90) and dissected the parietal lobe cortex. Because of the different development times of rhesus monkeys, prenatal cortex size and morphology are different. To ensure that the anatomical sites of each sample are roughly the same, we use the lateral groove as a reference to collect the parietal lobe for single-cell sequencing (as indicated by bright yellow in Figure S1A) and do not make a clear distinction between the different regional parts including primary somatosensory cortex and association cortices in the process of sampling”. As shown in Figure S1A, due to the small volume of the cerebral cortex at early time points, especially in E40, a small number of cells beyond the dorsal parietal lobe, including the ventral cortex cells and thalamus cells, were collected during the sampling process with the brain stereotaxic instrument.

In this study, the BD method was used to capture single cells. Due to the fixed size of the micropores, this method might be less efficient in capturing mature excitatory neurons. However, it has a good capture effect on newborn neurons at each sampling time point so that the generation of excitatory neurons at different developmental time points can be well observed, as shown in Figure 2, which aligns with our research purpose.

To verify the reliability of our cell annotation results, we compared the similarity of cell-type association between our study and recently published research(Micali N, Ma S, Li M, et al. Science. doi:10.1126/science.adf3786.PMID: 37824652), using the scmap package to project major cell types in our macaque development scRNA-seq dataset to GSE226451. The river plot in Author response image 1 illustrates the broadly similar relationships of cell type classification between the two datasets.

Author response image 1.

Riverplot illustrates relationships between datasets in this study and recently published developing macaque telencephalon datasets major cell type annotation.

Furthermore, bioinformatics analysis is used for the validation of genes specifically expressed in outer radial glia. We verified terminal oRG differentiation genes in the recently published macaque telencephalic development dataset(Micali N, Ma S, Li M, et al. Science. doi:10.1126/science.adf3786.PMID: 37824652) (GEO accession: GSE226451). The results of Author response image 2 show that the gene expression showed states/stages. Most of the oRG terminal differentiation markers genes identified in our study were also expressed in the oRG cells of the GSE226451 dataset. In particular, the two datasets were consistent in the expression of ion channel genes ATP1A2, ATP1A2, and SCN4B.

Author response image 2.

Heatmap shows the relative expression of genes displaying significant changes along the pseudotime axis of vRG to oRG from the dataset of Nicola Micali et al.2023(GEO: GSE226451). The columns represent the cells being ordered along the pseudotime axis.

Reviewer #2 (Public Review):

Summary:

This manuscript by Xu et al., is an interesting study aiming to identify novel features of macaque cortical development. This study serves as a valuable atlas of single cell data during macaque neurogenesis, which extends the developmental stages previously explored. Overall, the authors have achieved their aim of collecting a comprehensive dataset of macaque cortical neurogenesis and have identified a few unknown features of macaque development.

Strengths:

The authors have accumulated a robust dataset of developmental time points and have applied a variety of informatic approaches to interrogate this dataset. One interesting finding in this study is the expression of previously unknown receptors on macaque oRG cells. Another novel aspect of this paper is the temporal dissection of neocortical development across species. The identification that the regulome looks quite different, despite similar expression of transcription factors in discrete cell types, is intriguing.

Weaknesses:

Due to the focus on demonstrating the robustness of the dataset, the novel findings in this manuscript are underdeveloped. There is also a lack of experimental validation. This is a particular weakness for newly identified features (like receptors in oRG cells). It's important to show expression in relevant cell types and, if possible, perform functional perturbations on these cell types. The presentation of the data highlighting novel findings could also be clarified at higher resolution, and dissected through additional informatic analyses. Additionally, the presentation of ideas and goals of this manuscript should be further clarified. A major gap in the study rationale and results is that the data was collected exclusively in the parietal lobe, yet the rationale and interpretation of what this data indicates about this specific cortical area was not discussed. Last, a few textual errors about neural development are also present and need to be corrected.

We thank you for your comments and suggestions concerning our manuscript. The comments and suggestions are all valuable and helpful for revising and improving our paper and the essential guiding significance to our research. We have studied the comments carefully and made corrections, which we hope to meet with approval. We have endeavored to address the multiple points raised by the referee.

To support the reliability of our data and newly identified features, we verified terminal oRG differentiation genes in the recently published macaque telencephalic development dataset(Micali N, Ma S, Li M, et al. Science. doi:10.1126/science.adf3786.PMID: 37824652) (GEO accession: GSE226451). The results of Figure R2 show that the gene expression showed states/stages. Most of the oRG terminal differentiation markers genes identified in our study were also expressed in the oRG cells of the GSE226451 dataset. In particular, the two datasets were consistent in the expression of ion channel genes ATP1A2, ATP1A2, and SCN4B.

Our research results mainly explore the conserved features of neocortex development across species. By comparing evolution, we found the types of neural stem cells in the intermediate state, their generative trajectories, and gene expression dynamics accompanying cell trajectories. We further explored the stages of transcriptional dynamics during vRG generating oRG. More analysis was performed through transcriptional factor regulatory network analysis. We performed the TFs regulation network analysis of human vRG with pyscenic workflow. The top transcription factors of every time point in human vRG were calculated, and we used the top 10 TFs and their top 5 target genes to perform interaction analysis and generate the regulation network of human vRG in revised figure 6. In comparison of the pyscenic results of mouse, macaque and human vRG, it was obvious that the regulatory networks were not evolutionarily conservative. Compared with macaque, the regulatory network of transcription factors and target genes in humans is more complex. Some conserved regulatory relationships present in more than one species are identified, such as HMGN3, EMX2, SOX2, and HMGA2 network at an early stage when deep lager generation and SOX10, ZNF672, ZNF672 network at a late stage when upper-layer generation.

Although the parietal lobe is the center of the somatic senses and is significant for interpreting words as well as language understanding and processing. In this study, the parietal lobe area was selected mainly because of the convenience of sampling the dorsal neocortex. As we described in the Materials and Methods section as follows: “Because of the different development times of rhesus monkeys, prenatal cortex size and morphology are different. To ensure that the anatomical sites of each sample are roughly the same, we use the lateral groove as a reference to collect the parietal lobe for single-cell sequencing (as indicated by bright yellow in Figure S1A) and do not make a clear distinction between the different regional parts including primary somatosensory cortex and association cortices in the process of sampling”.

Thanks for carefully pointing out our manuscript's textual errors about neural development. We have corrected them which were descripted in the following response.

Reviewer #3 (Public Review):

Summary: The study adds to the existing data that have established that cortical development in rhesus macaque is known to recapitulate multiple facets cortical development in humans. The authors generate and analyze single cell transcriptomic data from the timecourse of embryonic neurogenesis.

Strengths:

Studies of primate developmental biology are hindered by the limited availability and limit replication. In this regard, a new dataset is useful.

The study analyzes parietal cortex, while previous studies focused on frontal and motor cortex. This may be the first analysis of macaque parietal cortex and, as such, may provide important insights into arealization, which the authors have not addressed.

Weaknesses:

The number of cells in the analysis is lower than recent published studies which may limit cell representation and potentially the discovery of subtle changes.

The macaque parietal cortex data is compared to human and mouse pre-frontal cortex. See data from PMCID: PMC8494648 that provides a better comparison.

A deeper assessment of these data in the context of existing studies would help others appreciate the significance of the work.

We thank the reviewer for these suggestions and constructive comments. We agree with the reviewer that the cell number in our study is lower than in recently published studies. The scRNA sequencing in this study was completed between 2018 and 2019, the early stages of the single-cell sequencing technology application. Besides, we have been unable to get extra macaque embryos to enlarge the sample numbers recently since rhesus monkey samples are scarce. Therefore, the number of cells in our study is relatively small compared to recently published single-cell studies.

The dataset suggested by the reviewers is extremely valuable, and we tried to perform analysis as the reviewer suggested to explore temporal expression patterns in different species of parietal cortex. The dataset from PMCID: PMC8494648 provides the developing human brain across regions from gestation week (GW)14 to gestation week (GW)25. Since this data set only covers the middle and late stages of embryonic neurogenesis, it did not fully match the developmental time points of our study for integration analysis. However, we quoted the results of this study in the discussion section.

The human regulation analysis with pyscenic workflow was added into new figure 6 for the comparison of different species vRG regulatory network. Compared with macaque, the regulatory network of transcription factors and target genes in humans is more complex. Some conserved regulatory relationships present in more than one species are identified, such as HMGN3, EMX2, SOX2, and HMGA2 network at an early stage when deep lager generation and SOX10, ZNF672, ZNF672 network at a late stage when upper-layer generation.

Besides, we performed additional integration analysis of our dataset with the recently published macaque neocortex development datase (GEO accession: GSE226451) to verify the reliability of our cell annotation results and terminal oRG differentiation genes. The river plot in Figure R1 illustrates the broadly similar relationships of cell type classification between the two datasets. The result in Figure R2 showed that most of the oRG terminal differentiation markers genes identified in our study were also expressed in the oRG cells of the GSE226451 dataset. In particular, the two datasets were consistent in the expression of ion channel genes ATP1A2, ATP1A2, and SCN4B.

Reviewer #1 (Recommendations For The Authors):

1) Throughout the manuscript, the term "embryonic" or "embryogenesis" is used in reference to all timepoints (E40-E90) in this study. The embryonic period is a morphologically and anatomically defined developmental period that ends ~E48-E50 in rhesus macaque. Prenatal or developing is a more accurate term when discussing all timepoints of this study.

We thank the reviewer for pointing out this terminology that needs to be clarified. We have now replaced “embryonic” with “prenatal” as a more appropriate description for the sampling time points in the manuscript.

2) Drosophila should be italicized in the introduction.

Thanks for suggesting that we have set the “Drosophila” words to italics in the manuscript.

3) Introduction - "In rodents, radial glia are found in the ventricular zone (VZ), where they undergo proliferation and differentiation." This sentence implies that only within rodents are radial glia found within the ventricular zone. Radial glia are present within the ventricular zone of all mammals.

Thanks for careful reading. This sentence has been corrected “In mammals, radial glial cells are found in the ventricular zone (VZ), where they undergo proliferation and differentiation.”

4) Figure 1A - an image of the E40 brain is missing.

We first sampled the prenatal developmental cortex of rhesus monkeys at the E40 timepoint. Unfortunately, we forgot to save the photo of the sampling at the E40 time point.

5) Figure 1B and 1C - it is unclear why cluster 20 is not annotated in Figure 1 as in the text it is stated "Each of the 28 identified clusters could be assigned to a cell type identity..." This cluster expresses VIM and PAX6 suggestive of ventricular radial glia and is located topographically approximate to IPC cluster 8 and seems to bridge the gap between neural stem cells and the interneuron clusters. Additionally, cluster 20 appears to be subclustered by itself in the progenitor subcluster UMAP (Figure 3A) suggestive of a batch effect or cells with low quality. The investigation, quality control, and proper annotation of this cluster 20 is necessary.

We appreciate for the reviewer’s suggestion. We detected specific expression marker genes of cluster 20, cells in this cluster specifically expressed VIM, IGFBP5 and TAC. According to the cell annotation results from a published study, we relabeled cluster 20 as ventral LGE-derived interneuron precursors (Yu, Yuan et al. Nat Neurosci. 2021. doi:10.1038/s41593-021-00940-3. PMID: 34737447.). Cluster 20 cells have been deleted in the new Figure 3A.

6) Figure 1B UMAP - it is unexpected that meningeal cells would cluster topographically closer to the excitatory neuron cluster (one could even argue that the meningeal cell cluster is located within the excitatory neuron clusters) instead of next to or with the endothelial cell clusters. This is suspicious for a mis-annotated cell cluster. ZIC2 and ZIC3 were used as the principal marker genes for meningeal cells. However, these genes are not specific for meninges (PanglaoDB) and had not been identified as marker genes in a developmental sc-RNAseq dataset of the developing mouse meninges (DeSisto et al. 2020). Additional marker genes (COL1A1, COL1A2, CEMIP, CYP1B1, SLC13A3) may be helpful to delineate the identity of this cluster and provide more evidence for a meningeal origin.

We thank the reviewer for the constructive advice. The violin plot in Author response image 3 has checked additional marker genes, including COL1A1, COL1A2, CEMIP, and CYP1B2. Cluster 23 does not express these marker genes but specifically expresses thalamus marker genes SHOX2(Rosin, Jessica M et al. Dev Biol. 2015. doi:10.1016/j.ydbio.2014.12.013. PMID: 25528224.) and TCF7L2(Lipiec, Marcin Andrzej et al. Development. 2020. doi: 10.1242/dev.190181. PMID: 32675279). According to the gene expression results, we corrected the cell definition of cluster 23 to thalamic cells in the revised manuscript. Specifically, we added marker genes SHOX2 and CYP1B1 in the new Figure 1D violin plot and corrected the cell definition of cluster23 from meninges to thalamus cells in the revised manuscript and figures.

Author response image 3.

Vlnplot of additional markers in cluster 23.

7) From Figure 1A, it appears that astrocytes (cluster 13) are present at E40 and E50 timepoints. This is inconsistent with literature and experimental data of the timing of the neuron-glia switch in primates and inconsistent with the claim within the text that, "Collectively, these results suggested that cortical neural progenitors undergo neurogenesis processes during the early stages of macaque embryonic cortical development, while gliogenic differentiation... occurs in later stages." The clarification of the percentage of astrocytes at each timepoint would clarify this point.

According to the suggestion, we have statistically analyzed the percentage of astrocytes (cluster 13) at each time point. The statistical results showed that the proportion of astrocytes was low to 0.1783% and 0.1046% at E40 and E50 time points, and increased significantly at E80 and E90, suggesting the onset of macaque gliogenesis might be around embryonic 80 days to 90 days. The result was consistent with published research on the timing of the neuron-glial transition in primates (Rash, Brian G et al. Proc Natl Acad Sci U S A. 2019. doi:10.1073/pnas.1822169116. PMID: 30894491). Besides, we thought that the cells in cluster 13 captured at E40 to E50 time points, with a total number of less than 200, maybe astrocyte precursor cells expressing the AQP4 gene (Yang, Lin, et al. Neuroscience bulletin. 2022. doi:10.1007/s12264-021-00759-9. PMID: 34374948).

8) A subcluster of ExN neurons was identified and determined to be of midbrain origin based on expression of TCF7L2. Did this subcluster express other known markers of the developing midbrain (OTX2, LMX1A, NR4A2, etc...)? Additionally, does this subcluster suggest that the limits of the dissection extended to the midbrain in samples E40 and E50?

We apologize for the previous inadequacy of the excitatory neuron cell annotation. In the description of the previous version of the manuscript, we misidentified the cells of the EN8 as midbrain cells. Following the reviewer’s suggestion, we verified the expression of more tissue- specific marker genes of EN8. As the violin diagram in Author response image 4 shows, other developing midbrain markers OTX2, NR4A2, and PAX7 did not express in EN8, but thalamus marker genes SHOX2, TCF7L2, and NTNG1 were highly expressed in EN8. Besides, dorsal cortex excitatory neuron markers NEUROD2, NEUROD6, and EMX1 were not expressed in EN8, which suggests that EN8 might not belong to cortical cells. After carefully reviewing the data analysis process, we determined that EN8 was a small group of cells in cluster 23 mistakenly selected during excitatory neuron analysis, as shown in Figure R5(A), which was corrected after revision. In the revised manuscript, we have removed EN8 from the analysis of excitatory neurons. In the revised manuscript, we have deleted the previous EN8 subcluster and renumbered the left excitatory neuron subclusters in new Figure 2 and Figure S3.

Author response image 4.

(A). Modified diagram of clustering of excitatory neuron subclusters collected at all time points, visualized via UMAP related to Figure 2A. (B) Vlnplot of different marker genes in EN8.

9) "These data suggested that the cell fate determination by diverse neural progenitors occurs in the embryonic stages of macaque cortical development and is controlled by several key transcriptional regulators" The authors present a list of differentially expressed genes specific to the various radial glia clusters along pseudotime. Some of these radial glia DEGs are known and have been characterized by previous literature while other DEGs they have identified had not been previously shown to be associated with radial glia specification/maturation. However, this list of DEGs does not support the claim that cell fate determination is controlled by several key transcriptional regulators. What were the transcriptional regulators of radial glia specification identified in this study and how were they validated?

We agree with the reviewer and honestly admit that the description of this part in the previous manuscript is inaccurate. The description has been deleted in the revised manuscrip.

10) "Comparing vRG to IPC trajectory between human, macaque, and mouse, we found this biological process of vRG-to-IPC is very conserved across species, but the vRG to oRG trajectory is divergent between species. The latter process is almost invisible in mice, but it is very similar in primates and macaque." Firstly, macaques are primates, and the text should be updated to reflect this. Secondly, from Figure 5C., it seems there were no outer radial glia detected at all within the vRG-oRG and vRG-IPC developmental trajectories. This would imply that oRGs are not "almost invisible" in mice, but rather do not exist. The authors need to clarify the presence or absence of identifiable outer radial glia in the integrated dataset and relate the relative abundance of these cells to their interpretation of the developmental trajectories for each species.

We apologize for the description inaccuracies in the manuscript and thank the reviewer for pointing out the expression errors. At your two suggestions, the description has been corrected in the revised manuscript as "Comparing vRG to IPC trajectory between human, macaque, and mouse, we found this biological process of vRG-to-IPC is very conserved across species. However, the vRG to oRG trajectory is divergent between species because the oRG population was not identified in the mouse dataset. The latter process is almost invisible in mice but similar in humans and macaques".

Although several published research has shown that oRG-like progenitor cells were present in the mouse embryonic neocortex(Wang, Xiaoqun et al. Nature neuroscience.2011. doi:10.1038/nn.2807; Vaid, Samir et al. Development. 2018, doi:10.1242/dev.169276. PMID: 30266827). However, oRG cells were barely detected in the scRNA-seq dataset of mice cortical development studies(Ruan, Xiangbin et al. Proc Natl Acad Sci U S A. 2021. doi:10.1073/pnas.2018866118. PMID: 33649223; Di Bella, Daniela J et al. Nature. 2021. doi:10.1038/s41586-021-03670-5. PMID: 34163074; Chen, Ao et al. Cell. 2022. doi:10.1016/j.cell.2022.04.003. PMID: 35512705). There were no oRG populations detected in the mouse embryonic cortical development dataset (GEO: GSE153164) used for integration analysis in our study.

11) "Ventral radial glia cells generate excitatory neurons by direct and indirect neurogenesis" This should be corrected to dorsal radial glia cells as this paper is discussing radial glia of the dorsal pallium.

13) Editorially, gene names need to be italicized in the text, figures, and figure legends.

14) Figure 5B - a scale bar showing the scale of the relative expression denoted by the dark blue color would be beneficial.

15) Figure S7D is mislabeled in the figure legend.

Merged response to points 11 to 15: Thank you for kindly pointing out the errors in our manuscript. We have corrected the above four points in the revised version.

Reviewer #2 (Recommendations For The Authors):

Specific suggestions for authors:

In the abstract the authors state: "thicker upper-layer neurons". I think it's important to be clear in the language by stating either that the layers are thicker or the neurons are most dense.

Thanks for your good comments. The description of “thicker upper-layer neurons” was corrected to “the thicker supragranular layer” in the revised manuscript. The supragranular layer thickness in primates was much higher than in rodents, both in absolute thickness and in proportion to the thickness of the whole neocortex (Hutsler, Jeffrey J et al. Brain research. 2005. doi:10.1016/j.brainres.2005.06.015. PMID: 16018988). Here, we want to describe the supragranular layer of primates as significantly higher than that of rodents, both in absolute thickness and in proportion to the thickness of the whole neocortex.

The introduction needs additional clarification regarding the vRG vs oRG discussion. I was unclear what the main takeaway for readers should be. Similarly, the discussion of previous studies and the importance for comparing human and macaque could be clarified.

We appreciate the suggestion and apologize for the shortcomings of the introduction part. We have rewritten the section and added additional clarification in the revised introduction. In the revised manuscript, the contents of the introduction are as follows:

“The neocortex is the center for higher brain functions, such as perception and decision-making. Therefore, the dissection of its developmental processes can be informative of the mechanisms responsible for these functions. Several studies have advanced our understanding of the neocortical development principles in different species, especially in mice. Generally, the dorsal neocortex can be anatomically divided into six layers of cells occupied by distinct neuronal cell types. The deep- layer neurons project to the thalamus (layer VI neurons) and subcortical areas (layer V neurons), while neurons occupying more superficial layers (upper-layer neurons) preferentially form intracortical projections1. The generation of distinct excitatory neuron cell types follows a temporal pattern in which early-born neurons migrate to deep layers (i.e., layers V and VI), while the later- born neurons migrate and surpass early-born neurons to occupy the upper layers (layers II-IV) 2. In Drosophila, several transcription factors are sequentially explicitly expressed in neural stem cells to control the specification of daughter neuron fates, while very few such transcription factors have been identified in mammals thus far. Using single-cell RNA sequencing (scRNA-seq), Telley and colleagues found that daughter neurons exhibit the same transcriptional profiles of their respective progenitor radial glia, although these apparently heritable expression patterns fade as neurons mature3. However, the temporal expression profiles of neural stem cells and the contribution of these specific temporal expression patterns in determining neuronal fate have yet to be wholly clarified in humans and non-human primates. Over the years, non-human primates (NHP) have been widely used in neuroscience research as mesoscale models of the human brain. Therefore, exploring the similarities and differences between NHP and human cortical neurogenesis could provide valuable insight into unique features during human neocortex development.

In mammals, radial glial cells are found in the ventricular zone (VZ), where they undergo proliferation and differentiation. The neocortex of primates exhibits an extra neurogenesis zone known as the outer subventricular zone (OSVZ), which is not present in rodents. As a result of evolution, the diversity of higher mammal cortical radial glia populations increases. Although ventricular radial glia (vRG) is also found in humans and non-human primates, the vast majority of radial glia in these higher species occupy the outer subventricular zone (OSVZ) and are therefore termed outer radial glia (oRG). Outer radial glial (oRG) cells retain basal processes but lack apical junctions 4 and divide in a process known as mitotic somal translocation, which differs from vRG 5. VRG and oRG are both accompanied by the expression of stem cell markers such as PAX6 and exhibit extensive self-renewal and proliferative capacities 6. However, despite functional similarities, they have distinct molecular phenotypes. Previous scRNA-seq analyses have identified several molecular markers, including HOPX for oRGs, CRYAB, and FBXO32 for vRGs7. Furthermore, oRGs are derived from vRGs, and vRGs exhibit obvious differences in numerous cell-extrinsic mechanisms, including activation of the FGF-MAPK cascade, SHH, PTEN/AKT, and PDGF pathways, and oxygen (O2) levels. These pathways and factors involve three broad cellular processes: vRG maintenance, spindle orientation, and cell adhesion/extracellular matrix production8.

Some transcription factors have been shown to participate in vRG generation, such as INSM and TRNP1. Moreover, the cell-intrinsic patterns of transcriptional regulation responsible for generating oRGs have not been characterized.

ScRNA-seq is a powerful tool for investigating developmental trajectories, defining cellular heterogeneity, and identifying novel cell subgroups9. Several groups have sampled prenatal mouse neocortex tissue for scRNA-seq 10,11, as well as discrete, discontinuous prenatal developmental stages in human and non-human primates 7,12 13,14. The diversity and features of primate cortical progenitors have been explored 4,6,7,15. The temporally divergent regulatory mechanisms that govern cortical neuronal diversification at the early postmitotic stage have also been focused on 16. Studies spanning the full embryonic neurogenic stage in the neocortex of humans and other primates are still lacking. Rhesus macaque and humans share multiple aspects of neurogenesis, and more importantly, the rhesus monkey and human brains share more similar gene expression patterns than the brains of mice and humans17-19. To establish a comprehensive, global picture of the neurogenic processes in the rhesus macaque neocortex, which can be informative of neocortex evolution in humans, we sampled neocortical tissue at five developmental stages (E40, E50, E70, E80, and E90) in rhesus macaque embryos, spanning the full neurogenesis period. Through strict quality control, cell type annotation, and lineage trajectory inference, we identified two broad transcriptomic programs responsible for the differentiation of deep-layer and upper-layer neurons. We also defined the temporal expression patterns of neural stem cells, including oRGs, vRGs, and IPs, and identified novel transcription factors involved in oRG generation. These findings can substantially enhance our understanding of neocortical development and evolution in primates.”

Why is this study focused on the parietal lobe? This should be discussed in the introduction and interpretation of the data should be contextualized in the context of this cortical area.

In this study, samples were collected from the parietal lobe area mainly for the following reasons:

(1) To ensure that the cortical anatomical parts collected at each time point are consistent, we used the lateral cerebral sulcus as a marker to collect the parietal lobe tissue above the lateral sulcus for single-cell sequencing sample collection. Besides, the parietal region is also convenient for sampling the dorsal cortex.

(2) Previous studies have made the timeline of the macaque parietal lobe formation process during the prenatal development stage clear （ Finlay, B L, and R B Darlington.Science.1995. doi:10.1126/science.7777856. PMID: 7777856）, which is also an essential reason for using the parietal lobe as the research object.

Figure 1:

Difficult to appreciate how single cell expression reflects the characterization of layers described in Figure 1A. A schematic for temporal development would be helpful. Also, how clusters correspond to discrete populations of excitatory neurons and progenitors would improve figure clarity. Perhaps enlarge and annotate the UMAPS on the bottom of Figure 1A.

We thank the reviewer for the suggestion and apologize for that Figure 1A does not convey the relationship between single-cell expression and neocortex layer formation. In the revised manuscript, time points information associated with the hierarchy is labeled to the diagram in Figure S1A. The UMAPS on the bottom of Figure 1A was enlarged in the revised manuscript as new Figure 1C.

Labels on top of clusters for 1A/1B would be helpful as it's difficult to see which colors the numbers correspond to on the actual UMAP.

Many thanks to the reviewer for carefully reading and helpful suggestions. We have adjusted the visualization of UMAP in the revised vision. The numbers in the label bar of Figure 1B have been moved to the side of the dot so that the dot can be seen more clearly.

Microglia and meninges are also non-neural cells. This needs to be changed in the discussion of the results.

Thanks for the suggestion. We have fixed the manuscript as the reviewer suggested. The description in the revised manuscript has been fixed as follows: “According to the expression of the marker genes, we assigned clusters to cell type identities of neurocytes (including radial glia (RG), outer radial glia (oRG), intermediate progenitor cells (IPCs), ventral precursor cells (VP), excitatory neurons (EN), inhibitory neurons (IN), oligodendrocyte progenitor cells (OPC), oligodendrocytes, astrocytes, ventral LGE-derived interneuron precursors and Cajal-Retzius cells, or non-neuronal cell types (including microglia, endothelial, meninge/VALC(vascular cell)/pericyte, and blood cells). Based on the expression of the marker gene, cluster 23 was identified as thalamic cells, which are small numbers of non-cortical cells captured in the sample collection at earlier time points. Each cell cluster was composed of multiple embryo samples, and the samples from similar stages generally harbored similar distributions of cell types.”.

It's important to define the onset of gliogenesis in the text and figure. What panels/ages show this?

We identified the onset of gliogenesis by statistically analyzing the percentage of astrocytes (cluster 13) at each time point and added the result in Figure S1. The statistical results showed that the proportion of astrocytes was deficient at E40 and E50 time points and increased significantly at E80 and E90, suggesting the onset of macaque gliogenesis might be around embryonic 80 days to 90 days. The result was consistent with published research on the timing of the neuron-glial transition in primates (Rash, Brian G et al. Proceedings of the National Academy of Sciences of the United States of America 201. doi:10.1073/pnas.1822169116. PMID: 30894491).

Figure 2:

Why are there so few neurons at E90? Is it capture bias, dissociation challenges (as postulated for certain neuronal subtypes in the discussion), or programmed cell death at this time point?

We thought it was because mature neurons at E90 with abundant axons and processes were hard to settle into micropores of the BD method for single cell capture. Due to the fixed size of the BD Rhapsody microwells, this sing-cell capture method might be less efficient in capturing mature excitatory neurons but has a good capture effect on newborn neurons at each sampling time point. In conclusion, based on the BD cell capture method feature, the immature neurons at each point are more easily captured than mature neurons in our study, so the generation of excitatory neurons at different developmental time points can be well observed, as shown in Figure 2, which aligns with our research purpose.

The authors state: "We then characterized temporal changes in the composition of each EN subcluster. While the EN 5 and EN 11 (deep-layer neurons) subclusters emerged at E40 and E50 and disappeared in later stages, EN subclusters 1, 2, 3, and 4 gradually increased in population size from E50 to E80 (Figure 2D)." What about EN7? It's labeled as an upper layer neuron that is proportionally highest at E40. Could this be an interesting, novel finding? Does this indicate something unique about macaque corticogenesis? The authors don't describe/discuss this cell type at all.

We apologize for the manuscript’s lack of detailed descriptions of EN results. In our study, EN7 is identified as CUX1-positive, PBX3-positive, and ZFHX3-positive excitatory neuron subcluster. The results of Fig. 2B show that EN7 was mainly captured from the early time points (E40/E50) samples. Above description was added in the revised manuscript.

The Pbx/Zfhx3-positive excitatory neuron subtype reported in Moreau et al. study on mouse neocortex development progress （ Moreau, Matthieu X et al. Development. 2021. doi:10.1242/dev.197962. PMID: 34170322）. Our study verified that the Pbx3/Zfhx3-positive cortical excitatory neurons also exist in the early stage of prenatal macaque cortex development.

Is there any unique gene expression in identified subtypes that are surprising? Did the comparison against human data, in later figures, inform any unique features of gene expression?

Based on the excitatory neuron subclusters analysis result in our study, we found no astonishing results in excitatory neuron subclusters. In subsequent integrated cross-species analyses, macaque excitatory neurons showed similar transcriptional characteristics to human excitatory neurons. In general, excitatory neurons tend to have a greater diversity in the cortex of animals that are more advanced in evolution (Ma, Shaojie et al. Science. 2022. doi:10.1126/science.abo7257. PMID: 36007006; Wei, Jia-Ru et al. Nat Commun. 2022. doi:10.1038/s41467-022-34590-1. PMID: 36371428; Galakhova, A A et al. Trends Cogn Sci. 2022. doi:10.1016/j.tics.2022.08.012. PMID: 36117080; Berg, Jim et al. Nature. 2021. doi:10.1038/s41586-021-03813-8. PMID: 34616067). Since only single-cell transcriptome data was analyzed in this study, we did not find any unique features of the prenatal developing macaque cortex excitatory neurons in the comparison against the human dataset due to the limitation of information dimension.

Figure 3:

The identification of terminal oRG differentiation genes is interesting. The confirmation of known gene expression as well as novel markers that indicate different states/stages of oRG cells is a valuable resource. As the identification of described ion channel expression is a novel finding, it should be explored more and would be strengthened by validation in tissue samples and, if possible, functional assays.

E is the most novel part of this figure, but it's very hard to read. I think increasing the focus of this figure onto this finding and parsing these results more would be informative.

Thanks for the positive comments. We apologize for the lack of clarity and conciseness in figure visualizations. We hypothesized vRG to oRG cell trajectories into three phases: onset, commitment, and terminal. The leading information conveyed by Figure 3E was the dynamic gene expression along the developmental trajectory from vRG to oRG. Specific genes were selected and shown in the schema diagram of new Figure 3.

We verified terminal oRG differentiation genes in the recently published macaque telencephalic development dataset(Micali N, Ma S, Li M, et al. Science. doi:10.1126/science.adf3786.PMID: 37824652) (GEO accession: GSE226451). The results of Author response image 2 show that the gene expression showed states/stages. Most of the oRG terminal differentiation markers genes identified in our study were also expressed in the oRG cells of the GSE226451 dataset. In particular, the two datasets were consistent in the expression of ion channel genes ATP1A2, ATP1A2, and SCN4B.

I'm curious about the granularity of the oRG_C12 terminal cluster. Are there ways to subdivide the different cells that seem to be glial-committed vs actively dividing vs neurogenically committed to IPCs? In the text, the authors referred to different oRG populations, but they are annotated as the same cluster and cell type. The authors should clarify this.

According to the reviewer's suggestion, we subdivide the oRG_C12 into eight subclusters. Based on the marker gene in Author response image 5C, subclusters 1,2 and 4 might be glial- committed with AQP4/S100B positive expression; subclusters 3,6,7 might be neurogenically committed to IPCs with NEUROD6 positive expression; subclusters 0,3,5,6,7 might be actively dividing state with MKI67/TOP2A positive expression.

Author response image 5.

Subdivide analysis of oRG_C12. (A)and (B) Subdividing of e oRG_C12 visualized via UMAP. Cells are colored according to subcluster timepoint (A) and subcluster identities (B). (C) Violin plot of molecular markers for the subclusters.

Figure 4:

Annotating/labeling the various EN clusters (even as deep/upper) would help improve the clarity of this and other figures. It's clear what each progenitor subtype is but it's hard to read the transitions. Why are all the EN groups in pink/red? It makes the data challenging to interpret.

In Figure4A, we use different yellow/orange colors for deep-layer excitatory neuron subclusters (EN5 and EN10), and different red/pink colors for upper-layer excitatory neuron subclusters (EN1, EN2, EN3, EN4, EN6, EN7, EN8 and EN9). We add the above information in the legend of Figure 4 in the revised manuscript.

E50 seems to be unique - what's EN11?

Based on the molecular markers for EN subclusters in Author response image 2, we recognized EN11 as a deep-layer excitatory neuron subcluster expressing BCL11B and FEZF2. As explained in the above reply, the microplate of BD has a good effect on capturing newborn neurons at each time point. The EN11 was mainly a newborn excitatory neuron at the E50 timepoint, which makes the subcluster seem unique.

Author response image 6.

Vlnplot of different markers in EN8.

Figure 4E - the specificity of gene expression for deep vs upper layer markers seems to be over stated given the visualized gene expression pattern (ex FEZF2). Could the right hand panels be increased to better appreciate the data and confirm the specificity, as described.

In our study, we used slingshot method to infer cell lineages and pseudotimes, which have been used to identifying biological signal for different branching trajectories in many scRNA- seq studies. We apologize for the lack of visualization clarity in the figure 4E. Due to the size limitation of the uploaded file, the file was compressed, resulting in a decrease in the clarity of the image. Below, we provided figure 4E with a higher definition and increased several genes’ slingshot branching tree results according to the reviewer's suggestion.

Figure 5:

There are some grammatical typos at the bottom of page 8. In this section, it also feels like there is a missing logical step between expansion of progenitors through elongated developmental windows that impact long-term expansion of the upper cortical layers.

We apologize for the grammatical typos and have corrected them in the revised manuscript. We understand the reviewer’s concern. Primates have much longer gestation than rodents, and previous study evidence had shown that extending neurogenesis by transplanting mouse embryos to a rat mother increases explicitly the number of upper-layer cortical neurons, with concomitant abundant neurogenic progenitors in the subventricular zone(Stepien, Barbara K et al. Curr Biol. 2020. doi:10.1016/j.cub.2020.08.046. PMID: 32888487). We thought this mechanism could also explain primates' much more expanded abundance of upper-layer neurons.

I'm curious about the IPCs that arise from the oRGs. Lineage trajectory shows vRG decision to oRG or IPC, but oRGs also differentiate into IPCs. Could the authors conjecture why they are not in this dataset or are indistinguishable from vRG-derived IPCs.

Several published experiments have proved that oRG can generate IPC in human and macaque developing neocortex. (Hansen, David V et al. Nature. 2010. doi:10.1038/nature08845. PMID: 20154730; Betizeau, Marion et al. Neuron. 2013. doi:10.1016/j.neuron.2013.09.032. PMID: 24139044). Clearly identifying the difference between IPC generated from vRG and oRG at the transcriptional level in our single-cell transcriptome dataset is difficult. We hypothesized that the IPCs produced by both pathways have highly similar transcriptional features. Due to the limit of the scRNA data analysis algorithm used in this study, we didn’t distinguish the two kinds of IPC, which could not be in terms of pseudo-time trajectory reconstruction and transcriptional data.

Figure 6 :

How are the types 1-5 in 6A defined? Were they defined in one species and then applied across the others?

We applied the same analysis to each species. We first picked up vRG cells in each species dataset and screened the differentially expressed genes (DEGs) between adjacent development time points using the “FindMarkers” function (with min. pct = 0.25, logfc. threshold = 0.25). After separate normalization of the DEG expression matrix from different species datasets, we use the “standardise” function from the Mfuzz package to standardize the data. The DEGs of vRG in each species were grouped into five clusters using the Mfuzz package in R with fuzzy c- means algorithm.

The temporal dynamics in the highlighted section in B have interesting, consistent patterns of gene expression of the genes described, but what about the genes below that appear less consistent temporally? What processes do not appear to be conserved, given those gene expression differences?

Many thanks for the constructive comments. The genes in Figure 6B below are temporal dynamics non-conserved transcription factors among the three species vRG. We performed a functional enrichment analysis on the temporal dynamics of non-conserved transcription factors with the PANTHER (Protein ANalysis THrough Evolutionary Relationships) Classification System(https://www.pantherdb.org/), and the analysis results are shown in Author response image 7. The gene ontology (GO) analysis results show that unconserved transcription factors were related to different biological processes, cellular components, and molecular functions. However, subsequent experiments are still needed to verify specific genes.

Author response image 7.

Gene Ontology (GO) analysis of unconserved temporal patterns transcription factors among mouse, macaque and human vRG cells.

The identification of distinct regulation of gene networks, despite conservation of transcription factors in discrete cell types, is interesting. What does the comparison between humans and macaques indicate about regulatory differences evolutionarily?

We appreciate the reviewer for the comments. We performed the TFs regulation network analysis of human vRG with pyscenic workflow. The top transcription factors of every time point in human vRG were calculated, and we used the top 10 TFs and their top 5 target genes to perform interaction analysis and generate the regulation network of human vRG in revised figure 6. In comparison of the pyscenic results of mouse, macaque and human vRG, it was obvious that the regulatory networks were not evolutionarily conservative. Compared with macaque, the regulatory network of transcription factors and target genes in humans is more complex. Some conserved regulatory relationships present in more than one species are identified, such as HMGN3, EMX2, SOX2, and HMGA2 network at an early stage when deep lager generation and SOX10, ZNF672, ZNF672 network at a late stage when upper-layer generation.

Reviewer #3 (Recommendations For The Authors):

The data should be compared to a similar brain region in human and mouse, if available. (See data from PMCID: PMC8494648).

We appreciate the reviewer’s suggestions. In Figure 6, the species-integration analysis, the mouse data were from the perspective of the somatosensory cortex, macaque data were mainly from the parietal lobe in this study, and human data including the frontal lobe (FL), parietal lobe (PL), occipital lobe (OL), and temporal lobe (TL). PMC8494648 offered high-quality data covering the period of gestation week 14 to gestation week 25. However, our study's development stage of rhesus monkeys is E40-E90 days, corresponding to pcw8-pcw21 in humans. The quality of data from PMC8494648 is particularly good. However, the developmental processes covered by PMC8494648 don’t perfectly match the development time of the macaque cortex that we focused on in this study. Therefore, it is challenging to integrate the dataset (PMCID: PMC8494648) into the data analysis part. However, we have cited the results of this precious research (PMCID: PMC8494648) in the discussion part of the revised manuscript.

A deeper assessment of these data in the context of existing studies would help distinguish the work and enable others to appreciate the significance of the work.

We appreciate the reviewer’s constructive suggestions. The human regulation analysis with pyscenic workflow was added into new figure 6 for the comparison of different species vRG regulatory network. Analysis of the regulatory activity of human, macaque and mouse prenatal neocortical neurogenesis indicated that despite commonalities in the roles of classical developmental TFs such as GATA1, SOX2, HMGN3, TCF7L1, ZFX, EMX2, SOX10, NEUROG1, NEUROD1 and POU3F1. The top 10 TFs of the human, macaque, and mouse vRG each time point and their top 5 target genes identified by pySCENIC as an input to construct the transcriptional regulation network (Figure 6 D, F and H). Some conserved regulatory TFs present in more than one species are identified, such as HMGN3, EMX2, SOX2, and HMGA2 at an early stage when deep- lager generation and SOX10, ZNF672, and ZNF672 at a late stage when upper-lay generation.

Besides, we performed some comparative analysis with our macaque dataset and the newly published macaque telencephalon development dataset. The results were only used to provide additional information to reviewers and were not included in the revised manuscript.

To verify the reliability of our cell annotation results, we compared the similarity of cell-type association between our study and recently published research(Micali N, Ma S, Li M, et al. Science. doi:10.1126/science.adf3786.PMID: 37824652), using the scmap package to project major cell types in our macaque development scRNA-seq dataset to GSE226451. The river plot in Author response image 1 illustrates the broadly similar relationships of cell type classification between the two datasets. Otherwise, we used more marker genes for cell annotation to improve the results of cell type definition in new Figure 1D. Besides, the description of distinct excitatory neuronal types has been improved in the new Figure 2.

Furthermore, we verified terminal oRG differentiation genes in the recently published macaque telencephalic development dataset(Micali N, Ma S, Li M, et al. Science. doi:10.1126/science.adf3786.PMID: 37824652) (GEO accession: GSE226451). The results of Authro response image 2 show that the gene expression showed states/stages. Most of the oRG terminal differentiation markers genes identified in our study were also expressed in the oRG cells of the GSE226451 dataset. In particular, the two datasets were consistent in the expression of ion channel genes ATP1A2, ATP1A2, and SCN4B.

Author Response

Note to the editor and reviewers.

All the authors would like to thank the editorial team and the two anonymous reviewers for their efforts and thoughtfulness in assessing our manuscript. We very much appreciate it and we all believe that the manuscript has been much improved in addressing the comments and suggestions made.

General considerations on the revised manuscript

We have applied extensive modifications to the manuscript with our main goal being the improvement of clarity. The Introduction has been changed mainly to introduce precisely our terminology and we have stuck to it in the rest of the manuscript. The Results section has been divided up into more defined sections. The discussion has been extensively re-written to improve clarity, following the suggestion of the reviewers. Main figures 1 and 4 have been modified with clearer schematics. Supplementary figures and legends have been modified and several supplementary schematic figures have been added to clearly present our interpretations for various data. We have added a Supplementary Discussion where the most detailed technical parts of our discussion are presented to avoid unnecessarily weighing down the main discussion, where our main conclusions are outlined. We have presented our mass photometry mixing experiment in a new supplementary figure, with detailed explanation. We have also expanded our discussion of in vivo and general relevance of our study.

Response to manuscript evaluation

Our manuscript has been evaluated as a valuable study and presenting solid experimental evidence. We appreciate the recognition of our work.

Two weaknesses were identified by reviewers: 1) our experiments do not completely exclude the possibility of an alternative nucleophile. This relates to the evaluation of our experimental evidence. 2) Our study does not address the in vivo relevance of the interface swapping phenomenon, which relate to the value of the study for the community.

Response to the evaluation of experimental evidence (Weakness #1):

We argued in the original manuscript that we have excluded completely the presence of an alternative nucleophile. This conclusion is based on a series of experiments which were presented in the originally submitted manuscript. These experiments are not discussed by the reviewers in relation to this main conclusion and therefore we suggest that they have not been properly evaluated. We believe our conclusion to be appropriately supported by these data (see our response to reviewer #1). In addition, the criticism of our gel-filtration data by reviewer #2 was based on a misinterpretation of Supplementary figure 1 b. We accept of course that the way the data was presented could be misleading and we assume responsibility for this. We have attempted to correct this by changing the main text and the figures legends and annotation. In conclusion, we believe that the evaluation of experimental evidence as presented in the revised manuscript could be upgraded to “convincing”.

Response to our study general relevance evaluation (weakness #2):

We agree with both reviewers about the in vivo relevance of our observation being an important question, not addressed so far. Indeed, the value of our study would be greatly increased by in vivo data and be of interest to a wider audience. However, we would like to argue that our study would interest a wider audience than initially stated for the following reasons: 1) Our study is the first evidence of interface swapping in vitro and will constitute a base to investigate this phenomenon both in vivo and in vitro. It will therefore interest a wide audience due to the potential involvement of interface swapping in a wide range of processes, such as recombination, evolution, and drug targeting (see also below). 2) DNA cleavage is the central mode of action of antibiotics targeting bacterial type II topoisomerases (i.e. topoisomerases “poisons”). This already established target is one of the few having produced new scaffolds and too few new antibacterial are in production to fulfill medical needs. The role of interface stability is also emerging as a modulator of the efficiency of topoisomerase poisons. See for instance (Germe, Voros et al. 2018, Bandak, Blower et al. 2023). By shedding light on interface dynamics, our study will be of interest to scientist interested in the development of these drugs. In addition, the heterodimer system can potentially produce detailed mechanistic information (Gubaev, Weidlich et al. 2016, Hartmann, Gubaev et al. 2017, Stelljes, Weidlich et al. 2018) not only on gyrase but also on other, dimeric type II topoisomerases or even other dimeric enzyme in general. We have amended the manuscript to make these points clearer. Therefore, we believe that the evaluation of the revised manuscript’s relevance could be upgraded to “important”.

Point-by-point response to the reviewer

Reviewer #1 (Public Review):

Germe and colleagues have investigated the mode of action of bacterial DNA gyrase, a tetrameric GyrA2GyrB2 complex that catalyses ATP-dependent DNA supercoiling. The accepted mechanism is that the enzyme passes a DNA segment through a reversible double-stranded DNA break formed by two catalytic Tyr residues-one from each GyrA subunit. The present study sought to understand an intriguing earlier observation that gyrase with a single catalytic tyrosine that cleaves a single strand of DNA, nonetheless has DNA supercoiling activity, a finding that led to the suggestion that gyrase acts via a nicking closing mechanism. Germe et al used bacterial co-expression to make the wild-type and mutant heterodimeric BA(fused). A complexes with only one catalytic tyrosine. Whether the Tyr mutation was on the A side or BA fusion side, both complexes plus GyrB reconstituted fluoroquinolone-stabilized double-stranded DNA cleavage and DNA supercoiling. This indicates that the preparations of these complexes sustain double strand DNA passage. Of possible explanations, contamination of heterodimeric complexes or GyrB with GyrA dimers was ruled out by the meticulous prior analysis of the proteins on native Page gels, by analytical gel filtration and by mass photometry. Involvement of an alternative nucleophile on the Tyr-mutated protein was ruled unlikely by mutagenesis studies focused on the catalytic ArgTyrThr triad of residues. Instead, results of the present study favour a third explanation wherein double-strand DNA breakage arises as a consequence of subunit (or interface/domain) exchange. The authors showed that although subunits in the GyrA dimer were thought to be tightly associated, addition of GyrB to heterodimers with one catalytic tyrosine stimulates rapid DNA-dependent subunit or interface exchange to generate complexes with two catalytic tyrosines capable of double-stranded DNA breakage. Subunit exchange between complexes is facilitated by DNA bending and wrapping by gyrase, by the ability of both GyrA and GyrB to form higher order aggregates and by dense packing of gyrase complexes on DNA. By addressing a puzzling paradox, this study provides support for the accepted double strand break (strand passage) mechanism of gyrase and opens new insights on subunit exchange that may have biological significance in promoting DNA recombination and genome evolution.

The conclusions of the work are mostly well supported by the experimental data.

Strengths:

The study examines a fundamental biological question, namely the mechanism of DNA gyrase, an essential and ubiquitous enzyme in bacteria, and the target of fluoroquinolone antimicrobial agents.

The experiments have been carefully done and the analysis of their outcomes is comprehensive, thoughtful and considered.

The work uses an array of complementary techniques to characterize preparations of GyrA, GyrB and various gyrase complexes. In this regard, mass photometry seems particularly useful. Analysis reveals that purified GyrA and GyrB can each form multimeric complexes and highlights the complexities involved in investigating the gyrase system.

The various possible explanations for the double-strand DNA breakage by gyrase heterodimers with a single catalytic tyrosine are considered and addressed by appropriate experiments.

The study highlights the potential biological importance of interactions between gyrase complexes through domain-or subunit-exchange

We thank the reviewer for their support, effort, and comments. The above is a great summary.

Weaknesses:

The mutagenesis experiments described do not fully eliminate the perhaps unlikely participation of an alternative nucleophile.

We agree that the mutagenesis experiment on its own does not fully eliminate the possibility of an alternative nucleophile. The number of residues mutated is limited, and therefore it is possible we have missed a putative alternative nucleophile.

However, we have other data and experiments supporting the conclusion that no alternative nucleophile exists. Therefore, we want to stress that our conclusion that no such alternative exist is based on these extra data. These data and experiments are not discussed by either reviewer despite being present in the original manuscript. This puzzled us and we have modified the manuscript and the figures in the hope that they, and their significance, would not be missed.

Briefly:

1) We have performed cleavage-based labeling of the nucleophile responsible for cleavage. This experiment is depicted in Figure 4. The nucleophilic activity of the residue involved results in covalent link between the polypeptide (that includes the residue) and radiolabeled DNA. Therefore, a polypeptide that includes an active nucleophile will be radiolabeled and visible, whereas a polypeptide that is missing an active nucleophile will remain unlabeled and invisible. We can distinguish the BA and the A polypeptide from their size. In the case of the BA.A complex both the BA polypetide and the A polypetide are radiolabeled and therefore both have an active nucleophile. In the case of the BAF.A complex, the unmutated A polypeptide is labeled, meaning that a nucleophile is still active. In contrast, the BAF polypeptide shows no detectable labeling. This result means that removing the hydroxyl group from the catalytic tyrosine abolishes any protein-DNA covalent link, suggesting that no other nucleophile from the BA polypetidic chain can substitute for the catalytic tyrosine hydroxyl group. This experiment excludes the possibility of an alternative nucleophile coming from the polypeptidic chain of either GyrA or GyrB. This experiment, described in figure 4, is not discussed by the reviewer. This experiment is similar in principle to early experiments identifying catalytic tyrosine in topoisomerases. See for instance, (Shuman, Kane et al. 1989).

2) The experiment above does not exclude a nucleophile coming from the solvent. To exclude this possibility, we have used T5 exonuclease (which needs a free 5’ DNA end to digest) and ExoIII (which need a free 3’ DNA end to digest). We have shown the reconstituted cleavage is not sensitive to T5 and sensitive to ExoIII. This shows that the 5’ end of the cleaved sites are protected by a bulky polypeptide impairing T5 activity, which is active in our reaction as shown by the digestion of a control DNA fragment. This experiment shows that the reconstituted cleavage is very unlikely to come from a small nucleotide potentially provided by the solvent. This experiment is described in the main text and the results are shown in supplementary figure 5. It is not mentioned by either reviewer.

3) Finally, we would like to emphasize our experiment comparing the BAF.A59 to BALLL.A59. The BALLL.A59 complex displays increased cleavage compared to BAF.A59. If this increased cleavage was due to an alternative nucleophile on the BALLL side, we would expect an accompanying increase in supercoiling activity since the BALLL.A59 possesses one CTD, which is sufficient for supercoiling. The fact that no increased supercoiling activity is observed strongly suggests subunit exchange reconstituting an A59 dimer, inactive for supercoiling but active for cleavage. We believe this somewhat complex observation to be quite significant and we have attempted to clarify the manuscript and discuss its full significance in several places.

Reviewer #1 (Recommendations For The Authors):

An interesting paper on DNA gyrase that explains a puzzling paradox in terms of the double-strand break mechanism.

Major points

1) The authors consider several mechanisms that could potentially explain their data. On page 15, the authors present the evidence against the nicking closing mechanism proposed by Gubaev et al. Throughout the manuscript, they indicate where their experimental results agree with this earlier work but should also indicate and account for differences. For example, Gubaev et al describe cross linking experiments that they claim rule out subunit exchange. These aspects should be clearly explained.

Thank you for the suggestion. We have re-written the discussion to address this point. We are extensively discussing experiments from (Gubaev, Weidlich et al. 2016), and offer our interpretation of apparently conflicting results. We suggest that their experiments are basically consistent with our data when correctly interpreted. To keep the main manuscript clear, we have added a supplementary discussion where experiments from (Gubaev, Weidlich et al. 2016) are discussed further in relation to our data.

2) Page 9. The experiments done to rule out the perhaps unlikely alternative nucleophile hypothesis relate to the possible role of the Arg and Threonine of the RYT triad. These residues are close to the DNA and therefore are prime candidates and attractive targets for mutagenesis. However, strictly speaking, the mutant enzyme data presented do not rule all possibilities. For example, Serine is often the nucleophile used by resolvases to effect DNA recombination via subunit exchange. The ideal experiment to rule out/rule in other nucleophiles would be to identify the residue(s) that become attached to DNA in the cleavage reaction.

Please see above. We have effectively ruled an alternative nucleophile with our cleavage-based labeling experiment and others that were present and discussed in the original manuscript but were missed. We have modified the manuscript and figures in order to make this point clearer than before.

3) p17. The readout for subunit exchange used by the authors is double-stranded DNA cleavage. Attempts to directly detect the formation of the DNA cleaving complexes GyrA2B2 and (GyrBA)2 (arising from subunit exchange between heterodimers) by mass photometry were not successful. Perhaps FRET would have been another approach to try as it could also detect interface and domain interchanges.

Directly detecting interface exchange directly by proximity experiment would be extremely useful. FRET would have to be done in the BAF.A + GyrB configuration where the amount of interface exchange is important. Now, we do not have the tools to do that and developing them would be outside the scope of the study. We propose cross linking experiment to be done in the future. We argue that the manuscript is convincing without these for now. This will be addressed in the future. This point, and other possible future experiments are now discussed in the discussion section.

4) The underlying canvas of this paper is the strand passage mechanism of gyrase. It would seem appropriate to include the papers first proposing it - Brown P.O and Cozzarelli N.R. (1979) and Mizuuchi K et al (1980).

We very much agree. These papers have now been added in the introduction as appropriate, highlighting the relationship between double-strand cleavage and the strand-passage mechanism.

5) Figure 1. The quality of the insets is poor. It is difficult to pick out the key catalytic residues and their disposition vis-a-vis DNA.

We agree, Figure 1 has been re-done and the schematic theme has been harmonized throughout the whole manuscript. We very much hope that clarity has improved. Thank you for the suggestion.

6) The experimental work is a very detailed analysis of a specific feature of engineered gyrase heterodimers. Making the work accessible to the general reader will be important. Using shorter paragraphs each with a specific theme might help. In particular, the second paragraph of the Results on p7, the section on p9 and bottom of p11, p13 and the first paragraph of the Discussion on p14 are each a page or more long. A shorter manuscript that avoids overinterpretation of the smaller details would also help.

We agree. We have now split long paragraphs into individual sections, with titles, in the Results. This structure is recapitulated at the beginning of the discussion, and we have split the discussion into shorter paragraphs, each with a unique point being made.

7) The impact of the Gubaev et al (2016) paper for the field in general, and as the catalyst for the present work should be better documented. Mention of this earlier paper and its significance at the beginning of the Abstract and elsewhere e.g in the Introduction might also help with a more logical organization of the current findings and result in a shorter paper (which would be easier to read).

We have added a reference to (Gubaev, Weidlich et al. 2016) in the abstract and have expanded our introduction

Minor points

1) Legends for Figs 2 and 6; Supplementary Figs 1 and 8. The designation of subfigures as a, b, c, d , e etc appears to be incorrect. Check throughout and in the text.

The manuscript has been checked for such errors.

2) Figure 2, and first paragraph p8. Peaks in Fig 2c should be labelled to facilitate discussion on p8.

Agreed, this has been done.

3) Supplementary Fig 4 and elsewhere in the manuscript. A variety of notations are used to denote phenylalanine mutants e.g. AsubscriptF, AsuperscriptF and AF. Check and use one format throughout.

Done

4) Figures showing gels include the label '+EtBr, +cipro'. This is somewhat confusing because EtBr was contained in the gel (not the samples) whereas cipro was included in the reaction. Modify or describe in the legend..

We have re-written the figure legend.

5) Supplementary Fig 4b describes a small effect on the ratio of linear to nicked DNA for the triple LLL mutant. Is this significant? How many times was the measurement made?

This has been addressed in the original manuscript in the supplementary data. In term of quantification, the experiment has been done 3 times for each prep, with the same GyrB prep and concentration. The standard error is displayed on the figure. This result is very reproducible and have been reproduced more than 3 times. No LLL cleavage assay showed more single-strand than double-strand cleavage. For the phenylalanine mutant, no cleavage assay showed more double-strand than single-strand cleavage.

6) Supplementary Fig 5 legend. Should 'L' read 'size markers' (and give their sizes)?

Yes indeed, we have modified the figure to clarify.

7) p11 line 5. Is this statement correct?

Yes, it is correct. Although we hope we are on the same line. When the Tyrosine is mutated on one side only of the heterodimer, both single- and double-strand cleavage are protected from T5 exonuclease digestion.

8) 12 last line should read...and supercoiling activity (not shown)..were

Thank you, done.

There are a number of typos throughout the text, for example:

Page 3 line..Difficult to conclude...what?

Page 3 para 3...Lopez....and Blazquez

We have corrected these typos and checked the whole manuscript.

Reviewer #2 (Public Review):

DNA gyrase is an essential enzyme in bacteria that regulates DNA topology and has the unique property to introduce negative supercoils into DNA. This enzyme contains 2 subunits GyrA and GyrB, which forms an A2B2 heterotetramer that associates with DNA and hydrolyzes ATP. The molecular structure of the A2B2 assembly is composed of 3 dimeric interfaces, called gates, which allow the cleavage and transport of DNA double stranded molecules through the gates, in order to perform DNA topology simplification. The article by Germe et al. questions the existence and possible mechanism for subunit exchange in the bacterial DNA gyrase complex.

The complexes are purified as a dimer of GyrA and a fusion of GyrB and GyrA (GyrBA), encoded by different plasmids, to allow the introduction of targeted mutations on one side only of the complex. The conclusion drawn by the authors is that subunit exchange does happen, favored by DNA binding and wrapping. They propose that the accumulation of gyrase in higher-order oligomers can favor rapid subunit exchange between two active gyrase complexes brought into proximity.

The authors are also debating the conclusions of a previous article by Gubaev, Weidlich et al 2016 (https://doi.org/10.1093/nar/gkw740). Gubaev et al. originally used this strategy of complex reconstitution to propose a nicking-closing mechanism for the introduction of negative supercoils by DNA gyrase, an alternative mechanism that precludes DNA strand passage, previously established in the field. Germe et al. incriminate in this earlier study the potential subunit swapping of the recombinant protein with the endogenous enzyme, that would be responsible for the detected negative supercoiling activity.

Accordingly, the authors also conclude that they cannot completely exclude the presence of endogenous subunits in their samples as well.

Strengths

The mix of gyrase subunits is plausible, this mechanism has been suggested by Ideka et al, 2004 and also for the human Top2 isoforms with the formation of Top2a/Top2b hybrids being identified in HeLa cells (doi: 10.1073/pnas.93.16.8288).

Germe et al have used extensive and solid biochemical experiments, together with thorough experimental controls, involving :

• the purification of gyrase subunits including mutants with domain deletion, subunit fusion or point mutations.

• DNA relaxation, cleavage and supercoiling assays

• biophysical characterization in solution (size exclusion chromatography, mass photometry, mass spectrometry)

Together the combination of experimental approaches provides solid evidence for subunit swapping in gyrase in vitro, despite the technical limitations of standard biochemistry applied to such a complex macromolecule.

We thank the reviewer for their supportive and considered comments.

Weaknesses

The conclusions of this study could be strengthened by in vivo data to identify subunit swapping in the bacteria, as proposed by Ideka et al, 2004. Indeed, if shown in vivo, together with this biochemical evidence, this mechanism could have a substantial impact on our understanding of bacterial physiology and resistance to drugs.

Thank you for this comment. Indeed, whether this interface exchange can happen in vivo and lead to recombination is a very important question. However, we believe that this is outside the scope of this study simply because of the amount of work one can fit into one paper. Proving that interface exchange can happen in vitro has already necessitated a number of non-trivial experiments and likewise investigating interface exchange in vivo will require a careful, long-term study (see our reply to reviewer #2 comment, who also raised this point). We can’t address it with one additional experiment with the tools we have. However, we very much hope to do it in the future.

Reviewer #2 (Recommendations For The Authors):

Specific questions and comments for the authors:

1) Complex identification during purification

The statement line 236-237 that "Our heterodimer preparation showed a single-peak on a gel-filtration column, distinct from the GyrA dimer peak" is not entirely clear. In Fig supp 1 b, how can the authors conclude from the superose 6 that GyrBA is separated from the GyrA dimer? Since they seem close in size 160/180kDa, they are unlikely to be well separated in a superose 6 gel filtration column. The SDS-PAGE seems to show both species in the same fractions #15-17 therefore it would not be possible to distinguish GyrBA. A from A2.

There appears to be some confusion about what Supp Fig. 1b shows. First, in all our gel filtration conditions both GyrBA and GyrA can’t exist as monomers at a significant concentration. Therefore, we can never observe the GyrBA monomer on a gel filtration column. Supp Fig. 1b shows the gel filtration profile of the BA.A heterodimer only. This is the output of the last, polishing step in the reaction. We analyze these results using SDS-PAGE. Therefore, the BA.A heterodimer will be denatured and separated into 2 polypeptides: GyrBA and GyrA, which migrates according to their size in an SDS-PAGE and forms two bands. These two bands do not represent two separate species in solution. They represent the separation of one species only, the BA.A heterodimer into its two, denatured, subunits: GyrA and GyrBA. We do not conclude from Supp Fig. 1 as a whole that GyrBA and the GyrA dimer are well separated, and this is not stated in the manuscript. We conclude that the BA.A dimer is fairly well separated from the GyrA dimer. They have significant different size (~260 kDa and ~180 kDa respectively) and form different peaks on a gel filtration column. The BA.A heterodimer has a GyrA subunit and therefore will shows a GyrA band on an SDS-PAGE, like the GyrA dimers but the two are obviously distinct in their quaternary structure. We are hoping that our new schematics and re-write of some of the results and figure legends will clarify this.

Panel 6 shows a different elution volume for the 2 species BA.A and A2 on an analytical S200 column, which appears better at separating the complexes in this size range.

Did the authors consider using a S200 column instead of superose 6 for the sample preparation, to optimize the separation of GyrBA. A from A2?

This is not a necessarily true statement (see above). We have not run the GyrA dimer on a Superose 6 column. The analysis was done on an s200 because extensive data for the GyrA dimer was already available with this, already calibrated column. We do not expect the Superose 6 to be worse in this size range. In fact, it might even be better. The Superose 6 profile in Supp. Fig. 1b shows BA.A only and no GyrA dimer. We have clarified the annotations in the figure to make this clearer.

Regarding the analytical gel filtration experiment, there is however an overlap in the elution volume in the analytical column, therefore how can the authors ensure there is no excess free A2 complex in the GyrBA. A sample?

Indeed, there is an overlap, but we argue that it is overstated. The important part of the overlap is where the maximum height of the GyrA peak is positioned compared to the BA.A trace, not where the traces intersect. This overlap is minimal. If a contaminating GyrA peak was hidden in the BA.A peak, it would have to be at least 10 times less intense than the BA.A peak. Since BA.A and GyrA dimer have roughly the same extinction coefficient, this means that a contamination would detectable at 10 % or even less. Our mass photometry further excludes such contamination.

Alternatively, the addition of a larger (cleavable) tag at the C-terminal end of the BA construct (therefore not disturbing dimer association) could allow to better distinguish the 2 populations already at the size exclusion step.

This is true and could allow cleaner purification. There are also other ways to achieve cleaner purification, like adding a secondary tag. However, like we argue in the manuscript, our contaminations are already minimal. It is questionable what benefits could be gained in changing the protocol. We also argue that the tandem tag method does not completely exclude contamination (Supplementary Discussion) and therefore we are not sure if this would be worth the time and expenditure.

2) GyrA and GyrB Oligomers:

In the mass photometry experiment, the authors explain that the low concentration of the proteins promotes dissociation of GyrA dimers, hence the detection of GyrA monomers instead of GyrA dimers, which are also detected in the GyrBA.A sample.

However, it cannot be concluded that the GyrA dimer is not formed in the condition of the gel filtration chromatography, at higher concentration.

In our mass photometry experiment, The BA.A sample is not as diluted as the GyrA dimer and much closer to our experimental condition. Since we have calculated the dissociation constant, we can calculate the expected level of dissociation (or reassociation). The level of dissociation is minimal in these conditions. If some dissociation is expected from the BA.A heterodimers, a very low amount of GyrBA monomer should also be present and yet they are not observed. We presume that it is because mass photometry is much more sensitive to GyrA (see our mixing mass photometry experiment that we have added). If the GyrA would reassociate at higher concentration, it would do so either with itself (forming a GyrA dimer) or with the GyrBA monomer, reforming the heterodimer. Assuming both GyrA dimer and heterodimer have the same dissociation constant, roughly one third of the GyrA monomer would reassociate with themselves. Assuming even complete reassociation of the GyrA dimer, this would leave only GyrA dimer accounting for 2% of the prep.

Another interpretation would be to assume that GyrBA monomers are not present at all and that GyrA monomer are reassociating only with themselves. This is not valid because of the following thermodynamic reason:

Since the profile for the GyrA dimer are collected at equilibrium, we should expect a ratio between GyrA monomer and dimers that follow the dissociation constant. In other words, if the GyrA monomer were in equilibrium with GyrA dimer we should expect a much higher dimer concentration already as the GyrA monomers are not as dilute. We do not observe a GyrA dimer peak in the BA.A profile, even though we can detect a low amount of GyrA dimer mixed with BA.A. Therefore, we conclude that the observed GyrA monomer must be in equilibrium with another dimerization partner, which is most probably the GyrBA monomer (see above). Therefore, only a minimal amount of GyrA dimer is expected to be formed at higher concentration by direct reassociation. This could probably increase if we let this solution-based exchange carry on for a long time at dissociation equilibrium. We have actually shown that this solution-based exchange is very slow and take several days because of the low dissociation at equilibrium.

The mass spectrometry analysis in Fig 2 confirms the presence of (monomeric) GyrA in the sample, despite different experimental conditions.

The concentration of heterodimer in the mass spectrometry experiment is actually higher than in the mass photometry experiment. This shows that self-reassociation of the GyrA monomer as suggested above is undetectable with mass spectrometry at higher concentration.

We considered that the “GyrA monomer” peak could be a contaminating GyrB monomer, which is ~90 kDa, which would explain the lack of reassociation. However, the mass spectrometry peak shows precisely the expected molecular weight of GyrA so we interpret this peak as arising from very limited dissociation of the BA.A heterodimer. The reassociation is limited at high concentration due simply to the fact that the difference in concentration between the mass photometry and our other experimental conditions is not that high. The GyrA dimer had to be diluted 400 times to see significant dissociation and yet even at this very low concentration the dissociation is far from complete.

Our general conclusions on the couple of point above is that we cannot completely exclude the presence of GyrA dimers being present, although they are undetectable in our working conditions either by mass photometry (lower concentration), Mass spectrometry (higher concentration) and even gel filtration (even higher concentration, see above). For the mass photometry, we have established that our detection threshold for a contamination is very low (see our mixing experiment).

Figure 2A: the authors state in the introduction that GyrB is a monomer in solution and then explain that the upper bands in the native gel are multimer of GyrB. Could the authors comment and provide the size exclusion profile of the Gyr B purification?

We have expanded our discussion of this. However, we have not been successful in collecting a gel filtration profile for GyrB. This is likely due to excessive oligomerization at the concentration we are using for gel filtration. We suggest that our mass photometry and Blue-Native PAGE experiment shows clearly that GyrB can be detected as a monomer in solution at the appropriate dilution. However, GyrB tends to oligomerize in a regular fashion (Consider especially Supp Fig. 8a), which suggest that it could align heterodimers on DNA in a linear, regular orientation. We have added a discussion of this.

Together the relevance of the oligomeric state of purified GyrA or GyrB should be clarified, relative to their role in subunit swapping.

We have added explanation in our discussion, while also trying to not be too speculative. Basically, we believe that GyrB oligomerization is likely to be involved. It is difficult to conclude for GyrA since no experiment has allowed us to test it. Therefore, the role of GyrA oligomerization, if any, is unclear. The GyrA tetramer is very prominent though and forms very easily. GyrB on the contrary forms longer oligomers more readily than GyrA and we surmise that this would help interface exchange. However, the structure of these GyrA and GyrB oligomers is not clear, which make it difficult to go beyond speculation on this. It would be a very interesting experiment if we were able to suppress GyrB oligomerization whilst conserving its ability to promote strand-passage and cleavage. Same goes for GyrA. Unfortunately, we are unable to do that at this time.

4) Subunit exchange

Line 320: the concept of subunit exchange in this context should be clearly explained. If one understands correctly, the authors mean that the BAF polypeptide, part of the BAF.A complex, could be replaced by a combination of B+A therefore forming a fully functional WT A2B2 gyrase complex.

Thank you for the suggestion. We have harmonized and clearly defined our terminology for interface swapping and subunit exchange in the introduction and attempted to be much more rigorous when referring to it.

A great effort has been done in this study to explain all the pros and cons of the experimental design but the length of the explanations may prevent readers outside of the field to fully appreciate the conclusions. This article would benefit from the addition of a few schematics to summarize the working hypothesis.

Thanks for the suggestion. We have added a series of schematics to illustrate our interpretation for each construct. As mentioned above the terminology has been more rigorously defined and updated throughout the manuscript.

5) Presence of endogenous GyrA

Line 419-425: it is quite difficult to follow the explanations regarding the possible contamination of the sample by endogenous GyrA.

Maybe these points should rather be addressed in the discussion, when debating the conclusions of Gubaev et al.

We agree. We have re-organized the Discussion doing just that. We added a Supplementary Discussion in which we further discuss the contamination problem in relation to (Gubaev, Weidlich et al. 2016).

Production of the subunits in another (non bacterial) expression system or a cell free system may prevent the association of endogenous protein.

Absolutely. We are planning on addressing this in the future, using the yeast expression system.

6) Mechanism for subunit swapping

Lines 588-595: As described by the authors the BA fusion shows decreased activity when compared with the WT probably due to limited conformational flexibility in absence of an additional linker sequence between the fused subunits.

The affinity of BA for A may possibly be reduced compared to the free A2B2 complex, due to a relative stiffness of the fusion upon full association with a free B subunit, as rightfully pointed by the authors.

If subunit exchange do happen in vitro, at least in the conditions of this study, the authors could assess the affinity of BA for A, when compared to the association of free B and A subunits

Experiments using analytical ultracentrifugation or surface plasmon resonance (SPR) may allow to determine the relative affinity of the BA +(A+B) compared to the A2B2 complex. This could be done also for the BALLL mutant and association with A59.

It would be extremely useful to measure the affinity of BA for A. However, this is difficult because of the high affinity of the interface. To measure a dissociation constant, one has to be able to measure the concentration of the monomer and the dimer at equilibrium. Because of this, the complex must be diluted enough to see any dissociation, making detection difficult. In practice, this also means that we cannot purify monomeric versions of these subunits. We therefore can’t perform “on-rate” study on an SPR surface, which would require flowing monomers on its partner subunit tethered to the SPR surface. However, we could perform “off-rate” studies, but the dissociation time is likely to be very long, making the measurement difficult. We have not tried it though, and it could turn out to be informative. An analysis of antibodies off-rate done in the past could provide a guideline for us to perform this experiment. Analytical ultracentrifugation is an excellent technique and could in theory provide information. In practice however it would be still necessary to dilute the complex enough to obtain significant dissociation at equilibrium, making detection difficult. As far as we are aware, analytical ultracentrifugation rely on UV absorbance for protein detection and therefore we probably would not detect our material at the necessary dilution. We are however open-minded about technique with very sensitive detection methods that could be used.

9) In vivo relevance

The study does not conclude on the subunits exchange in vivo, which have been suggested by earlier studies by Ikeda et al. To elaborate further on the relevance of such mechanism in the bacteria, experiments involving the fluorescent labeling of endogenous / exogenous mutant subunits may be required to provide further information on this phenomenon.

We completely agree that the in vivo relevance of such phenomena is the central question. Addressing this directly is not trivial though. Expressing both BA and A in vivo will results in random partnering and lead to a mix of dimers: A2 (1/4), BA2(1/4) and BA.A (1/2), assuming equal interface affinity. Therefore, to see subunit exchange in the same way as in vitro, one would have to get rid of the BA2 and A2 dimer together, or the BA.A dimer only. Our initial strategy to do that would be to engineer a specific dimer as being uniquely targeted for degradation. This could allow us to “get rid” of for instance the BA.A dimer. Subsequently, we would turn off the degradation and translation together and observe the rate of subunit exchange. This is not trivial though and would be the subject of a further study.

10) Figure 3: I guess the "intact" label refers to the supercoiled DNA (SC) ? It also appears as "uncleaved" in supp Figure 6. The same label for this topoisomer should be used throughout.

Thank you for pointing that out. It has now been corrected.

Bandak, A. F., T. R. Blower, K. C. Nitiss, R. Gupta, A. Y. Lau, R. Guha, J. L. Nitiss and J. M. Berger (2023). "Naturally mutagenic sequence diversity in a human type II topoisomerase." Proceedings of the National Academy of Sciences 120(28).

Germe, T., J. Voros, F. Jeannot, T. Taillier, R. A. Stavenger, E. Bacque, A. Maxwell and B. D. Bax (2018). "A new class of antibacterials, the imidazopyrazinones, reveal structural transitions involved in DNA gyrase poisoning and mechanisms of resistance." Nucleic Acids Res.

Gubaev, A., D. Weidlich and D. Klostermeier (2016). "DNA gyrase with a single catalytic tyrosine can catalyze DNA supercoiling by a nicking-closing mechanism." Nucleic Acids Res 44(21): 10354-10366.

Hartmann, S., A. Gubaev and D. Klostermeier (2017). "Binding and Hydrolysis of a Single ATP Is Sufficient for N-Gate Closure and DNA Supercoiling by Gyrase." J Mol Biol 429(23): 3717-3729. Shuman, S., E. M. Kane and S. G. Morham (1989). "Mapping the active-site tyrosine of vaccinia virus DNA topoisomerase I." Proc Natl Acad Sci U S A 86(24): 9793-9797.

Stelljes, J. T., D. Weidlich, A. Gubaev and D. Klostermeier (2018). "Gyrase containing a single C-terminal domain catalyzes negative supercoiling of DNA by decreasing the linking number in steps of two." Nucleic Acids Res.

Author Response

Reviewer #3 (Public Review):

Strengths:

NanoPDLIM2, nanotechnologies that efficiently deliver lentivirus overcomes resistance to chemotherapy and anti-PD-1 immunotherapy. This is a new strategy for enhancing the efficiency of immune checkpoint inhibitors.

This finding is important from a clinical translation perspective, but I have several minor concerns.

Weaknesses:

1) Please describe the mechanism of increased MHC class I and PD-L1 by PDLIM2.

Our previous studies showed that PDLIM2 induces MHC-I induction through decreasing STAT3 whereas it is dispensable for PD-L1 expression (Sun et al, 2019, PMID: 31757943). In line with the studies, PD-L1 is induced by chemotherapeutic drugs, but not by NanoPDLIM2 (Figure 6A). Together with the roles of PDLIM2 in repressing RelA-dependent MDR1 induction by chemotherapy and in preventing expression of cell survival and proliferation genes by targeting both RelA and STAT3 (Sun et al, 2019, PMID: 31757943), further providing the mechanistic basis for the combination and synergistic effect of nanoPDLIM2, anti-PD-1 and chemo drugs. The improvement has now been further incorporated.

2) Please describe the mechanism of decreased MDR1, nuclear RelA and STAT3 by PDLIM2.

Our previous studies demonstrated that PDLIM2 reduces MDR1 expression by degrading nuclear RelA (Sun et al, 2019, PMID: 31757943).

3) Please determine whether PDLIM2 expression directly impacts immune cells (function and number)?

As shown in Figure 5, NanoPDLIM2 increased the number and activation of tumor infiltrating lymphocytes (TILs); and in prior study, PDLIM2 knockout repressed the numbers of TILs and inhibited the activation of CD4+ and CD8+ T cells, while its re-expression in lung tumors led to T cell activation (Sun et al. 2019, PMID: 31757943). On the other hand, selective deletion of PDLIM2 in immune cells and in particular myeloid cells repressed the numbers and activation of TILs (Li et al, 2021, PMID: 33539325; PMCID: PMC8021114). Thus, PDLIM2 may impact immune cells both directly and indirectly, particularly when nanoparticles can deliver PDLIM2 into both tumor cells and tumor-associated immune cells (despite PDLIM2 is delivered into much fewer immune cells compared to tumor cells).

4) What is the efficiency of PDLIM2 delivery? Does delivery efficiency determine anti-tumor effect?

As shown in the manuscript, the dose of PDLIM2 used already shows high delivery (20-30 copies per tumor cell in Figure 3B) and therapeutic efficacy in the mouse model of refractory lung cancer and particularly when being combined with anti-PD-1 and chemo drugs. It is of interest to test different doses in the model for the best delivery and efficacy, which is actively being pursued in the lab.

5) Authors used a non-immunogenic tumor model. Can you demonstrate the combination effect with PDLIM2 in immunogenic lung cancer models to determine whether the combination of PDLIM2 with anti-PD-1 Ab confers a synergistic effect without chemotherapy?

Yes, it is of interest to demonstrate the combination of PDLIM2 and anti-PD-1 in immunogenic lung cancer models with chemotherapy although a synergy is highly expected. The greatest challenge in the lung cancer field is the low response of non-immunogenic tumor, which is the focus of the current manuscript.

6) On page 11, % change can make one over-interpret data.

The % change has been removed from the manuscript.

7) In Figure 5, what is the difference between 5A and 5D?

Figure 5A shows the increase of TILs by nanoPDLIM2 in animals that did not receive PD-1 blockade immunotherapy, Figure 5D shows the increase of TILs by nanoPDLIM2 in animals received PD-1 blockade immunotherapy.

8) It is unclear whether PDLIM2 confers an additive or a synergistic effect with anti-PD-1/chemo.

PDLIM2 nanotherapy confers a synergistic effect with chemotherapy on increasing apoptosis in tumors (Figure 4B) and tumor reduction (Figure 4A and 6E, left panel, tumor number), confers a synergistic effect with antiPD-1 on increasing CD4+ and CD8+ TILs (Figure 5A and 5D), and apoptosis in tumors (Figure 5F), and an additive effect on tumor reduction (Figure 5C and 6E), and confers a synergistic effect with chemotherapy plus anti-PD-1 on increasing CD4+ and CD8+ TILs (Figure 5A and 6F) and tumor reduction (Figure 6E, left panel, tumor number).

9) Have the authors tested any toxicity in normal lungs?

Same to tumor lungs, no obvious toxicity has been observed in normal lungs.

Reviewer #1 (Recommendations For The Authors):

The paper is clear and well-written, although some minor edits are needed. For example, the title could be changed to reflect both human and mouse studies in the manuscript for more general readers. Moreover, 'lung cancer' should be used instead of 'lung cancers'. The manuscript could be further improved by validating their findings in a different model and particularly the syngeneic model of metastatic lung cancer for a better overall survival time by the new combination therapy, given the fact that clinical trial studies usually start in patients with metastatic tumors. But this is optional because the therapeutic effect on primary lung cancer is already significant.

Thanks for the correction and wonderful suggestions. The “lung cancers” were replaced with “lung cancer”, and the title was changed to “Improving PD-1 blockade plus chemotherapy for complete remission of lung cancer by nanoPDLIM2”.

Reviewer #2 (Recommendations For The Authors):

1) What is the rationale for i.v. injection of nanoparticles containing PDLIM2 plasmid? Intranasal administration of nanoparticles may potentially target nanoPDLIM2 specifically to the lungs. Another potential option is intranasal infection of mice with adenovirus expressing PDLIM2.

The rationale for i.v. injection of nanoPDLIM2 is that iv injected nanoPDLIM2 first reach into the lung and more importantly tumor tissues as well as the convenience and high efficacy of mouse i.v. injection, particularly when multiple injections are needed. Mice are much less stressful compared to other intranasal or even intratracheal injection. Adenovirus can be used only once, because it will initiate ant-viral immune response in mice.

2) The authors examine PDLIM2 expression in lung tumors 1 week after i.v. administration of nanoparticles (Fig. 3A). Do all tumor cells express PDLIM2 after nanoPDLIM2 treatment? How long does PDLIM2 persist in the tumors? The kinetics of PDLIM2 expression may be informative to help interpret the results from the various combination treatments given to the mice. Multiple rounds of nanoPDLIM2 treatment could potentially improve the efficacy of the treatment.

For all the sections examined (n=6), PDLIM2 was re-expressed in most but not all lung cancer cells at 1-week of the i.v administration. Accordingly, nanoPDLIM2 was injected weekly. We are examining if PDLIM2 reexpression can last longer. We are also testing the best dose with the best efficacy.

3) Does the plasmid DNA from nanoparticles trigger an innate immune response in the lung that contributes to anti-tumor responses?

In line with previous studies showing no effect on immune responses (Bonnet et al. 2008. PMID: 18709489), the dose used in current study does not significantly affect immune cells in the lung, suggesting no obvious effect of nanoparticles with empty plasmid on innate immune response.

4) In Fig. 4, does the combination of nanoPDLIM2 and chemotherapy diminish STAT3 nuclear staining?

NanoPDLIM2 alone decreased nuclear STAT 3 in tumor cells (Figure 2C), it also diminished nuclear STAT3 in tumor cells with the combination of chemotherapy.

Author Response

On behalf of my co-authors, I thank you very much for sending our manuscript (# eLifeRP-RA-2023-91223) entitled “Elimination of subtelomeric repeat sequences exerts little effect on telomere functions in Saccharomyces cerevisiae” for review and providing us an opportunity for revision. We also thank the reviewers for their critical and constructive comments and suggestions which have helped us to strengthen our study. We have performed more experiments to address the concerns the reviewers raised, and we have also revised or corrected some of our statements as the reviewers suggested.

Reviewer #1

1) The author’s data indicate that cells with many chromosomes are more dependent on possibly homologous recombination than SY12 cells with three chromosomes. Telomerase-deficient cells exhibit the type I and type II telomere structures, whereas telomerase-deficient SY12 cells often generate different telomere structures (named Type X survivors or atypical survivors). Type I survivor depends on Rad51 possessing tandem Y' elements whereas Type II survivor depends on Rad59 carrying long TG sequences (line 60-70). Both types require Rad52 (line 66-70). At the moment, it is not determined how Type X or atypical survivors are generated in telomerase-deficient SY12 cells.

The authors need to determine whether Type X or atypical survivors depend on other repair pathways from Type I and Type II, and what DNA sequences are retained adjacent to telomeres in Type X or atypical survivors by sequencing analysis (Fig. 2).

We thank the reviewer’s valuable comments and suggestions. Atypical survivor is a subtype of survivor that exhibits non-uniform telomere patterns, distinct from those observed in Type I, Type II, Type X, or circular survivors. To further determine its genetic requirements, we deleted RAD52 in SY12 tlc1Δ, SY12YΔ tlc1Δ, SY12XYΔ tlc1Δ, and SY12XYΔ+Y tlc1Δ strains. Southern blotting results showed that neither Type I nor Type II survivors were found in the series of strains; circular survivor was in the predomination; beside circular survivor, some survivors exhibiting non-uniform telomere patterns suggested they were atypical survivor. These results have been presented as Figure 2—figure supplement 6B, Figure 5—figure supplement 2B and Figure 6—figure supplement 4B in the revised version. The results showed that atypical survivors still emerged when Rad52 pathway was repressed, indicating that the formation of atypical survivors does not strictly rely on the homologous recombination.

Given that "atypical" clones exhibit non-uniform telomere patterns, it’s not surprising that their chromosome structures are variable and tanglesome. Consequently, it is hard for us to amplify and sequence the DNA sequences retained adjacent to telomeres.

Since no Type X survivor was detected in SY12 tlc1Δ rad52Δ strain (Author response image 1A), we deleted RAD50 or RAD51 in SY12 tlc1Δ strain to investigate on which pathway the formation of the Type X survivor relied. Results showed that Type X survivor emerged in the absence of Rad51 but not Rad50, suggesting that the formation of Type X survivor depended on Rad50 pathway. These results have been presented as Figure 2—figure supplement 7.

To determine the chromosomal end structure of the Type X survivor, we randomly selected a typical Type X survivor, and performed PCR-sequencing analysis. The results revealed the intact chromosome ends for I-L, X-R, XIII-L, XI-R, and XIV-R, albeit with some mismatches compared with the S. cerevisiae S288C genome, which possibly arising from recombination events that occurred during survivor formation. Notably, the sequence of the Y’-element in XVI-L could not be detected, while the X-element remained intact. Figure 2—figure supplement 5 in the revised manuscript.

2) Survivor generation of each type (Type I, Type II, Type X or atypical and circularization) needs to be accurately quantitated. The authors concluded that X or Y' elements are not strictly necessary for survivor formation (Fig. 5 and Fig. 6). However, their removal appears to increase atypical survivor and chromosome circularization (Fig. 2 vs Fig. 5 and 6).

We are grateful for the reviewer’s critical and constructive suggestions. According to the reviewer’s requirement, we quantified each type of survivors in SY12 tlc1Δ, SY12YΔ tlc1Δ, SY12XYΔ tlc1Δ and SY12XYΔ+Y tlc1Δ strains (Figure 2D, 5C, 6A and 6B). In SY12 tlc1Δ strain, Type I survivors accounted for 16%, Type II survivors for 2%, Type X survivors for 24%, circular survivors for 20% and atypical survivors for 38%. In SY12YΔ tlc1Δ strain, 4% were Type II survivors, 52% were circular survivors and 44% were atypical survivors.

For the SY12XYΔ tlc1Δ strain, 8% were Type II survivors, 48% were circular survivors and 44% were atypical survivors. In SY12XYΔ+Y tlc1Δ strain, the proportions of Type II, circular and atypical survivors were 14%, 44%, and 42%, respectively (Author response image 1).

In comparing SY12YΔ with SY12XYΔ, we observed a similar ratio of circular and atypical survivors. This result indicates that the remove of X-elements exert little effect on the formation of circular and atypical survivors. Similarly, in SY12XYΔ+Y strain, the proportions of circular and atypical survivors were comparable to those in SY12XYΔ strain, indicating that Y’-elements also have little effect on the formation of circular and atypical survivors. However, due to the unknown frequency of survivor formation, alternative explanations of these data are possible. For example, subtelomeric elements previously suggested to have no impact on the formation of any survivor types might influence every type to similar extents, leading to similar ratios across all survivor types. With our present data, it is still unclear whether the absence of X and Y'-elements enhances the formation of circular and atypical survivors. Therefore, we did not present these results in the revised manuscript.

Author response image 1.

Quantitation of each survivor type in SY12 subtelomerice engineered strains. The ratio of survivor types in SY12 tlc1Δ, SY12YΔ tlc1Δ, SY12XYΔ tlc1Δ and SY12XYΔ+Y tlc1Δ strains. Type I, pulper; Type II, green; Type X, gray; atypical survivor, orange; circular survivor, blue.

3)The authors asked whether X and Y' elements are required for cell proliferation, stress response, telomere length control and telomere silencing (Fig. 4). Similar studies have been previously carried out by using synthetic chromosomes (see PMID: 28300123). The authors need to discuss this point.

Thanks for your suggestion, we have added the information in the revised version. (p.24 line 449-453)

4) The Fig. 7 data support that circular chromosomes do not require Ku-dependent DNA end protection. This is consistent with the current view that Ku binds and protects DNA ends. This finding by itself does not contribute significantly to our understanding of telomere maintenance. The authors need to more extensively discuss the significance of their findings in SY12 cells compared to wild-type cells with 16 chromosomes.

We agree with the logic that this reviewer has pointed out. Our results demonstrate that combinatorial deletion of YKU70 and TLC1 caused synthetic lethality in SY12 cells, which possess three linear chromosomes, However, it did not affect the viability of "circular survivors", supporting the notion that telomere deprotection leads to the synthetic lethality in yku70Δ tlc1Δ double mutants. Nevertheless, this conclusion merely confirms the current view observed in wild-type cells that Ku binds and protects DNA ends.

To avoid confusing readers and maintain the logical flow of the manuscript, we have deleted this section in the revised version.

Minor issues:

1) Line 112-113: " for SY13, which contains two chromosomes, could also have a high probability of circularizing all chromosomes for survival": The reference or the supplemental data are required.

Thank this reviewer for the suggestion. According to the reviewer’s comments, we performed a Southern blotting assay to examine the types of survivors in SY13 tlc1Δ strain. We found that the majority of SY13 tlc1Δ clones exhibited hybridization signal similar to SY14 tlc1Δ circular survivors, pointing to the possibility that two chromosomes in these survivors may undergo intra-chromosomal fusions. This result has been added to figure 1D in the revised version.

2) Line 349-350: The BY4742 mre11Δ haploid strain serves as a negative control. The authors need to explain why mre11 cells serve as a negative control.

Thank this reviewer for the comment. We employed mre11Δ as negative control because Mre11 is a member of the RAD52 epistasis group, which is involved in the repair of double-stranded breaks in DNA, and mutants in MRE11 exhibit defects in the repair of DNA damages caused by DNA damage drugs (Krogh and Symington, 2004; Lewis et al., 2004; Symington, 2002). (p.23 line 420-422)

Reviewer #2

1) The qualification of survivor types mostly relies on molecular patterns in Southern blots. While this is a valid method for a standard strain, it might be more difficult to apply to the strains used in this study. For example, in SY8, SY11 and SY12, the telomere signal at 1-1.2 kb can be very faint due to the small number of terminal Y' elements left. As another example, for the Y'-less strain, it might seem obvious that no Type I survivor can emerge given that Y' amplification is a signature of Type I, but maybe Type-I-specific molecular mechanisms might still be used. To reinforce the characterization of survivor types, an analysis of the genetic requirements for Type I and Type II survivors (e.g. RAD51, RAD54, RAD59, RAD50) could complement the molecular characterization in specific result sections.

We thank this reviewer for his/her constructive comments and suggestions. To investigate whether Type-I-specific molecular mechanisms are still utilized in the survivor formation in Y'-less strain, we deleted RAD51 in SY12XYΔ tlc1Δ. SY12XYΔ tlc1Δ rad51Δ strain was able to generate three types of survivors, including Type II survivor, circular survivor and atypical survivor, similar to the observations in SY12XYΔ tlc1Δ strain. However, the ratios of circular and atypical survivors were 36% and 32%, respectively, lower than the 48% and 44% observed in SY12XYΔ tlc1Δ strain (supplementary file 5). This result indicates that Type-I-specific molecular mechanisms contribute to the survivor formation. Given that our work primarily focuses on the function of subtelomeric elements, we chose not to include this result in our revised manuscript to maintain a coherent logical flow.

To reinforce the characterization of survivor types, we deleted RAD50, RAD51 and RAD52 in SY12 tlc1Δ strain, respectively. Southern blotting assay revealed that in the absence of Rad51, no Type I survivor was detected; in the absence of Rad50, neither Type I nor Type X survivor was detected. However, circular and atypical survivors still emerged in the absence of Rad52, suggesting that the RAD52-mediated homologous recombination is not strictly necessary for the formation of circular and atypical survivors. These results have been presented as Figure 2—figure supplement 6 and Figure 2— figure supplement 7.

2) In the title, the abstract and throughout the discussion, the authors chose to focus on the effect of X- and Y'-element deletion on different phenotypes and on survivor formation, as the main message to convey. While it is a legitimate and interesting message, other important results of this work might benefit from more spotlight. Namely, the observation that strains with different chromosome numbers show different survivor patterns and that several survival strategies beyond Type I and II exist and can reach substantial frequencies depending on the chromosomal context.

Thanks for your valuable suggestion. While we value your suggestion to highlight additional aspects of our work, we would like to express our perspective on the current emphasis on the effect of X- and Y'-element deletion. We believe that by maintaining this focus, we can present a more coherent and impactful narrative for our readers. Additionally, we recognize that the relationship between chromosome numbers and survivor type frequencies is complex and warrants further experimental validation. We are considering exploring this aspect in more detail in our future projects. However, we fully acknowledge the importance of the observations you raised concerning strains with different chromosome numbers and the diversity of survival strategies.

3) In SY12 strain, while X- and Y'-elements are not essential for survivor emergence, they do modulate the frequency of each type of survivors, with more chromosome circularization events observed for SY12YΔ, SY12XYΔ and SY12XYΔ+Y strains. This result should be stated and discussed, maybe alongside the change in survivor patterns in the other SY strains, to more accurately assess the roles of these subtelomeric elements.

Following the reviewer’s suggestion, we compared the circular survivor ratios in SY12 tlc1Δ, SY12YΔ tlc1Δ, SY12XYΔ tlc1Δ and SY12XYΔ+Y tlc1Δ strains (supplementary file 5). It appears that the formation of circular survivors is less efficient in the SY12 tlc1Δ, with a ratio of 20%, much lower than that in SY12YΔ tlc1Δ, SY12XYΔ tlc1Δ or SY12XYΔ+Y tlc1Δ strains. However, it should be noted that SY12 tlc1Δ can generate Type I and Type X survivors, potentially decreasing the ratio of circular survivors.

Therefore, we further compared the circular survivor ratios in SY12YΔ tlc1Δ, SY12XYΔ tlc1Δ and SY12XYΔ+Y tlc1Δ strains. In the SY12YΔ tlc1Δ strain, circular survivors accounted for 52% (26/50), comparable to 48% (24/50) in the SY12XYΔ tlc1Δ strain, indicating that X- elements exert little effect on the formation of circular survivor. Additionally, the ratio of circular survivors was 44% (22/50) in SY12XYΔ+Y tlc1Δ strain, also comparable to 48% (24/50) in the SY12XYΔ tlc1Δ strain, suggesting that Y’-element also has little effect on chromosome circularization. However, due to the unknown frequency of survivor formation, alternative explanations of these data are possible. For example, subtelomeric elements previously suggested to have no impact on the formation of any survivor types might influence every type to similar extents, resulting in similar ratios across all survivor types. With our current data, it is still uncertain whether X and Y'-elements modulate the frequency of each type of survivors. Therefore, we did not include these results in the revised manuscript.

4) The authors might want to update some general information about subtelomere structure and their diversity across yeast strain with the recent paper by O'Donnell et al. 2023 Nature Genetics, "Telomere-to-telomere assemblies of 142 strains characterize the genome structural landscape in Saccharomyces cerevisiae".

Thanks for your advice. We have added this information in the revised manuscript. (p.3 line 51-54)

5) Although it is cited in the discussion, the recent work by the Malkova lab (Kockler et al. 2021 Mol Cell) could be mentioned in the introduction as it conceptually changes our views on survivor formation, its dynamics and the categorization into Type I and Type II.

Thanks for your advice. We have added this information in the revised manuscript. (p.5 line 75-78)

6) p.7 line 128-130: rather than chromosome number, the ratio of survivor types might be controlled by the fraction of subtelomeres with Y'-elements and their relative configuration across chromosomes. A map of the structure of remaining subtelomeres in the SYn strains might be good to have.

We have added this information in supplementary file 2 in the revised manuscript.

7) Fig. 1C: in SY9 tlc1Δ, the lane with triangle mark looks like a type II.

The hybridization pattern of SY9 tlc1Δ clone 2 has both amplified Y’L-element and long heterogeneous TG1-3 repeats, it might be the “hybrid” survivor mentioned by Kockler’s work (Kockler et al., 2021). Therefore, we classify it as a no-classical survivor.

8) p.9 line 149: the title of this result section "Y'-element is not essential for the viability of cells carrying linear chromosomes" doesn't reflect well the content of the section, which is more about characterizing the survivor pattern in SY12.

Thanks for your advice. We have changed the title of this section into “Characterizing the survivor pattern in SY12” in the revised manuscript. (p.9 line 155)

9) p.10 line 167: that type I can emerge in SY12 indicates that multiple Y'-elements in tandem are not required for type I recombination. I am not sure if this was already known, but it could be noted.

We appreciate the reviewer’s comment. We have added this information in the revised manuscript. (p.10 175-177)

10) p.18 line 318-320: the deletion of the Y' element also seems to remove the centromere-proximal telomere sequence adjacent to it. Maybe it should be stated as well. Even more importantly, in lines 327-329, the Y'-element that is reintroduced in the strain does not include the centromere-proximal short telomere sequence. This is important to interpret the Southern blots.

We thank the reviewer for this critical suggestion. The deletion of Y'-element including both Y’- and X- element sequence in XVI-L (supplementary file 4), and the Y’element in the XVI-L does not contain the centromere-proximal telomere sequence. The Y'-element reintroduced into the left arm of Chr 3 in SY12XYΔ strain was cloned from native left arm of XVI in SY12 strain which does not contain the centromere-proximal short telomere sequence. Besides listing these details in supplementary file 4, we also emphasize it in the revised manuscript (p.21 line 397-398).

11) p.29 lines 496-497: it seems that X and Y'-elements tend to inhibit formation of circular survivors either directly (by participating in end protection), or by promoting type I and type II, thus reducing the fraction of circular survivors. Maybe this could be added to the conclusion of this section.

We thank the reviewer for his/her comments and have analyzed survivor types in SY12 tlc1Δ, SY12YΔ tlc1Δ, SY12XYΔ tlc1Δ and SY12XYΔ+Y tlc1Δ strains (supplementary file 5). Circular survivor formation appears less efficient in the SY12 tlc1Δ, with a ratio of 20%, significantly lower than SY12YΔ tlc1Δ, SY12XYΔ tlc1Δ or SY12XYΔ+Y tlc1Δ strains. However, it is noteworthy that SY12 tlc1Δ can generate Type I and Type X survivors, potentially impacting the circular survivor ratio.

We further compared circular survivor ratios in SY12YΔ tlc1Δ, SY12XYΔ tlc1Δ and SY12XYΔ+Y tlc1Δ strains. SY12YΔ tlc1Δ had 52% circular survivors, similar to SY12XYΔ tlc1Δ with 48%, indicating minimal impact of X- elements. Additionally, SY12XYΔ+Y tlc1Δ had 44% circular survivors, also similar to SY12XYΔ tlc1Δ, suggesting that Y’-element has little effect on chromosome circularization. However, due to unknown frequency of survivor formation, alternative explanations, like subtelomeric elements affecting all the type of survivor similarly, are possible. With our current data, it remains unclear whether X and Y'-elements are involved in end protection and consequently inhibit the formation of circular survivors.

Therefore, these results were not included in the revised manuscript.

12) p.32 line 533: this result section doesn't really fit with the rest of the paper, does it?

Thanks for your valuable advice. To avoid confusing readers and to keep the fluency of logic flow of the manuscript we have deleted this section in the revised version.

13) The methods section does not describe the experiments sufficiently and it often lacks specific details such as the manufacturer or references. Some sections of the methods are more exhaustive than others. They should all be written with the same level of detail in my opinion.

Thanks for your advice. We have described the experiments more sufficiently and added the manufacturer or references in the ‘materials and methods’ part in the revised manuscript. (p.41 line741-745, p.42 line 755-756, p.42 line 762-770, p.43 line 788 and p.45 line 812-813)

Minor comments, typos and grammatical errors:

p.3 line 33: "INTROUDUCTION" should be "INTRODUCTION".

We have corrected it in the revised manuscript. (p.3 line 33) p.4 line 54: "S, cerevisiae", use dot instead of comma. R15: We have corrected it in the revised manuscript. (p.4 line 57)

p.4 line 55: I believe TLC1 as the RNA moiety should be in (non-italicized) capital letters and not written as a protein.

We have corrected it in the revised manuscript. (p.4 line 58)

p.7 line 115: please indicate that pRS316 uses URA3 as a marker, otherwise the counterselection with 5'-FOA is not obvious.

Thank this reviewer for the comment. We have added this statement in the revised manuscript. (p.7 line 121-122)

p.12 line 206: tlc1Δ should be in italic.

We have corrected it in the revised manuscript. (p.10 line 184)

p.13 lines 227-229: "where only one hybridization signal", a verb seems to be missing.

We thank the reviewer’s kind reminder and have corrected the mentioned errors in the revised manuscript. (p.14 line 254-255)

Reviewer #3

1) A weakness of the manuscript is the analysis of telomere transcriptional silencing. They state: "The results demonstrated a significant increase in the expression of the MPH3 and HSP32 upon Sir2 deletion, indicating that telomere silencing remains effective in the absence of X and Y'-elements". However, there are no statistical analyses performed as far as I can see. For some of the strains, the significance of the increased expression in sir2 (especially for MPH3) looks questionable. In addition, a striking observation is that the SY12 strain (with only three chromosomes) express much less of both MPH3 and HSP32 than the parental strain BY4742 (16 chromosomes), both in the presence and absence of Sir2. In fact, the expression of both MPH3 and HSP32 in the SY12 sir2 strain is lower than in the BY4742 SIR2+ strain. In addition, relating this work to previous studies of subtelomeric sequences in other organisms would make the discussion more interesting.

First, I enjoyed reading your manuscript. It would be great if you performed the statistical analysis on the RT-qPCR data in figure 4B and addressed the issue of the difference of the BY4742 and SY12 strains. A model could be that this is a titration effect of silencing proteins due to fewer telomeres, which could be investigated by performing the analyses on more SY-strains with variable numbers of telomeres.

We highly appreciate the reviewer’s valuable comments and suggestions, which included a point that has also left us confused. We conducted statistical analyses on the RT-qPCR data, and the t-test result revealed that upon the deletion of Sir2, SY12YΔ, SY12XYΔ and SY12XYΔ+Y strains exhibited a significant increase in MPH3 expression (located on the right arm of chr X) with a P value < 0.05. In the case of SY12, the deletion of Sir2 resulted in an increase in gene expression (P value < 0.1). Similar tendencies were observed in the BY4742 strain. The statistical analyses of RTqPCR results on XVI-L mirrored those of X-R.

The results demonstrated a significant increase in MPH3 and HSP32 expression upon SIR2 deletion in SY12YΔ, SY12XYΔ and SY12XYΔ+Y strains, leading to the conclusion that telomere silencing remains effective in the absence of X-and Y’-elements. However, as the reviewer has pointed out, no statistically significant differences in MPH3 and HSP32 expression were observed between the SY12 and SY12 sir2Δ strain. For HSP32, this lack of significance may be attributed to the greater distance between HSP32 and telomere XVI-L in SY12 compared to SY12YΔ, SY12XYΔ or SY12XYΔ+Y strains, resulting in a weaker telomere position effect on HSP32 and a non-significant increase in gene expression in SY12. However, this explanation does not apply to MPH3, as SY12YΔ, with a same distance between MPH3 and telomere X-R as in SY12, still exhibits an effective telomere position effect on MPH3. We cannot provide a compelling explanation at this moment, and we suspect that the lack of statistically significant differences may be due to random clonal variation.

Additionally, the SY12 strain (with three chromosomes) exhibited lower expression levels of both MPH3 and HSP32 compared to the parental strain BY4742 (with 16 chromosomes). Notably, it has been reported that the expression of genes coding silencing proteins in SY14 (with one chromosomes) were nearly identical to that of BY4742 (with 16 chromosomes)(Shao et al., 2018). Consequently, with respect to the reduced chromosome numbers, the silencing proteins appeared to be relatively overexpressed. Therefore, as pointed out by the reviewer, this observed phenomenon may be attributed to a titration effect of silencing proteins due to fewer telomeres. We have added the statistical analyses result in Figure 4B.

We have related our work with previous studies of subtelomeric sequences in fission yeast in the discussion part. (p.37 line 655-676)

Minor points are to correct the figure legend for Figure 6 supplement 1 (the strain designations) and line 55, RNAs are written with all caps, i.e. TLC1, and line 537 delete the "which" in the sentence.

Thanks for your advice. We have corrected them in the revised manuscript.

1) The strain has been replaced with SY12XYΔ+Y (p.35 line 617, 618 and 620)

2) “Tlc1” has been replaced with “TLC1” (p.4 line 58).

3) We have deleted the section of “Circular chromosome maintain stable when double knockout of yku70 and tlc1” according to the suggestions raised by reviewer 1 and 2, the deleted section contain the sentence in line 537 you mentioned.

Kockler, Z.W., Comeron, J.M., and Malkova, A. (2021). A unified alternative telomerelengthening pathway in yeast survivor cells. Molecular Cell 81, 1816-1829.e1815. Krogh, B.O., and Symington, L.S. (2004). Recombination proteins in yeast. Annu Rev Genet 38, 233-271.

Lewis, L.K., Storici, F., Van Komen, S., Calero, S., Sung, P., and Resnick, M.A. (2004). Role of the nuclease activity of Saccharomyces cerevisiae Mre11 in repair of DNA double-strand breaks in mitotic cells. Genetics 166, 1701-1713.

Shao, Y., Lu, N., Wu, Z., Cai, C., Wang, S., Zhang, L.L., Zhou, F., Xiao, S., Liu, L., Zeng, X., et al. (2018). Creating a functional single-chromosome yeast. Nature 560, 331-335. Symington, L.S. (2002). Role of RAD52 epistasis group genes in homologous recombination and double-strand break repair. Microbiol Mol Biol Rev 66, 630-670, table of contents.

Author Response

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

eLife assessment

This valuable study reports on the potential of neural networks to emulate simulations of human ventricular cardiomyocyte action potentials for various ion channel parameters with the advantage of saving simulation time in certain conditions. The evidence supporting the claims of the authors is solid, although the inclusion of open analysis of drop-off accuracy and validation of the neural network emulators against experimental data would have strengthened the study. The work will be of interest to scientists working in cardiac simulation and quantitative pharmacology.

Thank you for the kind assessment. It is important for us to point out that, while limited, experimental validation was performed in this study and is thoroughly described in the work.

Reviewer 1 - Comments

This manuscript describes a method to solve the inverse problem of finding the initial cardiac activations to produce a desired ECG. This is an important question. The techniques presented are novel and clearly demonstrate that they work in the given situation. The paper is well-organized and logical.

Strengths:

This is a well-designed study, which explores an area that many in the cardiac simulation community will be interested in. The article is well written and I particularly commend the authors on transparency of methods description, code sharing, etc. - it feels rather exemplary in this regard and I only wish more authors of cardiac simulation studies took such an approach. The training speed of the network is encouraging and the technique is accessible to anyone with a reasonably strong GPU, not needing specialized equipment.

Weaknesses:

Below are several points that I consider to be weaknesses and/or uncertainties of the work:

C I-(a) I am not convinced by the authors’ premise that there is a great need for further acceleration of cellular cardiac simulations - it is easy to simulate tens of thousands of cells per day on a workstation computer, using simulation conditions similar to those of the authors. I do not really see an unsolved task in the field that would require further speedup of single-cell simulations. At the same time, simulations offer multiple advantages, such as the possibility to dissect mechanisms of the model behaviour, and the capability to test its behaviour in a wide array of protocols - whereas a NN is trained for a single purpose/protocol, and does not enable a deep investigation of mechanisms. Therefore, I am not sure the cost/benefit ratio is that strong for single-cell emulation currently.

An area that is definitely in need of acceleration is simulations of whole ventricles or hearts, but it is not clear how much potential for speedup the presented technology would bring there. I can imagine interesting applications of rapid emulation in such a setting, some of which could be hybrid in nature (e.g. using simulation for the region around the wavefront of propagating electrical waves, while emulating the rest of the tissue, which is behaving more regularly/predictable, and is likely to be emulated well), but this is definitely beyond of the scope of this article.

Thank you for this point of view. Simulating a population of few thousand cells is completely feasible on single desktop machines and for fixed, known parameters, emulation may not fill ones need. Yet we still foresee a great untapped potential for rapid evaluations of ionic models, such as for the gradient-based inverse problem, presented in the paper. Such inverse optimization requires several thousand evaluations per cell and thus finding maximum conductances for the presented experimental data set (13 cell pairs control/drug → 26 APs) purely through simulations would require roughly a day of simulation time even in a very conservative estimation (3.5 seconds per simulation, 1000 simulations per optimization). Additionally, the emulator provides local sensitivity information between the AP and maximum conductances in the form of the gradient, which enables a whole new array of efficient optimization algorithms [Beck, 2017]. To further emphasize these points, we added the number of emulations and runtime of each conducted experiment in the specific section and a paragraph in the discussion that addresses this point:

"Cardiomyocyte EP models are already very quick to evaluate in the scale of seconds (see Section 2.3.1), but the achieved runtime of emulations allows to solve time consuming simulation protocols markedly more efficient. One such scenario is the presented inverse maximum conductance estimation problem (see Section 3.1.2 and Section 3.1.3), where for estimating maximum conductances of a single AP, we need to emulate the steady state AP at least several hundred times as part of an optimization procedure. Further applications include the probabilistic use of cardiomyocyte EP models with uncertainty quantification [Chang et al., 2017, Johnstone et al., 2016] where thousands of samples of parameters are potentially necessary to compute a distribution of the steady-state properties of subsequent APs, and the creation of cell populations [Muszkiewicz et al., 2016, Gemmell et al., 2016, Britton et al., 2013]." (Section 4.2)

We believe that rapid emulations are valuable for several use-cases, where thousands of evaluations are necessary. These include the shown inverse problem, but similarly arise in uncertainty quantification, or cardiomyocyte population creation. Similarly, new use-cases may arise as such efficient tools become available. Additionally, we provided the number of evaluations along with the runtimes for each of the conducted experiments, showing how essential these speedups are to realize these experiments in reasonable timeframes. Utilizing these emulations in organ-level electrophysiological models is a possibility, but the potential problems in such scenarios are much more varied and depend on a number of factors, making it hard to pin-point the achievable speed-up using ionic emulations.

C I-(b) The authors run a cell simulation for 1000 beats, training the NN emulator to mimic the last beat. It is reported that the simulation of a single cell takes 293 seconds, while emulation takes only milliseconds, implying a massive speedup. However, I consider the claimed speedup achieved by emulation to be highly context-dependent, and somewhat too flattering to the presented method of emulation. Two specific points below:

First, it appears that a not overly efficient (fixed-step) numerical solver scheme is used for the simulation. On my (comparable, also a Threadripper) CPU, using the same model (”ToR-ORd-dyncl”), but a variable step solver ode15s in Matlab, a simulation of a cell for 1000 beats takes ca. 50 seconds, rather than 293 of the authors. This can be further sped up by parallelization when more cells than available cores are simulated: on 32 cores, this translates into ca. 2 seconds amortized time per cell simulation (I suspect that the NN-based approach cannot be parallelized in a similar way?). By amortization, I mean that if 32 models can be simulated at once, a simulation of X cells will not take X50 seconds, but (X/32)50. (with only minor overhead, as this task scales well across cores).

Second, and this is perhaps more important - the reported speed-up critically depends on the number of beats in the simulation - if I am reading the article correctly, the runtime compares a simulation of 1000 beats versus the emulation of a single beat. If I run a simulation of a single beat across multiple simulated cells (on a 32-core machine), the amortized runtime is around 20 ms per cell, which is only marginally slower than the NN emulation. On the other hand, if the model was simulated for aeons, comparing this to a fixed runtime of the NN, one can get an arbitrarily high speedup.

Therefore, I’d probably emphasize the concrete speedup less in an abstract and I’d provide some background on the speedup calculation such as above, so that the readers understand the context-dependence. That said, I do think that a simulation for anywhere between 250 and 1000 beats is among the most reasonable points of comparison (long enough for reasonable stability, but not too long to beat an already stable horse; pun with stables was actually completely unintended, but here it is...). I.e., the speedup observed is still valuable and valid, albeit in (I believe) a somewhat limited sense.

We agree that the speedup comparison only focused on a very specific case and needs to be more thoroughly discussed and benchmarked. One of the main strengths of the emulator is to cut the time of prepacing to steady state, which is known to be a potential bottleneck for the speed of the single-cell simulations. The time it takes to reach the steady state in the simulator is heavily dependant on the actual maximum conductance configuration and the speed-up is thus heavily reliant on a per-case basis. The differences in architecture of the simulator and emulator further makes direct comparisons very difficult. In the revised version we now go into more detail regarding the runtime calculations and also compare it to an adaptive time stepping simulation (Myokit [Clerx et al., 2016]) in a new subsection:

"The simulation of a single AP (see Section 2.1) sampled at a resolution of 20kHz took 293s on one core of a AMD Ryzen Threadripper 2990WX (clock rate: 3.0GHz) in CARPentry. Adaptive timestep solver of variable order, such as implemented in Myokit [Clerx et al., 2016], can significantly lower the simulation time (30s for our setup) by using small step sizes close to the depolarization (phase 0) and increasing the time step in all other phases. The emulation of a steady state AP sampled at a resolution of 20kHz for t ∈ [−10, 1000]ms took 18.7ms on a AMD Ryzen 7 3800X (clock rate: 3.9GHz) and 1.2ms on a Nvidia A100 (Nvidia Corporation, USA), including synchronization and data copy overhead between CPU and GPU.

"The amount of required beats to reach the steady state of the cell in the simulator has a major impact on the runtime and is not known a-priori. On the other hand, both simulator and emulator runtime linearly depends on the time resolution, but since the output of the emulator is learned, the time resolution can be chosen at arbitrarily without affecting the AP at the sampled times. This makes direct performance comparisons between the two methodologies difficult. To still be able to quantify the speed-up, we ran Myokit using 100 beats to reach steady state, taking 3.2s of simulation time. In this scenario, we witnessed a speed-up of 171 and 2 · 103 of our emulator on CPU and GPU respectively (again including synchronization and data copy overhead between CPU and GPU in the latter case). Note that both methods are similarly expected to have a linear parallelization speedup across multiple cells.

For the inverse problem, we parallelized the problem for multiple cells and keep the problem on the GPU to minimize the overhead, achieving emulations (including backpropagation) that run in 120µs per AP at an average temporal resolution of 2kHz. We consider this the peak performance which will be necessary for the inverse problem in Section 3.1.2." (Section 2.3.1)

Note that the mentioned parallelization across multiple machines/hardware applies equally to the emulator and simulator (linear speed-up), though the utilization for single cells is most likely different (single vs. multi-cell parallelization).

C I-(c) It appears that the accuracy of emulation drops off relatively sharply with increasing real-world applicability/relevance of the tasks it is applied to. That said, the authors are to be commended on declaring this transparently, rather than withholding such analyses. I particularly enjoyed the discussion of the not-always amazing results of the inverse problem on the experimental data. The point on low parameter identifiability is an important one and serves as a warning against overconfidence in our ability to infer cellular parameters from action potentials alone. On the other hand, I’m not that sure the difference between small tissue preps and single cells which authors propose as another source of the discrepancy will be that vast beyond the AP peak potential (probably much of the tissue prep is affected by the pacing electrode?), but that is a subjective view only. The influence of coupling could be checked if the simulated data were generated from 2D tissue samples/fibres, e.g. using the Myokit software.

Given the points above (particularly the uncertain need for further speedup compared to running single-cell simulations), I am not sure that the technology generated will be that broadly adopted in the near future.

However, this does not make the study uninteresting in the slightest - on the contrary, it explores something that many of us are thinking about, and it is likely to stimulate further development in the direction of computationally efficient emulation of relatively complex simulations.

We agree that the parameter identifiability is an important point of discussion. While the provided experimental data gave us great insights already, we still believe that given the differences in the setup, we can not draw conclusions about the source of inaccuracies with absolute certainty. The suggested experiment to test the influence of coupling is of interest for future works and has been integrated into the discussion. Further details are given in the response to the recommendation R III- (t)

Reviewer 2 - Comments

Summary:

This study provided a neural network emulator of the human ventricular cardiomyocyte action potential. The inputs are the corresponding maximum conductances and the output is the action potential (AP). It used the forward and inverse problems to evaluate the model. The forward problem was solved for synthetic data, while the inverse problem was solved for both synthetic and experimental data. The NN emulator tool enables the acceleration of simulations, maintains high accuracy in modeling APs, effectively handles experimental data, and enhances the overall efficiency of pharmacological studies. This, in turn, has the potential to advance drug development and safety assessment in the field of cardiac electrophysiology.

Strengths:

1) Low computational cost: The NN emulator demonstrated a massive speed-up of more than 10,000 times compared to the simulator. This substantial increase in computational speed has the potential to expedite research and drug development processes

2) High accuracy in the forward problem: The NN emulator exhibited high accuracy in solving the forward problem when tested with synthetic data. It accurately predicted normal APs and, to a large extent, abnormal APs with early afterdepolarizations (EADs). High accuracy is a notable advantage over existing emulation methods, as it ensures reliable modeling and prediction of AP behavior

C II-(a) Input space constraints: The emulator relies on maximum conductances as inputs, which explain a significant portion of the AP variability between cardiomyocytes. Expanding the input space to include channel kinetics parameters might be challenging when solving the inverse problem with only AP data available.

Thank you for this comment. We consider this limitation a major drawback, as discussed in Section 4.3. Identifiability is already an issue when only considering the most important maximum conductances. Further extending the problem to include kinetics will most likely only increase the difficulty of the inverse problem. For the forward problem though, it might be of interest to people studying ionic models to further analyze the effects of channel kinetics.

C II-(b) Simplified drug-target interaction: In reality, drug interactions can be time-, voltage-, and channel statedependent, requiring more complex models with multiple parameters compared to the oversimplified model that represents the drug-target interactions by scaling the maximum conductance at control. The complex model could also pose challenges when solving the inverse problem using only AP data.

Thank you pointing out this limitation. We slightly adapted Section 4.3 to further highlight some of these limitations. Note however that the experimental drugs used have been shown to be influenced by this drug interaction in varying degrees [Li et al., 2017] (e.g. dofetilide vs. cisapride). However, the discrepancy in identifiability was mostly channel-based (0%-100%), whereas the variation in identifiability between drugs was much lower (39%-66%).

C II-(c) Limited data variety: The inverse problem was solved using AP data obtained from a single stimulation protocol, potentially limiting the accuracy of parameter estimates. Including AP data from various stimulation protocols and incorporating pacing cycle length as an additional input could improve parameter identifiability and the accuracy of predictions.

The proposed emulator architecture currently only considers the discussed maximum conductances as input and thus can only compensate when using different stimulation protocols. However, the architecture itself does not prohibit including any of these as parameters for future variants of the emulator. We potentially foresee future works extending on the architecture with modified datasets to include other parameters of importance, such as channel kinetics, stimulation protocols and pacing cycle lengths. These will however vary between the actual use-cases one is interested in.

C II-(d) Larger inaccuracies in the inverse problem using experimental data: The reasons for this result are not quite clear. Hypotheses suggest that it may be attributed to the low parameter identifiability or the training data set were collected in small tissue preparation.

The low parameter identifiability on some channels (e.g. GK1) poses a problem, for which we state multiple potential reasons. As of yet, no final conclusion can be drawn, warranting further research in this area.

Reviewer 3 - Comments

Summary:

Grandits and colleagues were trying to develop a new tool to accelerate pharmacological studies by using neural networks to emulate the human ventricular cardiomyocyte action potential (AP). The AP is a complex electrical signal that governs the heartbeat, and it is important to accurately model the effects of drugs on the AP to assess their safety and efficacy. Traditional biophysical simulations of the AP are computationally expensive and time-consuming. The authors hypothesized that neural network emulators could be trained to predict the AP with high accuracy and that these emulators could also be used to quickly and accurately predict the effects of drugs on the AP.

Strengths:

One of the study’s major strengths is that the authors use a large and high-quality dataset to train their neural network emulator. The dataset includes a wide range of APs, including normal and abnormal APs exhibiting EADs. This ensures that the emulator is robust and can be used to predict the AP for a variety of different conditions.

Another major strength of the study is that the authors demonstrate that their neural network emulator can be used to accelerate pharmacological studies. For example, they use the emulator to predict the effects of a set of known arrhythmogenic drugs on the AP. The emulator is able to predict the effects of these drugs, even though it had not been trained on these drugs specifically.

C III-(a) One weakness of the study is that it is important to validate neural network emulators against experimental data to ensure that they are accurate and reliable. The authors do this to some extent, but further validation would be beneficial. In particular for the inverse problem, where the estimation of pharmacological parameters was very challenging and led to particularly large inaccuracies.

Thank you for this recommendation. Further experimental validation of the emulator in the context of the inverse problem would be definitely beneficial. Still, an important observation is that the identifiability varies greatly between channels. While the inverse problem is an essential reason for utilizing the emulator, it is also empirically validated for the pure forward problem and synthetic inverse problem, together with the (limited) experimental validation. The sources of problems arising in estimating the maximum conductances of the experimental tissue preparations are important to discuss in future works, as we now further emphasize in the discussion. See also the response to the recommendations R III-(t).

Reviewer 1 - Recommendations

R I-(a) Could further detail on the software used for the emulation be provided? E.g. based on section 2.2.2, it sounds like a CPU, as well as GPU-based emulation, is possible, which is neat.

Indeed as suspected, the emulator can run on both CPUs and GPUs and features automatic parallelization (per-cell, but also multi-cell), which is enabled by the engineering feats of PyTorch [Paszke et al., 2019]. This is now outlined in a bit more detail in Sec. 2 and 5.

"The trained emulator is provided as a Python package, heavily utilizing PyTorch [Paszke et al., 2019] for the neural network execution, allowing it to be executed on both CPUs and NVidia GPUs." (Section 5)

R I-(b) I believe that a potential use of NN emulation could be also in helping save time on prepacing models to stability - using the NN for ”rough” prepacing (e.g. 1000 beats), and then running a simulation from that point for a smaller amount of time (e.g. 50 beats). One could monitor the stability of states, so if the prepacing was inaccurate, one could quickly tell that these models develop their state vector substantially, and they should be simulated for longer for full accuracy - but if the model was stable within the 50 simulated beats, it could be kept as it is. In this way, the speedup of the NN and accuracy and insightfulness of the simulation could be combined. However, as I mentioned in the public review, I’m not sure there is a great need for further speedup of single-cell simulations. Such a hybrid scheme as described above might be perhaps used to accelerate genetic algorithms used to develop new models, where it’s true that hundreds of thousands to millions of cells are eventually simulated, and a speedup there could be practical. However one would have to have a separate NN trained for each protocol in the fitness function that is to be accelerated, and this would have to be retrained for each explored model architecture. I’m not sure if the extra effort would be worth it - but maybe yes to some people.

Thank you for this valuable suggestion. As pointed out in C I-(a), one goal of this study was to reduce the timeconsuming task of prepacing. Still, in its current form the emulator could not be utilized for prepacing simulators, as only the AP is computed by the emulator. For initializing a simulation at the N-th beat, one would additionally need all computed channel state variables. However, a simple adaptation of the emulator architecture would allow to also output the mentioned state variables.

R I-(c) Re: ”Several emulator architectures were tried on the training and validation data sets and the final choice was hand-picked as a good trade-off between high accuracy and low computational cost” - is it that the emulator architecture was chosen early in the development, and the analyses presented in the paper were all done with one previously selected architecture? Or is it that the analyses were attempted with all considered architectures, and the well-performing one was chosen? In the latter case, this could flatter the performance artificially and a test set evaluation would be worth carrying out.

We apologize for the unclear description of the architectural validation. The validation was in fact carried out with 20% of the training data (data set #1), which is however completely disjoint with the test set (#2, #3, #4, formerly data set #1 and #2) on which the evaluation was presented. To further clarify the four different data sets used in the study, we now dedicated an additional section to describing each set and where it was used (see also our response below R I-(d)), and summarize them in Table 1, which we also added at R II-(a). The cited statement was slightly reworked.

"Several emulator architectures were tried on the training and validation data sets and the final choice was hand-picked as a good trade-off between high accuracy on the validation set (#1) and low computational runtime cost." (Section 2.2.2)

R I-(d) When using synthetic data for the forward and inverse problem, with the various simulated drugs, is it that split of the data into training/validation test set was done by the drug simulated (i.e., putting 80 drugs and the underlying models in the training set, and 20 into test set)? Or were the data all mixed together, and 20% (including drugs in the test set) were used for validation? I’m slightly concerned by the potential of ”soft” data leaks between training/validation sets if the latter holds. Presumably, the real-world use case, especially for the inverse problem, will be to test drugs that were not seen in any form in the training process. I’m also not sure whether it’s okay to reuse cell models (sets of max conductances) between training and validation tests - wouldn’t it be better if these were also entirely distinct? Could you please comment on this?

We completely agree with the main points of apprehension that training, validation and test sets all serve a distinct purpose and should not be arbitrarily mixed. However, this is only a result of the sub-optimal description of our datasets, which we heavily revised in Section 2.2.1 (Data, formerly 2.3.1). We now present the data using four distinct numbers: The initial training/validation data, now called data set #1 (formerly no number), is split 80%/20% into training and validation sets (for architectural choices) respectively. The presented evaluations in Section 2.3 (Evaluation) are purely performed on data set #2 (normal APs, formerly #1), #3 (EADs, formerly #2) and #4 (experimental).

R I-(e) For the forward problem on EADs, I’m not sure if the 72% accuracy is that great (although I do agree that the traces in Fig 12-left also typically show substantial ICaL reactivation, but this definitely should be present, given the IKr and ICaL changes). I would suggest that you also consider the following design for the EAD investigation: include models with less severe upregulation of ICaL and downregulation of IKr, getting a population of models where a part manifests EADs and a part does not. Then you could run the emulator on the input data of this population and be able to quantify true, falsexpositive, negative detections. I think this is closer to a real-world use case where we have drug parameters and a cell population, and we want to quickly assess the arrhythmic risk, with some drugs being likely entirely nonrisky, some entirely risky, and some between (although I still am not convinced it’s that much of an issue to just simulate this in a couple of thousands of cells).

Thank you for pointing out this alternative to address the EAD identification task. Even though the values chosen in Table 2 seem excessively large, we still only witnessed EADs in 171 of the 950 samples. Especially border cases, which are close to exhibiting EADs are hardest to estimate for the NN emulator. As suggested, we now include the study with the full 950 samples (non-EAD & EAD) and classify the emulator AP into one of the labels for each sample. The mentioned 72.5% now represent the sensitivity, whereas our accuracy in such a scenario becomes 90.8% (total ratio of correct classifications):

"The data set #3 was used second and Appendix C shows all emulated APs, both containing the EAD and non-EAD cases. The emulation of all 950 APs took 0.76s on the GPU specified in Section 2.2.3 We show the emulation of all maximum conductances and the classification of the emulation. The comparison with the actual EAD classification (based on the criterion outlined in Appendix A) results in true-positive (EAD both in the simulation and emulation), false-negative (EAD in the simulation, but not in the emulation), false-positive (EAD in the emulation, but not in the simulation) and true-negative (no EAD both in the emulation and simulation). The emulations achieved 72.5% sensitivity (EAD cases correctly classified) and 94.9% specificity (non-EAD cases correctly classified), with an overall accuracy of 90.8% (total samples correctly classified). A substantial amount of wrongly classified APs showcase a notable proximity to the threshold of manifesting EADs. Figure 7 illustrates the distribution of RMSEs in the EAD APs between emulated and ground truth drugged APs. The average RMSE over all EAD APs was 14.5mV with 37.1mV being the maximum. Largest mismatches were located in phase 3 of the AP, in particular in emulated APs that did not fully repolarize." (Section 3.1.1)

R I-(f) Figure 1 - I think a large number of readers will understand the mathematical notation describing inputs/outputs; that said, there may be a substantial number of readers who may find that hard to read (e.g. lab-based researchers, or simulation-based researchers not familiar with machine learning). At the same time, this is a very important part of the paper to explain what is done where, so I wonder whether using words to describe the inputs/outputs would not be more practical and easier to understand (e.g. ”drug-based conductance scaling factor” instead of ”s” ?). It’s just an idea - it needs to be tried to see if it wouldn’t make the figure too cluttered.

We agree that the mathematical notation may be confusing to some readers. As a compromise between using verbose wording and mathematical notation, we introduced a legend in the lower right corner of the figure that shortly describes the notation in order to help with interpreting the figure.

R I-(g) ”APs with a transmembrane potential difference of more than 10% of the amplitude between t = 0 and 1000 ms were excluded” - I’m not sure I understand what exactly you mean here - could you clarify?

With this criterion, we try to discard data that is far away from fully repolarizing within the given time frame, which applies to 116 APs in data set #1 and 50 APs in data set #3. We added a small side note into the text:

"APs with a transmembrane potential difference of more than 10% of the amplitude between t = 0 and 1000ms (indicative of an AP that is far away from full repolarization) were excluded." (Section 2.2.1)

R I-(h) Speculation (for the future) - it looks like a tool like this could be equally well used to predict current traces, as well as action potentials. I wonder, would there be a likely benefit in feeding back the currents-traces predictions on the input of the AP predictor to provide additional information? Then again, this might be already encoded within the network - not sure.

Although not possible with the chosen architecture (see also R I-(b)), it is worth thinking about an implementation in future works and to study differences to the current emulator.

Entirely minor points:

R I-(i) ”principle component analysis” → principal component analysis

Fixed

R I-(j) The paper will be probably typeset by elife anyway, but the figures are often quite far from their sections, with Results figures even overflowing into Discussion. This can be often fixed by using the !htb parameters (\begin{figure}[!htb]), or potentially by using ”\usepackage[section]{placeins}” and then ”\FloatBarrier” at the start and end of each section (or subsection) - this prevents floating objects from passing such barriers.

Thank you for these helpful suggestions. We tried reducing the spacing between the figures and their references in the text, hopefully improving the reader’s experience.

R I-(k) Alternans seems to be defined in Appendix A (as well as repo-/depolarization abnormalities), but is not really investigated. Or are you defining these just for the purpose of explaining what sorts of data were also included in the data?

We defined alternans since this was an exclusion criterion for generating simulation data.

Reviewer 2 - Recommendations

R II-(a) Justification for methods selection: Explain the rationale behind important choices, such as the selection of specific parameters and algorithms.

Thank you for this recommendation, we tried to increase transparency of our choices by introducing a separate data section that summarizes all data sets and their use cases in Section 2.2.1 and also collect many of the explanations there. Additionally we added an overview table (Table 1) of the utilized data.

Author response table 1.

Table 1: Summary of the data used in this study, along with their usage and the number of valid samples. Note that each AP is counted individually, also in cases of control/drug pairs.

R II-(b) Interpretation of the evaluation results: After presenting the evaluation results, consider interpretations or insights into what the results mean for the performance of the emulator. Explain whether the emulator achieved the desired accuracy or compare it with other existing methods. In the revised version, we tried to further expand the discussion on possible applications of our emulator (Section 4.2). See also our response to C I-(a). To the best of our knowledge, there are currently no out-of-the-box methods available for directly comparing all experiments we considered in our work.

Reviewer 3 - Recommendations

R III-(a) In the introduction (Page 3) and then also in the 2.1 paragraph authors speak about the ”limit cycle”: Do you mean steady state conditions? In that case, it is more common to use steady state.

When speaking about the limit cycle, we refer to what is also sometimes called the steady state, depending on the field of research and/or personal preference. We now mention both terms at the first occurence, but stick with the limit cycle terminology which can also be found in other works, see e.g. [Endresen and Skarland, 2000].

R III-(b) On page 3, while comparing NN with GP emulators, I still don’t understand the key reason why NN can solve the discontinuous functions with more precision than GP.

The potential problems in modeling sharp continuities using GPs is further explained in the referenced work [Ghosh et al., 2018] and further references therein:

"Statistical emulators such as Gaussian processes are frequently used to reduce the computational cost of uncertainty quantification, but discontinuities render a standard Gaussian process emulation approach unsuitable as these emulators assume a smooth and continuous response to changes in parameter values [...] Applying GPs to model discontinuous functions is largely an open problem. Although many advances (see the discussion about non-stationarity in [Shahriari et al., 2016] and the references in there) have been made towards solving this problem, a common solution has not yet emerged. In the recent GP literature there are two specific streams of work that have been proposed for modelling non-stationary response surfaces including those with discontinuities. The first approach is based on designing nonstationary processes [Snoek et al., 2014] whereas the other approach attempts to divide the input space into separate regions and build separate GP models for each of the segmented regions. [...]"([Ghosh et al., 2018])

We integrated a short segment of this explanation into Section 1.

R III-(c) Why do authors prefer to use CARPentry and not directly openCARP? The use of CARPentry is purely a practical choice since the simulation pipeline was already set up. As we now point out however in Sec. 2.1 (Simulator), simulations can also be performed using any openly available ionic simulation tool, such as Myokit [Clerx et al., 2016], OpenCOR [Garny and Hunter, 2015] and openCARP [Plank et al., 2021]. We emphasized this in the text.

"Note, that the simulations can also be performed using open-source software such as Myokit [Clerx et al., 2016], OpenCOR [Garny and Hunter, 2015] and openCARP [Plank et al., 2021]." (Section 2.1)

R III-(d) In paragraph 2.1:

(a) In this sentence: ”Various solver and sampling time steps were applied to generate APs and the biomarkers used in this study (see Appendix A)” this reviewer suggests putting the Appendix reference near “biomarkers”. In addition, a figure that shows the test of various solver vs. sampling time steps could be interesting and can be added to the Appendix as well.

(b) Why did the authors set the relative difference below 5% for all biomarkers? Please give a reference to that choice. Instead, why choose 2% for the time step?

1) We adjusted the reference to be closer to “biomarkers”. While we agree that further details on the influence of the sampling step would be of interest to some of the readers, we feel that it is far beyond the scope of this paper.

2) There is no specific reference we can provide for the choice. Our goal was to reach 5% relative difference, which we surpassed by the chosen time steps of 0.01 ms (solver) and 0.05 ms (sampling), leading to only 2% difference. We rephrased the sentence in question to make this clear.

"We considered the time steps with only 2% relative difference for all AP biomarkers (solver: 0.01ms; sampling: 0.05ms) to offer a sufficiently good approximation." (Section 2.1)

R III-(e) In the caption of Figure 1 authors should include the reference for AP experimental data (are they from Orvos et al. 2019 as reported in the Experimental Data section?)

We added the missing reference as requested. As correctly assumed, they are from [Orvos et al., 2019].

R III-(f) Why do authors not use experimental data in the emulator development/training?

For the supervised training of our NN emulator, we need to provide the maximum conductances of our chosen channels for each AP. While it would be beneficial to also include experimental data in the training to diversify the training data, the exact maximum conductances in our the considered retrospective experiments are not known. In the case such data would be available with low measurement uncertainty, it would be possible to include.

R III-(g) What is TP used in the Appendix B? I could not find the acronymous explanation.

We are sorry for the oversight, TP refers to the time-to-peak and is now described in Appendix A.

R III-(h) Are there any reasons for only using ST and no S1? Maybe are the same?

The global sensitivity analysis is further outlined in Appendix B, also showing S1 (first-order effects) and ST (variance of all interactions) together (Figure 11) [Herman and Usher, 2017] and their differences (e.g. in TP) Since S1 only captures first-order effects, it may fail to capture higher-order interactions between the maximum conductances, thus we favored ST.

R III-(i) In Training Section Page 8. It is not clear why it is necessary to resample data. Can you motivate?

The resampling part is motivated by exactly capturing the swift depolarization dynamics, whereas the output from CARPentry is uniformly sampled. This is now further highlighted in the text.

"Then, the data were non-uniformly resampled from the original uniformly simulated APs, to emphasize the depolarization slope with a high accuracy while lowering the number of repolarization samples. For this purpose, we resamled the APs [...]" (Section 2.2.1)

R III-(j) For the training of the neuronal network, the authors used the ADAM algorithm: have you tested any other algorithm?

For training neural networks, ADAM has become the current de-facto standard and is certainly a robust choice for training our emulator. While there may exist slightly faster, or better-suited training algorithms, we witnessed (qualitative) convergence in the training (Equation (2)). We thus strongly believe that the training algorithm is not a limiting factor in our study.

R III-(k) What is the amount of the drugs tested? Is the same dose reported in the description of the second data set or the values are only referring to experimental data? Moreover, it is not clear if in the description of experimental data, the authors are referring to newly acquired data (since they described in detail the protocol) or if they are obtained from Orvos et al. 2019 work.

In all scenarios, we tested 5 different drugs (cisapride, dofetilide, sotalol, terfenadine, verapamil). We revised our previous presentation of the data available, and now try to give a concise overview over the utilized data (Section 2.2.1 and table 1) and drug comparison with the CiPA distributions (Table 5, former 4). Note that in the latter case, the available expected channel scaling factors by the CiPA distributions vary, but are now clearly shown in Table 5.

R III-(l) In Figure 4, I will avoid the use of “control” in the legend since it is commonly associated with basal conditions and not with the drug administration.

The terminology “control” in this context is in line with works from the CiPA initiative, e.g. [Li et al., 2017] and refers to the state of cell conditions before the drug wash-in. We added a minor note the first time we use the term control in the introduction to emphasize that we refer to the state of the cell before administering any drugs

"To compute the drugged AP for given pharmacological parameters is a forward problem, while the corresponding inverse problem is to find pharmacological parameters for given control (before drug administration) and drugged AP." (Section 1)

R III-(m) In Table 1 when you referred to Britton et al. 2017 work, I suggest adding also 10.1371/journal.pcbi.1002061.

We added the suggested article as a reference.

R III-(n) For the minimization problem, only data set #1 has been used. Have you tested data set #2?

In the current scenario, we only tested the inverse problem for data set #2 (former #1). The main purpose for data set #3 (former #2), was to test the possibility to emulate EAD APs. Given the overall lower performance in comparison to data set #2 (former #1), we also expect deteriorated results in comparison to the existing inverse synthetic problem.

R III-(o) In Figure 6 you should have the same x-axis (we could not see any points in the large time scale for many biomarkers). Why dVmMax is not uniformed distributed compared to the others? Can you comment on that?

As suggested, we re-adjusted the x-range to show the center of distributions. Additionally, we denoted in each subplot the number of outliers which lie outside of the shown range. The error distribution on dVmMax exhibits a slightly off-center, left-tailed normal distribution, which we now describe a bit more in the revised text:

"While the mismatches in phase 3 were simply a result of imperfect emulation, the mismatches in phase 0 were a result of the difficulty in matching the depolarization time exactly. [...] Likewise, the difficulty in exactly matching the depolarization time leads to elevated errors and more outliers in the biomarkers influenced by the depolarization phase (TP and dVmMax)," (Section 3.1.1)

R III-(p) Page 14. Can the authors better clarify ”the average RMSE over all APs 13.6mV”: is it the mean for all histograms in Figure 7? (In Figure 5 is more evident the average RMSE).

The average RMSE uses the same definition for Figures 5 and 7: It is the average over all the RMSEs for each pair of traces (simulated/emulated), though the amount of samples is much lower for the EAD data set and not normal distributed.

R III-(q) In Table 4, the information on which drugs are considered should be added. For each channel, we added the names of the drugs for which respective data from the CiPA initiative were available.

R III-(r) Pag. 18, second paragraph, there is a repetition of ”and”.

Fixed

R III-(s) The pair’s combination of scaling factors for simulating synthetic drugs reported in Table 2, can be associated with some effects of real drugs? In this case, I suggest including the information or justifying the choice.

The scaling factors in Table 2 are used to create data set #3 (former #2), and is meant to provide several APs which expose EADs. This is described in more detail in the new data section, Section 2.2.1:

"Data set #3: The motivation for creating data set #3 was to test the emulator on data of abnormal APs showing the repolarization abnormality EAD. This is considered a particularly relevant AP abnormality in pharmacological studies because of their role in the genesis of drug-induced ventricular arrhythmia’s [Weiss et al., 2010]. Drug data were created using ten synthetic drugs with the hERG channel and the Cav1.2 channel as targets. To this end, ten samples with pharmacological parameters for GKr and PCa (Table 2) were generated and the synthetic drugs were applied to the entire synthetic cardiomyocyte population by scaling GKr and PCa with the corresponding pharmacological parameter. Of the 1000 APs simulated, we discarded APs with a transmembrane potential difference of more than 10% of the amplitude between t = 0 and 1000ms (checked for the last AP), indicative of an AP that does not repolarize within 1000ms. This left us with 950 APs, 171 of which exhibit EAD (see Appendix C)." (Section 2.2.1)

R III-(t) A general comment on the work is that the authors claim that their study highlights the potential of NN emulators as a powerful tool for increased efficiency in future quantitative systems pharmacology studies, but they wrote ”Larger inaccuracies were found in the inverse problem solutions on experimental data highlight inaccuracies in estimating the pharmacological parameters”: so, I was wondering how they can claim the robustness of NN use as a tool for more efficient computation in pharmacological studies.

The discussed robustness directly refers to efficiently emulating steady-state/limit cycle APs from a set of maximum conductances (forward problem, Section 3.1.1). We extensively evaluated the algorithm and feel that given the low emulation RMSE of APs (< 1 mV), the statement is warranted. The inverse estimation, enabled through this rapid evaluation, performs well on synthetic data, but shows difficulties for experimental data. Note however that at this point there are multiple potential sources for these problems as highlighted in the Evaluation section (Section 4.1) and Table 5 (former 4) highlights the difference in accuracy of estimating per-channel maximum conductances, revealing a potentially large discrepancy. The emulator also offers future possibilities to incorporate additional informations in the forms of either priors, or more detailed measurements (e.g. calcium transients) and can be potentially improved to a point where also the inverse problem can be satisfactorily solved in experimental preparations, though further analysis will be required.

References [Beck, 2017] Beck, A. (2017). First-order methods in optimization. SIAM.

[Britton et al., 2013] Britton, O. J., Bueno-Orovio, A., Ammel, K. V., Lu, H. R., Towart, R., Gallacher, D. J., and Rodriguez, B. (2013). Experimentally calibrated population of models predicts and explains intersubject variability in cardiac cellular electrophysiology. Proceedings of the National Academy of Sciences, 110(23).

[Chang et al., 2017] Chang, K. C., Dutta, S., Mirams, G. R., Beattie, K. A., Sheng, J., Tran, P. N., Wu, M., Wu, W. W., Colatsky, T., Strauss, D. G., and Li, Z. (2017). Uncertainty quantification reveals the importance of data variability and experimental design considerations for in silico proarrhythmia risk assessment. Frontiers in Physiology, 8.

[Clerx et al., 2016] Clerx, M., Collins, P., de Lange, E., and Volders, P. G. A. (2016). Myokit: A simple interface to cardiac cellular electrophysiology. Progress in Biophysics and Molecular Biology, 120(1):100–114.

[Endresen and Skarland, 2000] Endresen, L. and Skarland, N. (2000). Limit cycle oscillations in pacemaker cells. IEEE Transactions on Biomedical Engineering, 47(8):1134–1137.

[Garny and Hunter, 2015] Garny, A. and Hunter, P. J. (2015). OpenCOR: a modular and interoperable approach to computational biology. Frontiers in Physiology, 6.

[Gemmell et al., 2016] Gemmell, P., Burrage, K., Rodr´ıguez, B., and Quinn, T. A. (2016). Rabbit-specific computational modelling of ventricular cell electrophysiology: Using populations of models to explore variability in the response to ischemia. Progress in Biophysics and Molecular Biology, 121(2):169–184.

[Ghosh et al., 2018] Ghosh, S., Gavaghan, D. J., and Mirams, G. R. (2018). Gaussian process emulation for discontinuous response surfaces with applications for cardiac electrophysiology models.

[Herman and Usher, 2017] Herman, J. and Usher, W. (2017). SALib: An open-source python library for sensitivity analysis. J. Open Source Softw., 2(9):97.

[Johnstone et al., 2016] Johnstone, R. H., Chang, E. T., Bardenet, R., de Boer, T. P., Gavaghan, D. J., Pathmanathan, P., Clayton, R. H., and Mirams, G. R. (2016). Uncertainty and variability in models of the cardiac action potential: Can we build trustworthy models? Journal of Molecular and Cellular Cardiology, 96:49–62.

[Li et al., 2017] Li, Z., Dutta, S., Sheng, J., Tran, P. N., Wu, W., Chang, K., Mdluli, T., Strauss, D. G., and Colatsky, T. (2017). Improving the in silico assessment of proarrhythmia risk by combining hERG (human ether`a-go-go-related gene) channel–drug binding kinetics and multichannel pharmacology. Circulation: Arrhythmia and Electrophysiology, 10(2).

[Muszkiewicz et al., 2016] Muszkiewicz, A., Britton, O. J., Gemmell, P., Passini, E., S´anchez, C., Zhou, X., Carusi, A., Quinn, T. A., Burrage, K., Bueno-Orovio, A., and Rodriguez, B. (2016). Variability in cardiac electrophysiology: Using experimentally-calibrated populations of models to move beyond the single virtual physiological human paradigm. Progress in Biophysics and Molecular Biology, 120(1):115–127.

[Orvos et al., 2019] Orvos, P., Kohajda, Z., Szlov´ak, J., Gazdag, P., Arp´adffy-Lovas, T., T´oth, D., Geramipour, A.,´ T´alosi, L., Jost, N., Varr´o, A., and Vir´ag, L. (2019). Evaluation of possible proarrhythmic potency: Comparison of the effect of dofetilide, cisapride, sotalol, terfenadine, and verapamil on hERG and native iKr currents and on cardiac action potential. Toxicological Sciences, 168(2):365–380.

[Paszke et al., 2019] Paszke, A., Gross, S., Massa, F., Lerer, A., Bradbury, J., Chanan, G., Killeen, T., Lin, Z., Gimelshein, N., Antiga, L., Desmaison, A., Kopf, A., Yang, E., DeVito, Z., Raison, M., Tejani, A., Chilamkurthy, S., Steiner, B., Fang, L., Bai, J., and Chintala, S. (2019). PyTorch: An Imperative Style, High-Performance Deep Learning Library. In Advances in Neural Information Processing Systems, volume 32. Curran Associates, Inc.

[Plank et al., 2021] Plank, G., Loewe, A., Neic, A., Augustin, C., Huang, Y.-L., Gsell, M. A., Karabelas, E., Nothstein, M., Prassl, A. J., S´anchez, J., Seemann, G., and Vigmond, E. J. (2021). The openCARP simulation environment for cardiac electrophysiology. Computer Methods and Programs in Biomedicine, 208:106223.

[Shahriari et al., 2016] Shahriari, B., Swersky, K., Wang, Z., Adams, R. P., and de Freitas, N. (2016). Taking the Human Out of the Loop: A Review of Bayesian Optimization. Proceedings of the IEEE, 104(1):148–175. Conference Name: Proceedings of the IEEE.

[Snoek et al., 2014] Snoek, J., Swersky, K., Zemel, R., and Adams, R. (2014). Input Warping for Bayesian Optimization of Non-Stationary Functions. In Proceedings of the 31st International Conference on Machine Learning, pages 1674–1682. PMLR. ISSN: 1938-7228.

[Weiss et al., 2010] Weiss, J. N., Garfinkel, A., Karagueuzian, H. S., Chen, P.-S., and Qu, Z. (2010). Early afterdepolarizations and cardiac arrhythmias. Heart Rhythm, 7(12):1891–1899.

Author Response

We thank you for your careful review of our manuscript and helpful comments and suggestions. We have carefully considered each point and have addressed them by adding changes to the manuscript and figures. The text below detailed our responses and edits.

Reviewer #1 (Public Review):

Summary:

Liao et al leveraged two powerful genomics techniques-CUT&RUN and RNA sequencing-to identify genomic regions bound by and activated or inactivated by SMAD1, SMAD5, and the progesterone receptor during endometrial stromal cell decidualization.

Strengths:

The authors utilized powerful next generation sequencing and identified important transcriptional mechanisms of SMAD1/5 and PGR during decidualization in vivo.

Weaknesses:

Overall, the manuscript and study are well structured and provide critical mechanistic updates on the roles of SMAD1/5 in decidualization and preparation of the maternal endometrium for pregnancy. Please consider the following to improve the manuscript:

• Figure 4: A and C show bar graphs, not histograms. Please alter this phrasing.

Figure legends were adjusted as suggested.

• What post hoc test was performed on qPCR analyses? (Figure 6). It is evident that any assumptions of equal variance need to be negated due to the wide dispersion in experimental response invalidating the assumptions of a one-way ANOVA.

Yes, a Tukey’s post hoc test was performed on the qPCR analyses. To address the reviewer’s question regarding equal variance, normality of the dataset was examined by D’agostino & Pearson test in GraphPad Prism. The data demonstrated a normal distribution pattern, thus justifying the one-way ANOVA test.

• Figure 6: what data points are plotted? Are these technical replicates from individual wells or qPCR technical replicates?

The dataset represents three technical and three biological data points.

• Figure 6: Consider changing graph colors to increase visibility of error bars and data points.

Thank you for this suggestion. The colors of the error bars in Figure 6 have been changed to increase visibility. Additionally, different shapes have been utilized to distinguish between different groups.

• Figure 6 legend: no histograms are shown in this figure. Refer to all gene names utilizing proper nomenclature and conventions (gene names should be italicized).

The legend was adjusted as suggested with the correct nomenclature implemented.

• qPCR analyses: qPCR normalization should be done to at least two internal control genes, preferably three according to the MIQE guidelines (PMID: 19246619).

As suggested, we have performed additional qPCR analysis with normalization done to three internal controls.

• Supplement figure 2: graphs are bar graphs, not histograms.

The legends have been changed as suggested.

Reviewer #2 (Public Review):

Summary:

Liao and colleagues generated tagged SMAD1 and SMAD5 mouse models and identified genome occupancy of these two factors in the uterus of these mice using the CUT&RUN assay. The authors used integrative bioinformatic approaches to identify putative SMAD1/5 direct downstream target genes and to catalog the SMAD1/5 and PGR genome co-localization pattern. The role of SMAD1/5 on stromal decidualization was assayed in vitro on primary human endometrial stromal cells. The new mouse models offer opportunities to further dissect SMAD1 and SMAD5 functions without the limitation from SMAD antibodies, which is significant. The CUT&RUN data further support the usefulness of these mouse models for this purpose.

Strengths:

The strength of this study is the novelty of new mouse models and the valuable cistromic data derived from these mice.

Weaknesses:

The weakness of the present version of the manuscript includes the self-limited data analysis approaches such as the proximal promoter based bioinformatic filter and a missed opportunity to investigate the role of SMAD1/5 on determining the genome occupancy of major uterine transcription regulators.

Thank you for the comments. We addressed the limitation of the promoter-based analysis in the discussion and pointed out the possibility of analyzing additional genomics features (Lines 548551). Based on the suggestions, we also included an analysis in which we compared SMAD1/5 binding activities in this study to known major uterine transcription regulators’ binding activities (namely, SOX17 and NR2F2) using published ChIP-seq data in the mouse uterus. Results from this analysis are discussed in Lines 426-436. Content from the adjusted manuscript is copied below.

Lines 548-551:

“From pathway enrichment analysis, we demonstrate that genes with SMAD1/5 and PR bound at the promoter regions are enriched for key pathways in directing the decidualization process, such as WNT and relaxin signaling pathways. Future studies can benefit from analyzing binding events beyond the promoter regions.”

Lines 426-436:

“To further evaluate the key roles of SMAD1/5 as major uterine transcription regulators, we cross-compared the genomic binding sites of SMAD1/5 with known key transcription factors, namely aforementioned SOX17 (Supplement Figure 1E), as well as NR2F2 (Supplement Figure 1F), an essential regulator of hormonal response, using our CUT&RUN data sets and published mouse uterine SOX17 and NR2F2 ChIP-seq data sets (GSE118328, GSE232583). Among the annotated genes, 5402 genes are shared between SMAD1/5 and SOX17, and 1922 genes are shared between SMAD1/5 and NR2F2. Such observations indicate a potential co-regulatory mechanism between SMAD1/5 and other key uterine transcription factors in maintaining appropriate uterine functions. Overall, our analyses demonstrate that the transcriptional activity of SMAD1, SMAD5, and PR coordinate the expression of key genes required for endometrial receptivity and decidualization.”

Reviewer #3 (Public Review):

Summary:

As SMAD1/5 activities have previously been indistinguishable, these studies provide a new mouse model to finally understand unique downstream activation of SMAD1/5 target genes, a model useful for many scientific fields. Using CUT&RUN analyses with gene overlap comparisons and signaling pathway analyses, specific targets for SMAD1 versus SMAD5 were compared, identified, and interpreted. These data validate previous findings showing strong evidence that SMADs directly govern critical genes required for endometrial receptivity and decidualization, including cell adhesion and vascular development. Further, SMAD targets were overlapped with progesterone receptor binding sites to identify regions of potential synergistic regulation of implantation. The authors report strong correlations between progesterone receptor and SMAD1/5 direct targets to cooperatively promote embryo implantation. Finally, the authors validated SMAD1/5 gene regulation in primary human endometrial stromal cells. These studies provide a data-rich survey of SMAD family transcription, defining its role as a governor of early pregnancy.

Strengths:

This manuscript provides a valuable survey of SMAD1/5 direct transcriptional events at the time of receptivity. As embryo implantation is controlled by extensive epithelial to stromal molecular crosstalk and hormonal regulation in space and time, the authors state a strong, descriptive narrative defining how SMAD1/5 plays a central role at the site of this molecular orchestration. The implementation of cutting-edge techniques and models and simple comparative analyses provide a straightforward, yet elegant manuscript.

Although the progesterone receptor exists as a major regulator of early pregnancy, the authors have demonstrated clear evidence that progesterone receptor with SMAD1/5 work in concert to molecularly regulate targets such as Sox17, Id2, Tgfbr2, Runx1, Foxo1 and more at embryo implantation. Additionally, the authors pinpoint other critical transcription factor motifs that work with SMADs and the progesterone receptor to promote early pregnancy transcriptional paradigms.

Weaknesses:

Although a wonderful new tool to ascertain SMAD1 versus SMAD5 downstream signaling, the importance of these factors in governing early pregnancy is not novel. Furthermore, functional validation studies are needed to confirm interactions at promoter regions. Addtionally, the authors presume that all overlapped genes are shared between progesterone receptor and SMAD1/5, yet some peak representations do not overlap. Although, transcriptional activation can occur at the same time, they may not occur in the same complex. Thus, further confirmation of these transcriptional events is warranted.

Thank you for the review; we appreciate these valuable comments. Although we used an overlap approach to investigate the gene regulatory networks between SMAD1/5 and PR at the gene level, we functionally validated the regulatory effect in an in vitro decidualization model using a qPCR approach. We acknowledge that gene activations may not occur at the exact same complex, but functional validation screenings at the promoter level are beyond the scope of the study. However, we added the discussion about the possibility of proposed investigations in Lines 553-558. Our current dataset and validation studies support our conclusions with robust evidence. Content from Lines 553-558 is copied below.

Lines 553-558: “In this study, we determined the overlapped transcriptional control between SMAD1/5 and PR at the gene level, and functionally validated the regulatory effect at the transcript level in a human stromal cell decidualization model. While we observe a subset of peak representations that do not overlap at the base pair level in the promoter regions, future functional screenings at the promoter level, such as luciferase reporter assays to assess transcriptional co-activation by SMAD1/5 and PR, will advance this study.”

• Since whole murine uterus was used for these studies, the specific functions of SMAD1/5 in the stroma versus the epithelium (versus the myometrium) remain unknown. Specific roles for SMAD1/5 in the uterine stroma and epithelial compartments still need to be examined. Also, further work is needed to delineate binding and transcriptional activation of SMAD1/5 and the progesterone receptor in stromal versus epithelial uterine compartments.

Thank you for the comments. Indeed, our study was performed in the whole mouse uterus, which includes stroma, epithelium and myometrium. Our previous data shows that nuclear SMAD1/5 are localized to both the stroma and epithelium in the decidua zone during the decidualization process at 4.5 dpc (PMID:34099644). Published in vivo studies also demonstrate the essential role of SMAD1/5 in the uterine epithelium and stroma compartments, respectively (PMIDs:35383354/27335065/17967875). Although we believe the binding/transcriptional activation of SMAD1/5 and PR occurs in both compartments based on the mouse phenotypic data, opportunities for further compartment-specific analysis were granted and discussion regarding such investigations was added (Lines 501-513). Content from Lines 501-513 is copied below.

Lines 501-513:

“Published studies have shown that nuclear SMAD1/5 localize to the stroma and epithelium during the decidualization process at 4.5dpc during the window of implantation. Conditional deletion of SMAD1/5 exclusively in the uterine epithelium using lactoferrin-icre (Ltf-icre) results in severe subfertility due to impaired implantation and decidual development. Conditional deletion of SMAD1/5/4 exclusively in the cells from mesenchymal lineage (including uterine stroma) using anti-Mullerian hormone type 2 receptor cre (Amhr2-cre) results in infertility with defective decidualization. Given the essential roles of SMAD1/5 in both stroma and epithelium identified by previous studies, we believe that transcriptional co-regulation by SMAD1/5 and PR reported here using the whole uterus validates a relationship between SMAD1/5 and PR in both the stromal and epithelial compartments. However, it does not rule out the potential coregulation of SMAD1/5 and PR in the myometrium, immune cells, and/or endothelium, given that whole uterus was used. The specific transcriptional evaluations of SMAD1/5 in the stroma versus the epithelium would require future single-cell sequencing (i.e., digital cytometry) and/or spatial transcriptomic analysis.”

• There are asynchronous gene responses in the SMAD1/5 ablated mouse model compared to the siRNA-treated human endometrial stromal cells. These differences can be confounding, and more clarity is required in understanding the meaning of these differences and as they relate to the entire SMAD transcriptome.

Thank you for the comments. From the mouse models with SMAD1/5 conditional deletions, we observed phenotypic defects at 4.5 dpc, which is the beginning of decidualization in the mouse. Our study used human endometrial stromal cells as a model to validate our findings functionally, aiming to mimic the specific time point during decidualization. Differences between the two models may arise from the strategy used to perturb SMAD1/5; in the mouse, a complete knockout of SMAD1/5 was used, resulting in failed decidualization, while the human endometrial stromal cells used an siRNA knockdown approach, which decreased the potential for decidualization. As such, this information needs to be considered when evaluating genome-wide effects on the transcriptome. We added a discussion of this point to Lines 564-572. Content from Lines 564-572 is copied below.

Lines 564-572:

“Since mice only undergo decidualization upon embryo implantation whilst human stromal cells undergo cyclic decidualization in each menstrual cycle in response to rising levels of progesterone, asynchronous gene responses may occur in comparison between mouse models and human cells. However, cellular transformation during decidualization is conserved between mice and humans, which makes findings in the mouse models a valuable and transferable resource to be evaluated in human tissues. Accordingly, our functional validation studies were performed using human endometrial stromal cells induced to decidualize in vitro for four days, which models the early phases of decidualization. Additional transcriptomic studies of the SMAD1/5 perturbations in human endometrial stromal cells will be of great resource in understanding the entire SMAD1/5 regulomes in humans.”

Reviewer #1 (Recommendations For The Authors):

• Minor grammatical errors requiring attention such as inserting punctuation at the end of sentences and including figure legends prior to the end of sentence punctuation.

Thanks for the comments. Additional proofreading was conducted for the revision.

Reviewer #2 (Recommendations For The Authors):

1) Between SMAD1 and SMAD5, does losing one SMAD affect the other SMAD's genome occupancy?

Thanks for the comments. Based on the mouse phenotypic data that conditional deletion of SMAD1 in the uterus does not affect female fertility, while conditional deletion of SMAD5 leads to subfertility, and conditional deletion of both SMAD1 and SMAD5 leads to complete infertility. We believe losing one SMAD will affect the other SMAD's genome occupancy. This point is discussed in Lines 514-517, with contents copied below.

Lines 514-517: “Although our studies herein confirm that SMAD1 and SMAD5 proteins have distinct transcriptional regulatory activities, our previous studies demonstrated that while SMAD5 can functionally replace SMAD1, SMAD1 cannot replace SMAD5 in the uterus. How this epistatic relationship is established in a tissue-specific manner still needs to be determined by further biochemical investigations.”

2) In light of SMAD1/5 and PGR co-occupied cis-acting elements and coregulating uterine transcriptome, does loss of SMAD1/5 alter the PGR and ESR1 genome occupancy?

Thanks for the comments. In the SMAD1/5 double conditional knockout mice, we observe the hyposensitivity towards progesterone and unopposed estrogen responses. We hypothesize that loss of SMAD1/5 alters PR genome occupancy and subsequently ER genome occupancy is altered as a secondary effect. To functionally address this question, genomic profiling studies need to be performed in the SMAD1/5 knockout mice, and, ideally, also performed in the PR knockout mice. However, such large-scale studies are beyond the scope of the current study and will not affect our conclusions under physiological conditions. We did include additional discussion regarding this comment in Lines 551-553, with the contents copied below.

Lines 551-553: “Profiling the PR genome occupancy in the SMAD1/5 deficient mice would provide an interesting perspective to reevaluate the major regulatory roles of SMAD1/5 in mediating uterine transcriptomes.”

3) In terms of investigating the impact of SAMD1/5 on cell type composition, perhaps the digital cytometry approach (e.g., PMID: 31061481) could provide unbiased inferences.

Thank you for the comments. We included expression analysis of a subset of SMAD1/5 direct target genes over different uterine compartments (Figure 4E). We also added the discussion of the opportunities for further compartment-specific analysis, including but not limited to the digital cytometry approach in Lines 506-513, with the contents copied below.

Line 506-513:

“Given the essential roles of SMAD1/5 in both stroma and epithelium identified by previous studies, we believe that the transcriptional co-regulatory roles of SMAD1/5 and PR reported here using the whole uterus validates a relationship between SMAD1/5 and PR in both the stromal and epithelial compartments. However, it does not rule out potential co-regulatory roles of SMAD1/5 and PR in the myometrium, immune cells, and/or endothelium, given that whole uterus was used. The specific transcriptional evaluations of SMAD1/5 in the stroma versus the epithelium would require future single-cell sequencing (i.e., digital cytometry) and/or spatial transcriptomic analysis.”

4) The limitation of focusing on the promoter occupied SMADs should be discussed.

Additional discussion of the limitation of focusing on the promoter regions was added in Lines 548-551, with contents copied below.

Lines 548-551:

“From pathway enrichment analysis, we demonstrate that genes with SMAD1/5 and PR bound at the promoter regions are enriched for key pathways in directing the decidualization process, such as WNT and relaxin signaling pathways. Future studies can benefit from analyzing binding events beyond the promoter regions.”

5) Methods: The reagent and the condition for PGR CUT&RUN is missing.

Information added in Line 153.

1. Line 260: Please clarify the statement of "suggesting the transcriptional of PR depends on BMP/SMAD1/5 signaling".

Thanks for the suggestion. The sentence was rephrased to (Lines 258-261) “Our previous studies revealed that conditional ablation of SMAD1 and SMAD5 in the uterus decreased P4 response during the peri-implantation period, suggesting that the transcriptional activities of PR depend on BMP/SMAD1/5 signaling.”

7) Line 280-289: This statement belongs to the discussion section.

The statement was moved as suggested.

8) Figure 4E is not cited in the result section.

Figure 4E was cited in the results section in the revised version. (Line 386)

9) Figures 3C, 3D, 3E, 3F, 5B and 5D: please include the full lists in the supplemental data so that labs with limited bioinformatic capabilities could use these findings to facilitate scientific discovery.

Data regarding the aforementioned figures were included in Supplement Tables 3-8 and Supplement Files 1-2.

10) Figure 2B and Figure 5A: the heatmaps without further grouping on common and distinct genome occupancy among assayed factors provided minimum useful information. Please reconsider the presentation format in order to deliver more meaningful results.

Figure 2B and Figure 5A were replotted with clustering using the k-means algorithm. Methods and legends were updated accordingly.

Reviewer #3 (Recommendations For The Authors):

To delineate specific roles for SMAD1/5 in the uterine stroma and epithelial compartments, methods such as single cell sequencing or spatial transcriptomic analysis may be warranted.

The manuscript now includes the discussion of future opportunities in investigating the roles of SMAD1/5 in different uterine compartments using single-cell sequencing and/or spatial transcriptomic analysis (Lines 498-513), with contents copied below.

Lines 498-513:

“Our studies also examined the role of SMAD1/5 in mediating progesterone responses at the genomic and transcription levels. Similarly, our analysis was based on data sets generated from the whole mouse uterus, which contains multiple compartments of the uterine structures, including but not limited to epithelium and stroma. Published studies have shown that nuclear SMAD1/5 localize to the stroma and epithelium during the decidualization process at 4.5 dpc, during the window of implantation. Conditional deletion of SMAD1/5 exclusively in the uterine epithelium using lactoferrin-icre (Ltf-icre) results in severe subfertility due to impaired implantation and decidual development. Conditional deletion of SMAD1/5/4 exclusively in the cells from mesenchymal lineage (including uterine stroma) using anti-Mullerian hormone type 2 receptor cre (Amhr2-cre) results in infertility with defective decidualization. Given the essential roles of SMAD1/5 in both stroma and epithelium identified by previous studies, we believe that the transcriptional co-regulatory roles of SMAD1/5 and PR reported here using the whole uterus validates a relationship between SMAD1/5 and PR in both the stromal and epithelial compartments. However, it does not rule out potential co-regulatory roles of SMAD1/5 and PR in the myometrium, immune cells, and/or endothelium, given that whole uterus was used. The specific transcriptional evaluations of SMAD1/5 in the stroma versus the epithelium would require future single-cell sequencing (i.e., digital cytometry) and/or spatial transcriptomic analysis.”

Author Response

We would like to thank the editor and the reviewers for their constructive comments and the chance to revise the manuscript. The suggestions have allowed us to improve our manuscript. We have been able to fulfil all reviewer comments and added new statistical analyses to examine associations for subsets of data. Whilst suggested by a reviewer, we did not perform large-scale experiments to confirm the viability of low sporozoite densities at different time-points post salivary gland colonization. For these assays there are currently no satisfactory in vitro models for sporozoites harvested from single mosquitoes and setting up and validating such experiments could be a PhD project in itself. We do consider this suggestion very relevant but beyond the scope of the current work.

Relevantly, during the time the manuscript was under review at eLife, we have been able to examine the multiplicity of infection in our field experiments. This was, as written in the original manuscript, a key reason to also perform experiments in the field where there is a greater diversity of parasite lines. We have successfully performed AMA-1 amplicon deep sequencing on infected mosquito salivary glands and infected skins. Although this does not change the key messages of the manuscript and is secondary to our main hypothesis, we do consider it a relevant addition since we were able to demonstrate that for some infected mosquitoes from the Burkina Faso study, multiple clones were expelled by mosquitoes during probing on a single piece of artificial skin. We have added a short paragraph to our revised manuscript and updated the acknowledgement section to include the supporting researcher who conducted those experiments.

Reviewer #1 (Public Review):

Summary: There is a long-believed dogma in the malaria field; a mosquito infected with a single oocyst is equally infectious to humans as another mosquito with many oocysts. This belief has been used for goal setting (and modelling) of malaria transmission-blocking interventions. While recent studies using rodent malaria suggest that the dogma may not be true, there was no such study with human P. falciparum parasites. In this study, the numbers of oocysts and sporozoite in the mosquitoes and the number of expelled sporozoites into artificial skin from the infected mosquito was quantified individually. There was a significant correlation between sporozoite burden in the mosquitoes and expelled sporozoites. In addition, this study showed that highly infected mosquitoes expelled sporozoites sooner.

Strengths:

• The study was conducted using two different parasite-mosquito combinations; one was lab-adapted parasites with Anopheles stephensi and the other was parasites, which were circulated in infected patients, with An. coluzzii. Both combinations showed statistically significant correlations between sporozoite burden in mosquitoes and the number of expelled sporozoites.

• Usually, this type of study has been done in group bases (e.g., count oocysts and sporozoites at different time points using different mosquitoes from the same group). However, this study determined the numbers in individual bases after multiple optimization and validation of the approach. This individual approach significantly increases the power of correlation analysis.

Weaknesses:

• In a natural setting, most mosquitoes have less than 5 oocysts. Thus, the conclusion is more convincing if the authors perform additional analysis for the key correlations (Fig 3C and 4D) excluding mosquitoes with very high total sporozoite load (e.g., more than 5-oocyst equivalent load).

In the revised manuscript, we have also performed our analysis including only the subset of mosquitoes with low oocyst burden. In our Burkina Faso experiments, where we could not control oocyst density, 48% (15/31) of skins were from mosquitoes with <5 oocyst sheets. Whilst low oocyst densities were thus not very uncommon, we acknowledge that this may have rendered some comparisons underpowered. At the same time, we observe a strong positive trend between oocyst density and sporozoite density and between salivary gland sporozoite density and mosquito inoculum. This makes it very likely that this trend is also present at lower oocyst densities, an association where sporozoite inoculation saturates at high densities is plausible and has been observed before for rodent malaria (DOI: 10.1371/journal.ppat.1008181) whilst we consider it less likely that sporozoite expelling would be more efficient at low (unmeasured) sporozoite densities.

• As written as the second limitation of the study, this study did not investigate whether all expelled sporozoites were equally infectious. For example, Day 9 expelled sporozoites may be less infectious than Day 11 sporozoites, or expelled sporozoites from high-burden mosquitoes may be less infectious because they experience low nutrient conditions in a mosquito. Ideally, it is nice to test the infectivity by ex vivo assays, such as hepatocyte invasion assay, and gliding assay at least for salivary sporozoites. But are there any preceding studies where the infectivity of sporozoites from different conditions was evaluated? Citing such studies would strengthen the argument.

We appreciate this thought and can see the value of these experiments. We are not aware of any studies that examined sporozoite viability in relation to the day of salivary gland colonization or sporozoite density.

One previous study assessed the NF54 sporozoite infectivity on different days post infection (days 12-13-14-15-16-18) and observed no clear differences in ‘per sporozoite hepatocyte invasion capacity’ over this period (DOI: 10.1111/cmi.12745). We nevertheless agree that it is conceivable that sporozoites require maturation in the salivary glands and might not all be equally infectious. While hepatocyte invasion experiments are conducted with bulk harvesting of all the sporozoites that are present in the salivary glands, it would even be more interesting to assess the invasion capacity of the smaller population of sporozoites that migrate to the proboscis to be expelled. This would, as the reviewer will appreciate, be a major endeavour. To do this well the expelled sporozoites would need to be harvested from the salivary glands/proboscis and used in the best and most natural environment for invasion. The suggested work would thus depend on the availability of primary hepatocytes since conventional cell-lines like HC-04 are likely to underestimate sporozoite invasion. Importantly, there are currently no opportunities to include the barrier of the skin environment in invasion assays whilst this may be highly important in determining the likelihood that sporozoites manage to achieve invasion and give rise to secondary infections. In short, we agree with the reviewer that these experiments are of interest but consider these well beyond the scope of the current work. We have added a section to the Discussion section to highlight these future avenues for research. ‘Of note, our assessments of EIP and of sporozoite expelling did not confirm the viability of sporozoites. Whilst the infectivity of sporozoites at different time-points post infection has been examine previously (https://doi.org/10.1111/cmi.12745), these experiments have never been conducted with individual mosquito salivary glands. To add to this complexity, such experiments would ideally retain the skin barrier that may be a relevant determinant for invasion capacity and primary hepatocytes.’

• Since correlation analyses are the main points of this paper, it is important to show 95% CI of Spearman rank coefficient (not only p-value). By doing so, readers will understand the strengths/weaknesses of the correlations. The p-value only shows whether the observed correlation is significantly different from no correlation or not. In other words, if there are many data points, the p-value could be very small even if the correlation is weak.

We appreciate this comment and agree that this is indeed insightful. We have added the 95% confidence intervals to all figure legends and main text. We also provide them below.

Fig 3b: 95% CI: 0.74, 0.85

Fig 3c: 95% CI: 0.17, 0.50

Fig 4c: 95% CI: 0.80, 0.95

Fig 4d: 95% CI: 0.52, 0.82

Supp Fig 5a: 95% CI: 0.74, 0.85

Supp Fig 5b: 95% CI: 0.73, 0.93

Supp Fig 6: 95% CI: 0.11, 0.48

Supp Fig 7: 95% CI: -0.12, 0.16

Reviewer #2 (Public Review):

Summary: The malaria parasite Plasmodium develops into oocysts and sporozoites inside Anopheles mosquitoes, in a process called sporogony. Sporozoites invade the insect salivary glands in order to be transmitted during a blood meal. An important question regarding malaria transmission is whether all mosquitoes harbouring Plasmodium parasites are equally infectious. In this paper, the authors investigated the progression of P. falciparum sporozoite development in Anopheles mosquitoes, using a sensitive qPCR method to quantify sporozoites and an artificial skin system to probe for parasite expelling. They assessed the association between oocyst burden, salivary gland infection intensity, and sporozoites expelled.

The data show that higher sporozoite loads are associated with earlier colonization of salivary glands and a higher prevalence of sporozoite-positive salivary glands and that higher salivary gland sporozoite burdens are associated with higher numbers of expelled sporozoites. Intriguingly, there is no clear association between salivary gland burdens and the prevalence of expelling, suggesting that most infections reach a sufficient threshold to allow parasite expelling during a mosquito bite. This important observation suggests that low-density gametocyte carriers, although less likely to infect mosquitoes, could nevertheless contribute to malaria transmission.

Strengths: The paper is well written and the work is well conducted. The authors used two experimental models, one using cultured P. falciparum gametocytes and An. stephensi mosquitoes, and the other one using natural gametocyte infections in a field setup with An. coluzzii mosquitoes. Both studies gave similar results, reinforcing the validity of the observations. Parasite quantification relies on a robust and sensitive qPCR method, and parasite expelling was assessed using an innovative experimental setup based on artificial skin.

Weaknesses: There is no clear association between the prevalence of sporozoite expelling and the parasite burden. However, high total sporozoite burdens are associated with earlier and more efficient colonization of the salivary glands, and higher salivary gland burdens are associated with higher numbers of expelled sporozoites. While these observations suggest that highly infected mosquitoes could transmit/expel parasites earlier, this is not directly addressed in the study. In addition, whether all expelled sporozoites are equally infectious is unknown. The central question, i.e. whether all infected mosquitoes are equally infectious, therefore remains open.

We agree that the manuscript provides important steps forward in our understanding of what makes an infectious mosquito but does not conclusively demonstrate that highly infected mosquitoes are more likely to initiate a secondary infection. We consider this to be beyond the scope of the current work although the current work lays the foundation for these important future studies. For human Plasmodium infections the most satisfactory answer on the infectiousness of low versus high infected mosquitoes comes from controlled human infection models. In response to reviewer comments, we have extended our Discussion section to highlight this importance. To accommodate the (very fair) reviewer comments, we have avoided any phrasings that suggest that our findings demonstrate differences in transmission.

Reviewer #3 (Public Review):

Summary: This study uses a state-of-the-art artificial skin assay to determine the quantity of P. falciparum sporozoites expelled during feeding using mosquito infection (by standardised membrane feeding assay SMFA) using both cultured gametocytes and natural infection. Sporozoite densities in salivary glands and expelled into the skin are quantified using a well-validated molecular assay. These studies show clear positive correlations between mosquito infection levels (as determined by oocyst numbers), sporozoite numbers in salivary glands, and sporozoites expelled during feeding. This indicates potentially significant heterogeneity in infectiousness between mosquitoes with different infection loads and thus challenges the often-made assumption that all infected mosquitoes are equally infectious.

Strengths: Very rigorously designed studies using very well validated, state-of-the-art methods for studying malaria infections in the mosquito and quantifying load of expelled sporozoites. This resulted in very high-quality data that was well-analyzed and presented. Both sources of gametocytes (cultures vs. natural infection) show consistent results further strengthening the quality of the results obtained.

Weaknesses: As is generally the case when using SMFAs, the mosquito infections levels are often relatively high compared to wild-caught mosquitoes (e.g. Bombard et al 2020 IJP: median 3-4 ), and the strength of the observed correlations between oocyst sheet and salivary gland sporozoite load even more so between salivary gland sporozoite load and expelled sporozoite number may be dominated by results from mosquitoes with infection levels rarely observed in wild-caught mosquitoes. This could result in an overestimation of the importance of these well-observed positive relationships under natural transmission conditions. The results obtained from these excellently designed and executed studies very well supported their conclusion - with a slight caveat regarding their application to natural transmission scenarios

For efficiency and financial reasons, we have worked with an approach to enhance mosquito infection rates. If we had worked with gametocytes at physiological concentrations and a small number of donors, we probably have had considerably lower mosquito infection rates. Whilst this would indeed result in lower infection burdens in the sparse infected mosquitoes, addressing the reviewer concern, it would have made the experiments highly inefficient and expensive. The skin mimic was initially provided free of charge when the matrix was close to the expiry date but for the experiments in Burkina Faso we had to purchase the product at market value. Whilst we consider the biological question sufficiently important to justify this investment – and think our findings prove us right – it remained important to avoid using skins for uninfected mosquitoes. Since oocyst prevalence and density are strongly correlated (doi: 10.1016/j.ijpara.2012.09.002; doi: 10.7554/eLife.34463), a low oocyst density in natural infections typically coincides with a high proportion of negative mosquitoes.

Of note, our approach did result in the inclusion of 15 skins from infected mosquitoes with 1-4 oocysts. This number may be modest but we did include observations from this low oocyst range which is, we agree, highly important for better understanding malaria epidemiology.

This work very convincingly highlights the potential for significant heterogeneity in the infectiousness between individual P. falciparum-infected mosquitoes. Such heterogeneity needs to be further investigated and if again confirmed taken into account both when modelling malaria transmission and when evaluating the importance of low-density infections in sustaining malaria transmission.

Reviewer #4 (Public Review):

Summary: The study compares the number of sporozoites expelled by mosquitoes with different Plasmodium infection burden. To my knowledge this is the first report comparing the number of expelled P. falciparum sporozoites and their relation to oocyst burden (intact and ruptured) and residual sporozoites in salivary glands. The study provides important evidence on malaria transmission biology although conclusions cannot be drawn on direct impact on transmission.

Strengths: Although there is some evidence from malaria challenge studies that the burden of sporozoites injected into a host is directly correlated with the likelihood of infection, this has been done using experimental infection models which administer sporozoites intravenously. It is unclear whether the same correlation occurs with natural infections and what the actual threshold for infection may be. Host immunity and other host related factors also play a critical role in transmission and need to be taken into consideration; these have not been mentioned by the authors. This is of particular importance as host immunity is decreasing with reduction in transmission intensity.

Weaknesses: The natural infections reported in the study were not natural as the authors described. Gametocyte enrichment was done to attain high oocyst infection numbers. Studying natural infections would have been better without the enrichment step. The infected mosquitoes have much larger infection burden than what occurs in the wild.

Nevertheless, the findings support the same results as in the experiments conducted in the Netherlands and therefore are of interest. I suggest the authors change the wording. Rather than calling these "natural" infections, they could be called, for example, "experimental infections with wild parasite strains".

We have addressed these concerns and, in the process, also changed our manuscript title. The following sentences have been changed:

“It is currently unknown whether all Plasmodium falciparum infected mosquitoes are equally infectious. We assessed sporogonic development using cultured gametocytes in the Netherlands and natural infections in Burkina Faso”.

Now reads: “It is currently unknown whether all Plasmodium falciparum infected mosquitoes are equally infectious. We assessed sporogonic development using cultured gametocytes in the Netherlands and experimental infections with naturally circulating parasite strains in Burkina Faso”. 226-228 “Experimental infections with naturally circulating parasite strains show comparable correlation between oocyst density, salivary gland density and sporozoite inoculum”.

Has now replaced the original phrasing: “Natural infected mosquitoes by gametocyte carriers in Burkina Faso show comparable correlation between oocyst density, salivary gland density and sporozoite inoculum”.

I do not believe the study results generate sufficient evidence to conclude that lower infection burden in mosquitoes is likely to result in changes to transmission potential in the field. In study limitations section, the authors say "In addition, our quantification of sporozoite inoculum size is informative for comparisons between groups of high and low-infected mosquitoes but does not provide conclusive evidence on the likelihood of achieving secondary infections. Given striking differences in sporozoite burden between different Plasmodium species - low sporozoite densities appear considerably more common in mosquitoes infected with P. yoelii and P. berghei the association between sporozoite inoculum and the likelihood of achieving secondary infections may be best examined in controlled human infection studies. However, in the abstract conclusion the authors state "Whilst sporozoite expelling was regularly observed from mosquitoes with low infection burdens, our findings indicate that mosquito infection burden is associated with the number of expelled sporozoites and may need to be considered in estimations of transmission potential." Kindly consider ending the sentence at "expelled sporozoites." Future studies on CHMI can be recommended as a conclusion if authors feel fit.

We agree that we need to be very cautious with conclusions on the impact of our findings for the infectious reservoir. We have rephrased parts of our abstract and have updated the Discussion section following the reviewer suggestions. We agree with the reviewer that CHMI studies are recommended and have expanded the Discussion section to make this clearer. The sentence in the abstract now ends as:

"Whilst sporozoite expelling was regularly observed from mosquitoes with low infection burdens, our findings indicate that mosquito infection burden is associated with the number of expelled sporozoites. Future work is required to determine the direct implications of these findings for transmission potential."

Reviewer #1 (Recommendations For The Authors):

• Prevalence data shown in Fig 2A and Table S1 are different. For example, >50K at Day 11, Fig 2A shows ~85% prevalence, but Table S1 says 100%. If the prevalence in Table S1 shows a proportion of observations with positive expelled sporozoites (instead of a proportion of positive mosquitoes shown in Fig 2A), then the prevalence for <1K at Day 11 cannot be 6.7% (either 0 or 20% as there were a total of 5 observations). So in either case, it is not clear why the numbers shown in Fig 2A and Table S1 are different.

Figure 2A and Table S2 are estimated prevalence and odds ratios from an additive logistic regression model (i.e. excluding the interaction between day and sporozoite categories). Table S1 includes this interaction when estimating prevalence and odds ratios and as we can see some categories in the interaction were extremely small resulting in blown up confidence intervals especially in day 11. So Table S1 and Fig 2A are the results from two different models. Whilst our results are thus correct, we can understand the confusion and have added a sentence to explain the model used in the figure/table legends.

Figure. 2 Extrinsic Incubation Period in high versus low infected mosquitoes. A. Total sporozoites (SPZ) per mosquito in body plus salivary glands (x-axis) were binned by infection load <1k; 1k-10k; 10k-50k; >50k and plotted against the proportion of mosquitoes (%) that were sporozoite positive (y-axis) as estimated from an additive logistic regression model with factors day and SPZ categories. Supplementary Table S1. The extrinsic incubation period of P. falciparum in An. stephensi estimated by quantification of sporozoites on day 9, 10, 11 by qPCR. Based on infection intensity mosquitoes were binned into four categories (<1k, 1k-10k, 10k-50k, >50) that was assessed by combining sporozoite densities in the mosquito body and salivary gland. Prevalences and odds ratios were estimated from a logistic regression model with factors day, SPZ category and their interaction.

There are 3 typos in the paper. Please fix them.

Line 464; ...were counted using a using an incident....

Line 473; Supplementary Figure 7 should be Fig S8.

Line 508: ...between days 9 and 10 using a (t=-2.0467)....

We appreciate the rigour in reviewing our text and have corrected all typos.

Reviewer #2 (Recommendations For The Authors):

High infection burdens may result in earlier expelling capacity in mosquitoes, which would reflect more accurately the EIP. The fact that earlier colonization of SG and correlation between SG burden and numbers expelled suggest it could be the case, but it would be interesting to directly measure the prevalence of expelling over time to directly assess the effect of the sporozoite burden (not just at day 15 but before). This could reveal how the parasite burden in mosquitoes is a determinant of transmission.

We appreciate this suggestion and will consider this for future experiments. It adds another variable that is highly relevant but will also complicate comparisons where sporozoite expelling is related to both time since infectious blood meal and salivary gland sporozoite density (that is also dependent on time since infectious bloodmeal). Moreover, we then consider it important to measure this over the entire duration of sporozoite expelling, including late time-points post infectious bloodmeal. This may form part of a follow-up study.

Another question is whether all sporozoites (among expelled parasites) are equally infective, i.e. susceptible to induce secondary infection. If not, this could reconcile the data of this study and previous results in the rodent model where high burdens were associated with an increased probability to transmit.

As also indicated above, we are aware of a single study that assessed NF54 sporozoite infectivity on different days post infection (days 12-13-14-15-16-18) and observed no clear differences in ‘per sporozoite hepatocyte invasion capacity’ over this period (DOI: 10.1111/cmi.12745). We nevertheless agree that it is conceivable that sporozoites require maturation in the salivary glands and might not all be equally infectious. While hepatocyte invasion experiments are conducted with bulk harvesting of all the sporozoites that are present in the salivary glands, it would even be more interesting to assess the invasion capacity of the smaller population of sporozoites that migrate to the proboscis to be expelled. This would, as the reviewer will appreciate, be a major endeavour. To do this well the expelled sporozoites would need to be harvested from the salivary glands/proboscis and used in the best and most natural environment for invasion. The suggested work would thus depend on the availability of primary hepatocytes since conventional cell-lines like HC-04 are likely to underestimate sporozoite invasion. Importantly, there are currently no opportunities to include the barrier of the skin environment in invasion assays whilst this may be highly important in determining the likelihood that sporozoites manage to achieve invasion and give rise to secondary infections. In short, we agree with the reviewer that these experiments are of interest but consider these well beyond the scope of the current work. We have added a section to the Discussion section to highlight these future avenues for research. ‘Of note, our assessments of EIP and of sporozoite expelling did not confirm the viability of sporozoites. Whilst the infectivity of sporozoites at different time-points post infection has been examine previously (ref), these experiments have never been conducted with individual mosquito salivary glands. To add to this complexity, such experiments would ideally retain the skin barrier that may be a relevant determinant for invasion capacity and primary hepatocytes.’

The authors evaluated oocyst rupture at day 18, i.e. 3 days after feeding experiments (performed at day 15). Did they check in control experiments that the prevalence of rupture oocysts does not vary between day 15 and day 18?

We did not do this and consider it very unlikely that there is a noticeable increase in the number of ruptured oocysts between days 15 and 18. We observe that salivary gland invasion plateaus around day 12 and the provision of a second bloodmeal that is known to accelerate oocyst maturation and rupture (doi: 10.1371/journal.ppat.1009131) makes it even less likely that a relevant fraction of oocysts ruptures very late. Perhaps most compellingly, the time of oocyst rupture will depend on nutrient availability and rupture could thus occur later for oocysts from a heavily infected gut compared to oocysts from mosquitoes with a low infection burden. We observe a very strong association between salivary gland sporozoite density (day 15) and oocyst density (assessed at day 18) without any evidence for change in the number of sporozoites per oocyst for different oocyst densities. In our revised manuscript we have also assessed correlations for different ranges of oocyst intensities and see highly consistent correlation coefficients and find no evidence for a change in ‘slope’. If oocyst rupture would regularly happen between days 15 and 18 and this late rupture would be more common in heavily infected mosquitoes, we would expect this to affect the associations presented in figures 3B and 4C This is not the case.

The authors report higher sporozoite numbers per oocyst and a higher proportion of SG invasion as compared to previous studies (30-50% rather than 20%). How do they explain these differences? Is it due to the detection method and/or second blood meal? Or parasite species?

We were also intrigued by these findings in light of existing literature. To address potential discrepancies, it is indeed possible that the 2nd bloodmeal made a difference. In addition, NF54 is known to be a highly efficient parasite in terms of gametocyte formation and transmission. And there are marked differences in these performances between NF54 isolates and definitely between NF54 and its clone 3D7 that is regularly used. We also used a molecular assay to detect and quantify sporozoites but consider it less likely that this is a major factor in terms of explaining SG invasion since sporozoite densities were typically within the range that would be detected by microscopy. We can only hypothesize that the 2nd bloodmeal may have contributed to these findings and acknowledge this in the revised Discussion section.

The median numbers of expelled sporozoites seem to be higher in the natural gametocyte infection experiments as compared to the cultures. Is it due to the mosquito species (An. coluzzii versus An. stephensi?).

The added value of our field experiments, a more relevant mosquito species and more relevant parasite isolates, is also a weakness in terms of understanding possible differences between in vitro experiments and field experiments with naturally circulating parasite strains. We only conclude that our in vitro experiments do not over-estimate sporozoite expelling by using a highly receptive mosquito source and artificially high gametocyte densities. We have clarified this in the revised Discussion.

39% of sporozoite-positive mosquitoes failed to expel, irrespective of infection densities. Could the authors discuss possible explanations for this observation?

In paragraph 304-307 we now write that:” This finding broadly aligns with an earlier study of Medica and Sinnis that reported that 22% of P. yoelii infected mosquitoes failed to expel sporozoites. For highly infected mosquitoes, this inefficient expelling has been related to a decrease of apyrase in the mosquito saliva”.

In Figure 3, it would be interesting to zoom in the 0-1k window, below the apparent threshold for successful expelling.

We have generated correlation estimates for different ranges of oocyst and sporozoite densities and added these in Supplementary Table 5. We agree that this helps the reader to appreciate the contribution of different ranges of parasite burden to the observed associations.

In Fig S8. Did they observe intact oocysts with fixed samples? These could be shown as well in the figure.

We have incorporated this comment. An intact oocyst from fixed samples was now added to Fig S10.

Minor points

-line 119: LOD and LOQ could be defined here.

We agree that this should have been defined. We changed line 119 to explain LOD and LOQ to: …“the limit of detection (LOD) and limit of quantification (LOQ)”….

• line 126: the title does not reflect the content of this paragraph.

We have changed the title: “Immunolabeling allows quantification of ruptured oocysts ”into: A comparative analysis of oocyst densities using mercurochrome staining and anti-CSP immunostaining.

-line 269: infectivity is not appropriate. The data show colonization of SG.

Line 269: infectivity has been changed with colonization of salivary glands.

There seems to be a problem with Fig S6. The graph seems to be the same as Fig 3C. Please check whether the graph and legends are correct.

Supplementary Figure 6 shows the sporozoite expelling density in relation to infection burden with a threshold set at > 20 sporozoites while Fig 3C shows the total sporozoite density (residual salivary gland sporozoites + sporozoites expelled, X-axis) in relation to the number of expelled sporozoites (Y-axis) by COX-1qPCR without any threshold density. We have explained this in more detail in the revised supplemental figure where we now state

“Of note, this figure differs from Figure 3C in the main text in the following manner. This figure presents sporozoite expelling density in relation to infection burden with a threshold set at > 20 sporozoites to conclude sporozoite positivity while Figure 3C shows the total sporozoite density (residual salivary gland sporozoites + sporozoites expelled, X-axis) in relation to the number of expelled sporozoites (Y-axis) by COX-1 qPCR without any threshold density and thus includes all observations with a qPCR signal”

Reviewer #3 (Recommendations For The Authors):

Congratulations to the authors for the really excellently designed and rigorously conducted studies.

My main concern is in regards to the relatively high oocyst numbers in their experimental mosquitoes (from both sources of gametocytes) compared to what has been reported from wild-caught mosquitoes in previous studies in Burkina Faso.

We have addressed this concern above. For completeness, we include the main points here again. We enriched gametocytes for efficiency reasons, experiments on gametocytes at physiological concentrations would have resulted in a lower oocyst density (and thus more ‘natural’ although a minority of individuals achieves very high oocyst densities in all studies that included a broad range of oocyst densities (e.g. doi: 10.1016/j.exppara.2014.12.010; doi: 10.1016/S1473-3099(18)30044-6). Of note, we did include 15 skins from low oocyst densities (1-4 oocysts). Whilst low oocyst densities were thus not very uncommon in our sample set, we acknowledge that this may have rendered some comparisons underpowered. At the same time, we observe a strong positive trend between oocyst density and sporozoite density and between salivary gland sporozoite density and mosquito inoculum. This makes it very likely that this trend is also present at lower oocyst densities, an association where sporozoite inoculation saturates at high densities is plausible and has been observed before for rodent malaria (DOI: 10.1371/journal.ppat.1008181) whilst we consider it less likely that sporozoite expelling would be more efficient at low (unmeasured) sporozoite densities. In the revised manuscript we have also performed our analysis including only the subset of mosquitoes with low oocyst burden.

The best way to address this would be to do comparable artificial skin-feeding experiments on such wild-caught mosquitoes, but I appreciate that this is very difficult to do.

This would indeed by difficult to do. Mostly because infection status can only be examined post-hoc and it is likely that >95% of mosquitoes are sporozoite negative at the moment experiments are conducted (in many settings this will even be >99%). Importantly, also in wild-caught mosquitoes very high oocyst burdens are observed in a small but relevant subset of mosquitoes (doi: 10.1016/j.ijpara.2020.05.012).

Instead, I would suggest the authors conduct addition analysis of their data using different cut-offs for maximum oocyst numbers (e.g. <5, <10, <20) to determine if these correlations hold across the entire range of observed oocyst sheets and salivary gland sporozoite load.

We have provided these calculations for the proposed range of oocyst numbers. In addition, we also provided them for a range of sporozoite densities. These findings are now provided in

Entire range of observed oocyst sheets and salivary gland sporozoite load. A minor point on the regression lines in Figures 3 & 4: both variables in these plots have inherent variation (measurement & natural), but regression techniques such as reduced major exit regression (MAR) that allow error in both x and y variables may be preferable to a standard lines regression. Also, as it is implausible that mosquitoes with zero sporozoite in salivary glands expel several hundred sporozoites at feeding, the regression should probably also be constrained to pass through the 0,0 point.

Since the main priority of the analyses is the correlation, and not the fit of the regression line – which is only for indication, and also because of the availability of software, we did not change the type of regression. We have however added a disclaimer to the legend, and we have also forced the intercept to 0 – which does indeed better reflect the biological association. Additionally we added 95% confidence intervals to all Spearman’s correlation coefficients in the legends.

Author Response

Reviewer #1 (Public Review):

The authors propose a hypothesis for ovarian carcinogenesis based on epidemiological data, and more specifically they suggest that the latter relates to ascending genital tract "infection" or "dysbiosis", the resulting fallopian tube inflammation ultimately predisposing to ovarian cancer.

While this hypothesis would ideally be addressed in a longitudinal set-up with repeated female genital tract sampling, such an approach is obviously hard to realize. Rather, the authors present this hypothesis as a rationale for a cross-sectional study involving 81 patients with ovarian cancer (most with the most common subtype of high grade serous ovarian carcinoma, though other subtypes were also included), as well as 106 control patients with various non-infectious conditions including endometriosis and benign ovarian cysts. In all patients was there a comprehensive microbiome sampling of ovarian surface/fallopian tube, cervix and peritoneal cavity as well sampling of a number of potential sources of contamination, including surgery sites, ambient environment, consumables used in the DNA extraction and sequencing pipeline, etc. In line with the hypothesis presented at the outset, species with a threshold of at least 100 reads in both at least one cervical and at least one fallopian tube sample, while absent from environmental swabs, were considered relevant to the postulated pathway.

Remarkably, fallopian tube microbiota in ovarian cancer patients tended to cluster more closely to those retrieved from the paracolic gutter, than fallopian tube microbiota in non-cancer controls, which showed more relative similarity to vaginal/genital tract microbiota.

Although not really addressed by the authors, there also seem to be quite a few differences, at least in terms of abundance, in cervical microbiota between ovarian cancer patients and controls as well, which is an interesting finding, even when accounting for differences in age distribution between ovarian cancer patients and included control patients.

Overall, very few data are available thus far on the upper genital tract/fallopian tube microbiome, while also invariably controversial, as it has proven extremely difficult to obtain pelvic samples in a valid, "sterile" manner, i.e. without affecting a resident low-biomass microbiome to be analyzed. The authors took a number of measures to counter so, and in this respect, this is likely the largest and most valid study on the subject, even though biases and contamination can never be completely excluded in this context.

As such, I believe the strength of this study and paper primarily relates to the rigour of the methodology, thereby giving us a valuable insight in the presumed fallopian tube/ovarian surface microbiome, which may definitely serve as an impetus and a reference to future translational ovarian cancer research, or ovarian microbiome research for that matter.

I believe that the authors should acknowledge in more detail, that the data obtained from their cross-sectional study, valid as these are, do not provide any direct support to the hypothesis - albeit also plausible - set forth, a discussion that I somehow missed to a certain extent. It is important to realize in this and related contexts that neoplasia may well induce microbiome alterations through a variety of mechanisms, hence microbiome alterations not per se being causative. Conclusions should therefore be more reserved. Along the same lines, potential biases introduced through the selection of control patients (some detail here would be insightful) also deserves some discussion, as it is not known, whether other conditions such as benign ovarian cysts or endometriosis have some relationship with the human microbiome, be it causative or 'reversely causative', see for instance very recent work in Science Translational Medicine.

We appreciate the reviewer’s detailed review and thoughtful comments. We have added the following sentences in the Discussion to address the reviewer’s concern: “Due to the cross-sectional nature of the study, we have limited ability to link specific bacteria to ovarian carcinogenesis, as we would need to demonstrate that exposure to bacteria precedes the cancer. However, identifying associations between FT microbiota and OC is a critical first step. Further investigations, especially backed by in vitro studies, are needed to test our initial hypotheses.”

Reviewer #2 (Public Review):

The authors aimed to investigate the microbiota present in the fallopian tubes (FT) and its potential association with ovarian cancer (OC). They collected swabs intraoperatively from the FT and other surgical sites as controls to profile the FT microbiota and assess its relationship with OC.

They observed a clear shift in the FT microbiota of OC patients compared to non-cancer patients. Specifically, the FT of OC patients had more types of bacteria typically found in the gastrointestinal tract and the mouth. In contrast, vaginal bacterial species were more prevalent in non-cancer patients. Serous carcinoma, the most common OC subtype, showed a higher prevalence of almost all FT bacterial species compared to other OC subtypes.

The strengths of the study include its large sample size, rigorous collection methods, and use of controls to identify the possible contaminants. Additionally, the study employed advanced sequencing techniques for microbiota analysis. However, there are some weaknesses to consider. The study relied on swabs collected intraoperatively, which may not fully represent the microbiota in the FT during normal physiological conditions. The study also did not establish causality between the identified bacteria and OC but rather demonstrated an association. Regardless, the findings are important and these questions need to be addressed by future studies. A few additions in data representation and analysis are instead recommended.

Overall, the authors achieved their aims of identifying the FT microbiota and assessing its relationship with OC. The results support the conclusion that there is a clear shift in the FT microbiota in OC patients, paving the way for further investigations into the role of these bacteria in the pathogenesis of ovarian cancer.

The identification of specific bacterial species associated with OC could contribute to the development of novel diagnostic and therapeutic approaches. The study design and the data generated here can be valuable to the research community studying the microbiota and its impact on cancer development. However, further research is needed to validate these findings and elucidate the underlying mechanisms linking the FT microbiota shift and OC.

We appreciate the reviewer’s detailed review and positive comments.

Reviewer #3 (Public Review):

The findings of Bo Yu and colleagues titled "Identification of fallopian tube microbiota and its association with ovarian cancer: a prospective study of intraoperative swab collections from 187 patients" describes the identification of the fallopian tube microbiome and relationship with ovarian cancer. The studies are highly rigorous obtaining specimens from the fallopian tube, ovarian surfaces, paracolic gutter of patients of known or suspected ovarian cancer or benign tumor patients. The investigators took great care to ensure there was no or limited contamination including test the surgical suite air, as the test locations are from low abundance microbiota. The findings provide evidence that the microbiota in the fallopian tube, especially in ovarian cancer has similarities to gut microbial communities. This is a potentially novel observation.

The studies investigate the microbiome of >1000 swabs from 81 ovarian cancer and 106 non-cancer patients. The sites collected are low biomass microbiota making the study particularly challenging. The studies provide descriptive evidence that the ovarian cancer fallopian tube microbiota contain species that are similar to the gut microbiota. In contrast the fallopian tube microbiota of non-cancer patients that exhibit more similarity to the uterine/cervical microbiota. This may be a relevant observation but is highly descriptive with limited insights on the functional relevance.

The data indicate the presence of low biomass FT microbiota. The findings support the existence of FT microbiota in ovarian cancer that appears to be related to gut microbial species. While interesting, there is no insights on how and why these microbial species are found in the FT. The studies only identify the species but there is no transcriptomic analysis to provide an indication on whether the bacteria are activating DNA damage pathways. This is an interesting observation that requires more insights to address how these bacteria reach the fallopian tube and a related question is whether these bacteria are found in the peritoneum.

An additional concern is whether these data can be used to develop biomarkers of disease and early detection of disease. can the investigators detect the ovarian cancer FT microbiota in cervical/vaginal secretions? That may yield more significant insights for the field.

We appreciate the reviewer’s detailed review and thoughtful comments. We have added the following sentences in the Discussion to acknowledge the reviewer’s concern: “Due to the cross-sectional nature of the study, we have limited ability to link specific bacteria to ovarian carcinogenesis, as we would need to demonstrate that exposure to bacteria precedes the cancer. However, identifying associations between FT microbiota and OC is a critical first step. Further investigations, especially backed by in vitro studies, are needed to test our initial hypotheses.”

Reviewer #1 (Recommendations For The Authors):

I have no additional comments here.

Reviewer #2 (Recommendations For The Authors):

The data analysis and data representation could be improved by the following points:

1. To compare the microbiota and assess the overall microbiota structure difference between the cancer vs non cancer cohort alpha- and beta-diversity of the microbial communities can be conducted.

2. A differential abundance analysis could also be conducted to assess the differences at the genera and taxa level between the cancer vs non cancer cohorts.

3. The analysis suggested above can also be conducted in the serous vs non serous cancer cohorts.

4. In Figure 4 and 5 it would be more intuitive to show the predominant niche of each bacterium by color coding

We appreciate these helpful suggestions from the reviewer. We have added Figure 2B to address the diversity as well as the differences between cancer versus non-cancer cohorts. We have added in the Results section the description of our findings in Figure 2B. We have added color coding to Figure 4 and 5 as the reviewer suggested.

Reviewer #3 (Recommendations For The Authors):

These studies are interesting but are very descriptive with no obvious approaches for understanding the mechanisms of FT microbiota in ovarian cancer. The identification of these bacteria is not sufficient to draw implications on their impact on ovarian cancer development or progression. This needs to be addressed.

We agree with the reviewer and have added the following sentences in the Discussion to acknowledge the reviewer’s concern: “Due to the cross-sectional nature of the study, we have limited ability to link specific bacteria to ovarian carcinogenesis, as we would need to demonstrate that exposure to bacteria precedes the cancer. However, identifying associations between FT microbiota and OC is a critical first step. Further investigations, especially backed by in vitro studies, are needed to test our initial hypotheses.”

Author Response

Responses to public reviews

Reviewer 1

We thank the reviewer for the valuable and constructive comments and are pleased that the re-viewer finds our study timely and our behavioral results clear.

1) The RSA basically asks on the lowest level, whether neural activation patterns (as measured by EEG) are more similar between linked events compared to non-linked events. At least this is the first question that should be asked. However, on page 11 the authors state: "We ex-amined insight-induced effects on neural representations for linked events [...]". Hence, the critical analysis reported in the manuscript fully ignores the non-linked events and their neu-ral activation patterns. However, the non-linked events are a critical control. If the reported effects do not differ between linked and non-linked events, there is no way to claim that the effects are due to experimental manipulation - neither imagination nor observation. Hence, instead of immediately reporting on group differences (sham vs. control) in a two-way in-teraction (pre vs. post X imagination vs. observation), the authors should check (and re-port) first, whether the critical experimental manipulation had any effect on the similarity of neural activation patterns in the first place.

We completely agree that the non-link items are a critical control. Therefore, we had reported not only the results for linked but also for non-linked events on page 15, lines 336-350. We clarified this important point now on page 12 lines 283-286:

“Subsequently, we examined insight-induced effects on neural representations for linked (vs. non-linked) events by comparing the change from pre- to post-insight (post-pre) and the difference between imagination and observation (imagination - observation) between cTBS and sham groups using an independent cluster-based permutation t-test.”

Moreover, to directly compare linked and non-linked events we performed a four-way in-teraction including link vs. non-link. This analysis yielded a significant four-way interaction, showing that the interaction of time (pre vs. post), mode of insight (imagination vs. obser-vation) and cTBS differed for linked vs. non-linked items. We then report the follow-up analyses, separately for linked and non-linked events. Please see pages 12-13, lines 287-294:

“First, we included the within-subject factors time (pre vs. post), mode of insight (imagina-tion vs. observation) and link (vs. non-link) by calculating the difference waves. Subse-quently we conducted a cluster-based permutation test comparing the cTBS and the sham groups. This analysis yielded a four-way interaction within a negative cluster in a fronto-temporal region (electrode: FT7; p = 0.007, ci-range = 0.00, SD = 0.00). This result indicates that the impact of cTBS over the angular gyrus on the neural pattern reconfiguration follow-ing imagination- vs. observation-based insight may differ between linked and non-linked events. For linked events, this analysis yielded a […]”

2) Overall, the focus on the targeted three-way interaction is poorly motivated. Also, a func-tional interpretation is largely missing.

In order to better explain our motivation for the three-way interaction, we em-phasized in the introduction the importance of disentangling potential differences due to the mode of insight, given the known role of the angular gyrus in imagination on pages 4-5, lines 107-115:

“Considering this involvement of the angular gyrus in imaginative processes, we expected that the effect of cTBS on the change in representational similarity from pre- to post-insight will differ based on the mode of insight – whether this insight was gained via imagination or observation. Specifically, we expected a more pronounced impairment in the neural recon-figurations when insight is gained via imagination, as this function may depend more on an-gular gyrus recruitment than insight gained via observation. Additionally, we expected cTBS to the left angular gyrus to interfere with the increase in neural similarity for linked events and with the decrease of neural similarity for non-linked event.”

As discussed on page 21 (starting from line 478; see also the intro on page 4), we expected that the angular gyrus would be particularly implicated in imagination-based insight, given its known role in imagination (e.g.: Thakral et al., 2017). Moreover, given the angular gyrus’s strong connectivity with other regions, the results observed may not be driven by this re-gion alone but also by interconnected regions, such as the hippocampus. We clarified these important points at the very end of the discussion on pages 23-24, lines 543-560:

“Furthermore, the differential impact of cTBS to the angular gyrus on neural reconfigura-tions between events linked via imagination and those linked via observation may be at-tributed to its crucial role in imaginative processes (Ramanan et al., 2018; Thakral et al., 2017). Another intriguing aspect to consider is that the stimulated site was situated in the more ventral portion of the angular gyrus, recognized for its stronger connectivity to the episodic hippocampal memory system in contrast to its more dorsal counterpart (Seghier, 2013; Uddin et al., 2010). This stronger connectivity between the ventral angular gyrus and the hippocampus may shed light on the greater impact of cTBS to the angular gyrus on im-agination-based insight. Given the angular gyrus’s robust connectivity with other brain re-gions, including the hippocampus (Seghier, 2013), it is plausible that the observed changes might not solely stem from alterations within the angular gyrus itself, but could also origi-nate from these interconnected regions. This notion may bear particular importance given the required accessibility to the hippocampus during imaginative processes (Benoit & Schacter, 2015; Grob et al., 2023a; Zeidman & Maguire, 2016). Interactions between the an-gular gyrus and the hippocampus may give rise to rich memory representations (Ramanan et al., 2018). In line with this, recent studies have demonstrated that cTBS to the angular gy-rus resulted in enhanced hippocampal connectivity and improved associative memory (Hermiller et al., 2019; Tambini et al., 2018; Wang et al., 2014).”

3) "Interestingly, we observed a different pattern of insight-related representational pattern changes for non-linked events." It is not sufficient to demonstrate that a given effect is pre-sent in one condition (linked events) but not the other (non-linked events). To claim that there are actually different patterns, the authors would need to compare the critical condi-tions directly (Nieuwenhuis et al., 2011).

We completely agree and now compared the two conditions directly. Specifical-ly, we now report the significant four-way interaction, including the factor link vs. non-link, before delving into separate analyses for linked and non-linked events on pages 12-13, lines 287-294:

“First, we included the within-subject factors time (pre vs. post), mode of insight (imagina-tion vs. observation) and link (vs. non-link) by calculating the difference waves. Subse-quently we conducted a cluster-based permutation test comparing the cTBS and the sham groups. This analysis yielded a four-way interaction within a negative cluster in a fronto-temporal region (electrode: FT7; p = 0.007, ci-range = 0.00, SD = 0.00). This result indicates that the impact of cTBS over the angular gyrus on the neural pattern reconfiguration follow-ing imagination- vs. observation-based insight may differ between linked and non-linked events. For linked events, this analysis yielded a […]”

4) "This analysis yielded a negative cluster (p = 0.032, ci-range = 0.00, SD = 0.00) in the parieto-temporal region (electrodes: T7, Tp7, P7; Fig. 3B)." (p. 11). The authors report results with specificity for certain topographical locations. However, this is in stark contrast to the fact that the authors derived time X time RSA maps.

We did derive time × time similarity maps for each electrode within each partic-ipant, which allowed us to find a cluster consisting of specific electrodes. We apologize for not making this aspect clear enough and have, therefore, modified the respective part of our methods section on page 38, lines 951-952:

“In total, this analysis produced eight Representational Dissimilarity Matrices (RDMs) for each electrode and each participant.”

5) "These theta power values were then combined to create representational feature vectors, which consisted of the power values for four frequencies (4-7 Hz) × 41 time points (0-2 sec-onds) × 64 electrodes. We then calculated Pearson's correlations to compare the power pat-terns across theta frequency between the time points of linked events (A with B), as well as between the time points of non-linked events (A with X) for the pre- and the post-phase separately, separately for stories linked via imagination and via observation. To ensure un-biased results, we took precautions not to correlate the same combination of stories twice, which prevented potential inflation of the data. To facilitate statistical comparisons, we ap-plied a Fisher z-transform to the Pearson's rho values at each time point. This yielded a global measure of similarity on each electrode site. We, thus, obtained time × time similarity maps for the linked events (A and B) and the non-linked events (A and X) in the pre- and post-phases, separately for the insight gained through imagination and observation." (p. 34+35).

If RSA values were calculated at each time point and electrode, the Pearson correlations would have been computed effectively between four samples only, which is by far not enough to derive reliable estimates (Schönbrodt & Perugini, 2013). The problem is aggra-vated by the fact that due to the time and frequency smoothing inherent in the time-frequency decomposition of the EEG data, nearby power values across neighboring theta frequencies are highly similar to start with. (e.g., Schönauer et al., 2017; Sommer et al., 2022).

Alternative approaches would be to run the correlations across time for each electrode (re-sulting in the elimination of the time dimension) or to run the correlations at each time point across electrodes (resulting in the elimination of topographic specificity).

At least, the authors should show raw RSA maps for linked and non-linked events in the pre- and post-phases separately for the insight gained through imagination and observa-tion in each group, to allow for assessing the suitability of the input data (in the supple-ments?) before progressing to reporting the results of three-way interactions.

Although we do see the reviewer’s point, we think that an RSA specific to the theta range yielding electrode specific time × time similarity maps must be run this way, otherwise, as you pointed out, one or the other dimension is compromised. Running an RSA across time for each electrode will lead to computing a similarity measure between the events without information on when these stimuli become more or less similar, thereby ig-noring the temporal dynamics crucial to EEG data and not taking advantage of the high temporal resolution. Conversely, conducting an RSA across electrodes might result in an overall similarity measure per participant, disregarding the spatial distribution and potential variations among electrodes. Although EEG has limited spatial resolution, different elec-trodes can capture differences that may aid in understanding neural processing. However, as suggested by the reviewer, we included the raw RSA maps for linked and non-linked events separately for pre- and post-phases, imagination and observation and link and non-link in the supplement and refer to these data in the results section on pages 12-13, lines 293-295:

“For linked events, this analysis yielded a negative cluster (p = 0.032, ci-range = 0.00, SD = 0.00) in the parieto-temporal region (electrodes: T7, Tp7, P7; Fig. 3B; Figure 3 – Figure sup-plement 1).”

And on page 15, lines 339-341:

“This analysis yielded a positive cluster (p = 0.035, ci-range = 0.00, SD = 0.00) in a fronto-temporal region (electrode: FT7; Fig. 3C; Figure 3 – Figure supplement 2).”

Reviewer 2

We thank the reviewer for the very helpful and constructive comments and appreciate that the reviewer finds our study relevant to all areas of cognitive research.

1) While the observed memory reconfiguration/changes are attributed to the angular gyrus in this study, it remains unclear whether these effects are solely a result of the AG's role in re-configuration processes or to what extent the hippocampus might also mediate these memory effects (e.g., Tambini et al., 2018; Hermiller et al., 2019).

We agree that, in addition to the critical role of the angular gyrus, there may be an involvement of the hippocampus. We point now explicitly to the modulatory capacities of angular gyrus stimulation on the hippocampus. Please see page 4, lines 81-88:

“One promising candidate that may contribute to insight-driven memory reconfiguration is the angular gyrus. The angular gyrus has extensive structural and functional connections to many other brain regions (Petit et al., 2023), including the hippocampus (Coughlan et al., 2023; Uddin et al., 2010). Accordingly, previous studies have shown that stimulation of the angular gyrus resulted in altered hippocampal activity (Thakral et al., 2020; Wang et al., 2014). Furthermore, the angular gyrus has been implicated in a myriad of cognitive func-tions, including mental arithmetic, visuospatial processing, inhibitory control, and theory-of-mind (Cattaneo et al., 2009; Grabner et al., 2009; Lewis et al., 2019; Schurz et al., 2014).”

We further added a new paragraph to the discussion pointing at the possibility that not solely the angular gyrus but another brain region, such as the hippocampus, may have me-diated the changes observed in our study on pages 23-24, lines 546-562:

“Another intriguing aspect to consider is that the stimulated site was situated in the more ventral portion of the angular gyrus, recognized for its stronger connectivity to the episodic hippocampal memory system in contrast to its more dorsal counterpart (Seghier, 2013; Ud-din et al., 2010). This stronger connectivity between the ventral angular gyrus and the hip-pocampus may shed light on the greater impact of cTBS to the angular gyrus on imagination-based insight. Given the angular gyrus’s robust connectivity with other brain regions, includ-ing the hippocampus (Seghier, 2013), it is plausible that the observed changes might not solely stem from alterations within the angular gyrus itself, but could also originate from these interconnected regions. This notion may bear particular importance given the re-quired accessibility to the hippocampus during imaginative processes (Benoit & Schacter, 2015; Grob et al., 2023a; Zeidman & Maguire, 2016). Interactions between the angular gyrus and the hippocampus may give rise to rich memory representations (Ramanan et al., 2018). In line with this, recent studies have demonstrated that cTBS to the angular gyrus resulted in enhanced hippocampal connectivity and improved associative memory (Hermiller et al., 2019; Tambini et al., 2018; Wang et al., 2014). However, it should be noted that our study detected impaired associative memory following cTBS to the angular gyrus.”

2) Another weakness in this manuscript is the use of different groups of participants for the key TMS intervention, along with underspecified or incomplete hypotheses/predictions.

In our view, the chosen between-subjects design is to be preferred over a crossover design for several reasons. First, our choice aimed to eliminate potential se-quence effects that may have adversely affected performance in the narrative-insight task (NIT). Second, this approach ensured consistency in expectations regarding the story links while also mitigating potential differences induced by fatigue. Additionally, we accounted for the potential advantage of a within-subject design – the stimulation of the same brain – by utilizing neuro-navigated TMS for targeting the stimulation coordinate. Finally, it is im-portant to note that we measured the event representations pre- and post-insight and that also the mode of insight was manipulated within-subject. Thus, our design did include a within-subject component and we are convinced that the chosen paradigm balances the different strengths and weaknesses of within-subject and between-subjects designs in the best possible manner. We specified our rationale for choosing a between-subjects ap-proach in the introduction on page 5, lines 122-126:

“We intentionally adopted a mixed design, combining both between-subjects and within-subject methodologies. The between-subjects approach was chosen to minimize the risk of carry-over effects and sequence biases. Simultaneously, we capitalized on the advantages of a within-subject design by altering the pre- to post-insight comparison and the mode of insight (imagination vs. observation) within each participant.”

Moreover, to provide a comprehensive portrayal of the two groups, we incorporated de-scriptions concerning trait and state variables alongside age and motor thresholds and in-cluded t-test comparisons between these variables on page 7, lines 157-160:

“Notably, the groups did not differ on levels of subjective chronic stress (TICS), state and trait anxiety (STAI-S, STAI-T), depressive mood (BDI), imaginative capacities (FFIS), person-ality dimensions (BFI), age, and motor thresholds (for descriptive statistics see Table 1; all p > 0.053).”

And further included age and motor thresholds as control variables in Table 1 on page 18, lines 402-404:

“Overall, levels of subjective chronic stress, anxiety, and depressive mood were relatively low and not different between groups. The groups did further not differ in terms of per-sonality traits, imagination capacity, age or motor thresholds (all p > 0.053; see Table 1).”

For greater precision in outlining our hypotheses, we specified these at the end of the in-troduction on pages 4-55, lines 107-118:

“Considering this involvement of the angular gyrus in imaginative processes, we expected that the effect of cTBS on the change in representational similarity from pre- to post-insight will differ based on the mode of insight – whether this insight was gained via imagination or observation. Specifically, we expected a more pronounced impairment in the neural recon-figurations when insight is gained via imagination, as this function may depend more on an-gular gyrus recruitment than insight gained via observation. Additionally, we expected cTBS to the left angular gyrus to interfere with the increase in neural similarity for linked events and with the decrease of neural similarity for non-linked events. We further predicted that cTBS to the left angular gyrus would reduce the impact of (imagination-based) insight into the link of initially unrelated events on memory performance during free recall, given its higher variability compared to other memory measures.”

3) Furthermore, in some instances, the types of analyses used do not appear to be suitable for addressing the questions posed by the current study, and there is limited explanation pro-vided for the choice of analyses and questionnaires.

We addressed this concern by inserting a new section “control variables” in the methods explaining our rationale for employing the different questionnaires as control var-iables on pages 40-41, lines 1003-1019:

“Control variables In order to ensure that the observed effects were solely attributable to the TMS manipula-tion and not influenced by other factors, we comprehensively evaluated several trait and state variables. To account for potential variations in anxiety levels that could impact our re-sults, we specifically measured state and trait anxiety using STAI-S and STAI-T (Laux et al., 1981), thus minimizing the potential confounding effects of anxiety on our findings (Char-pentier et al., 2021). Additionally, we evaluated participants’ chronic stress levels using the TICS (Schulz & Schlotz, 1999) to exclude any group variations that might explain the effect on memory, cosidering the well-established impact of stress on memory (Sandi & Pinelo-Nava, 2007; Schwabe et al., 2012). Moreover, we assessed participants’ depressive symp-toms employing the BDI (Hautzinger et al., 2006), to guarantee group comparability on this clinical measure. We further assessed fundamental personality dimensions using the BFI-2 (Danner et al., 2016) to exclude any potential group discrepancies that could account for dif-ferences observed. Lastly, we assessed participants’ imaginative capacities using the FFIS (Zabelina & Condon, 2019), to ensure uniformity across groups regarding this central varia-ble, considering the significant role of imagination in relation to the cTBS-targeted angular gyrus (Thakral et al., 2017).”

We further specified why we chose to analyze our behavioral data using LMMs on page 34, lines 849-85:

“For our behavioral analyses we opted to employ linear-mixed models (LMM), given their high robustness regarding the underlying distribution and high sensitivity to individual varia-tion (Pinheiro & Bates, 2000; Schielzeth et al., 2020).”

Moreover, we added an explanation on why we opted for the RSA approach in the meth-ods section on page 37, lines 920-923:

“This method is ideally suited to measure neural representation changes and was specifical-ly chosen as it has been previously identified as the preferred approach for quantifying in-sight-induced neural changes (Grob et al., 2023b; Milivojevic et al., 2015).”

To clarify on the rationale behind our coherence analysis, we incorporated an explanatory sentence in the methods section on page 39, lines 966-967:

“Due to the robust connectivity between the angular gyrus and other brain regions (Petit et al., 2023; Seghier, 2013), we proceeded with a connectivity analysis as a next step.”

Reviewer 3

We thank the reviewer for the constructive and very helpful comments. We are pleased that the reviewer considered our experimental design to be strong and our behavioral results to be striking.

1) My major criticism relates to the main claim of the paper regarding causality between the angular gyrus and the authors' behavior of interest. Specifically, I am not convinced by the evidence that the effects of stimulation noted in the paper are attributable specifically to the angular gyrus, and not other regions/networks.

While our results showed specific changes after cTBS over the angular gyrus, demonstrating a causal involvement of the angular gyrus in these effects, we completely agree that this does not rule out an involvement of additional areas. In particular, there is evidence suggesting that cTBS over parietal regions, such as the angular gyrus, could poten-tially influence hippocampal functioning. We address this issue now in a new paragraph that we have added to the discussion, on pages 23-24, lines 546-564:

“Another intriguing aspect to consider is that the stimulated site was situated in the more ventral portion of the angular gyrus, recognized for its stronger connectivity to the episodic hippocampal memory system in contrast to its more dorsal counterpart (Seghier, 2013; Ud-din et al., 2010). This stronger connectivity between the ventral angular gyrus and the hip-pocampus may shed light on the greater impact of cTBS to the angular gyrus on imagination-based insight. Given the angular gyrus’s robust connectivity with other brain regions, includ-ing the hippocampus (Seghier, 2013), it is plausible that the observed changes might not solely stem from alterations within the angular gyrus itself, but could also originate from these interconnected regions. This notion may bear particular importance given the re-quired accessibility to the hippocampus during imaginative processes (Benoit & Schacter, 2015; Grob et al., 2023a; Zeidman & Maguire, 2016). Interactions between the angular gyrus and the hippocampus may give rise to rich memory representations (Ramanan et al., 2018). In line with this, recent studies have demonstrated that cTBS to the angular gyrus resulted in enhanced hippocampal connectivity and improved associative memory (Hermiller et al., 2019; Tambini et al., 2018; Wang et al., 2014). However, it should be noted that our study detected impaired associative memory following cTBS to the angular gyrus. Expanding upon this idea, it is conceivable that targeting a more dorsal segment of the angular gyrus might exert a stronger influence on observation-based linking – an aspect that warrants future in-vestigations.”

Responses to reviewer recommendations

Reviewer 1

1) On page 26, the authors write: "[...] different video events (A, B, and X) were recalled from day one [...]". I may have missed this point, but I had the impression that the task was con-ducted within one day.

Indeed, this study was conducted within a single day. We rephrased the respec-tive statement accordingly. Please see page 7, lines 149-153:

“To test this hypothesis and the causal role of the angular gyrus in insight-related memory reconfigurations, we combined the life-like video-based narrative-insight task (NIT) with representational similarity analysis of EEG data and (double-blind) neuro-navigated TMS over the left angular gyrus in a comprehensive investigation within a single day.”

We further included this information in the methods section on page 27, lines 634-635:

“In total, the experiment took about 4.5 hours per participant and was completed within a single day. ”

Reviewer 2

1) There is a substantial disconnection between the introduction and the methods/results sec-tion. One reason is that there is not sufficient detail regarding the hypotheses/predictions and the specific types of analyses chosen to test these hypotheses/predictions. Additionally, it is not explained what comparisons and outcomes would be informative/expected. This should be made clear. Second and related to the above, the rationale for conducting certain types of analyses (correlation, coherence, see below) sometimes is not specified.

To address this concern, we elaborated on our hypotheses incorporating specif-ic predictions for the free recall, given its higher variability than the other memory measures, and for imagination vs. observation at the end of the introduction on pages 4-5, lines 107-122:

“Considering this involvement of the angular gyrus in imaginative processes, we expected that the effect of cTBS on the change in representational similarity from pre- to post-insight will differ based on the mode of insight – whether this insight was gained via imagination or observation. Specifically, we expected a more pronounced impairment in the neural recon-figurations when insight is gained via imagination, as this function may depend more on an-gular gyrus recruitment than insight gained via observation. Additionally, we expected cTBS to the left angular gyrus to interfere with the increase in neural similarity for linked events and with the decrease of neural similarity for non-linked events. We further predicted that cTBS to the left angular gyrus would reduce the impact of (imagination-based) insight into the link of initially unrelated events on memory performance during free recall, given its higher variability compared to other memory measures. Considering the high connectivity profile of the angular gyrus within the brain (Seghier, 2013), we conducted an EEG connec-tivity analysis building upon prior findings concerning alterations in neural reconfigurations. To establish a link between neural and behavioral findings, we chose a correlational ap-proach to relate observations from these two domains.”

Moreover, we made our rationale for the employed analyses more explicit and specified why we chose to analyze our behavioral data using LMMs on page 34, lines 849-851:

“For our behavioral analyses we opted to employ linear-mixed models (LMM), given their high robustness regarding the underlying distribution and high sensitivity to individual varia-tion (Pinheiro & Bates, 2000; Schielzeth et al., 2020).”

Moreover, we added an explanation on why we opted for the RSA approach in the meth-ods section on page 37, lines 920-923:

“This method is ideally suited to measure neural representation changes and was specifical-ly chosen as it has been previously identified as the preferred approach for quantifying in-sight-induced neural changes (Grob et al., 2023b; Milivojevic et al., 2015).”

To clarify on the rationale behind our coherence analysis, we incorporated an explanatory sentence in the methods section on page 39, lines 966-967:

“Due to the robust connectivity between the angular gyrus and other brain regions (Petit et al., 2023; Seghier, 2013), we proceeded with a connectivity analysis as a next step.”

2) The authors suggest that besides Branzi et al. (2021), this is one of the first studies showing that memory update is linked to the AG. I suggest having a look at work from Tambini, Nee, & D'Esposito, 2018, JoCN, and other papers from Joel Voss' group that target a similar re-gion of AG/Inferior parietal cortex. Many studies, using multiple TMS protocols, have now shown this brain region is causally involved in episodic and associative memory encoding.

As mentioned above, further consideration of this literature is important as it delves into the region's hippocampal connectivity (and other network properties), and how that mediates the memory effects. Indeed because of the nature of the methods employed in this study, we do not know if the memory-related behavioural effects are due to TMS-changes induced at the AG's versus the hippocampal' s level, or both. How do the current findings square with the existing TMS effects from this region? Can the connectivity profile of the target re-gion highlighted by previous studies provide further insight into how the current behaviour-al effect arises? Some comments on this could be added to the discussion.

We completely agree that the other studies showing enhanced associative memory after TMS to parietal regions need to be addressed. Therefore, we updated the discussion on page 20, lines 449-453:

“Interestingly, recent work has additionally indicated that targeting parietal regions with TMS led to alterations in hippocampal functional connectivity, thereby enhancing associa-tive memory (Nilakantan et al., 2017; Tambini et al., 2018; Wang et al., 2014), potentially shedding light on the underlying mechanisms involved.”

Moreover, we included a section specifically addressing the possibility that the effects ob-served may pertain to having modulated other regions via the targeted region and updated the discussion on pages 23-24, lines 543-562:

“Furthermore, the differential impact of cTBS to the angular gyrus on neural reconfigura-tions between events linked via imagination and those linked via observation may be at-tributed to its crucial role in imaginative processes (Ramanan et al., 2018; Thakral et al., 2017). Another intriguing aspect to consider is that the stimulated site was situated in the more ventral portion of the angular gyrus, recognized for its stronger connectivity to the episodic hippocampal memory system in contrast to its more dorsal counterpart (Seghier, 2013; Uddin et al., 2010). This stronger connectivity between the ventral angular gyrus and the hippocampus may shed light on the greater impact of cTBS to the angular gyrus on im-agination-based insight. Given the angular gyrus’s robust connectivity with other brain re-gions, including the hippocampus (Seghier, 2013), it is plausible that the observed changes might not solely stem from alterations within the angular gyrus itself, but could also origi-nate from these interconnected regions. This notion may bear particular importance given the required accessibility to the hippocampus during imaginative processes (Benoit & Schacter, 2015; Grob et al., 2023a; Zeidman & Maguire, 2016). Interactions between the an-gular gyrus and the hippocampus may give rise to rich memory representations (Ramanan et al., 2018). In line with this, recent studies have demonstrated that cTBS to the angular gy-rus resulted in enhanced hippocampal connectivity and improved associative memory (Hermiller et al., 2019; Tambini et al., 2018; Wang et al., 2014). However, it should be noted that our study detected impaired associative memory following cTBS to the angular gyrus.”

3) Another comment I have regards the results observed for the observation vs imagination insight conditions. The authors mention that the 'changes in representational similarity for the observation condition should be interpreted with caution, as these seemingly opposite changes appeared to be at least in part driven by group differences already in the pre-phase before participants gained insight.' I wonder what these group differences are and whether the authors have any hypothesis about what factors determined them.

We could only speculate about the basis of the observed pre-insight phase dif-ferences. However, we provide now the raw RSA data as supplemental material to make the pattern of the (raw) RSA findings in the pre- and post-insight phases more transparent. We refer the interested reader to this material on pages 12-13, lines 293 to 295:

“For linked events, this analysis yielded a negative cluster (p = 0.032, ci-range = 0.00, SD = 0.00) in the parieto-temporal region (electrodes: T7, Tp7, P7; Fig. 3B; Figure 3 – Figure sup-plement 1).”

And on page 15, lines 339-341:

“This analysis yielded a positive cluster (p = 0.035, ci-range = 0.00, SD = 0.00) in a fronto-temporal region (electrode: FT7; Fig. 3C; Figure 3 – Figure supplement 2).”

Furthermore, the age of participants is not reported separately for the two groups (cTBS to AG vs Sham), I think. This should be reported including a t-test showing that the two groups have the same age.

We agree and report now explicitly that groups did not significantly differ in rel-evant control variables including age. Please see page 7, lines 157-160:

“Notably, the groups did not differ on levels of subjective chronic stress (TICS), state and trait anxiety (STAI-S, STAI-T), depressive mood (BDI), imaginative capacities (FFIS), person-ality dimensions (BFI), age, and motor thresholds (for descriptive statistics see Table 1; all p > 0.053).”

And further included age and motor thresholds as control variables in Table 1 on page 18, lines 402-412:

“Overall, levels of subjective chronic stress, anxiety, and depressive mood were relatively low and not different between groups. The groups did further not differ in terms of per-sonality traits, imagination capacity, age or motor thresholds (all p > 0.053; see Table 1).”

The fact this study is not a within-subject design makes difficult the interpretation of the results and this should be recognised as an important limitation of the study.

As outlined above, a within-subject design would in our view come with several disadvantages, such as significant sequence/carry-over effects. Moreover, the neural rep-resentation change was measured in a pre-post design, enabling us to measure the insight-driven neural reconfiguration at the individual level.

We clarify our rationale for the between-subjects factor TMS in the introduction on page 5, lines 122-126:

“We intentionally adopted a mixed design, combining both between-subjects and within-subject methodologies. The between-subjects approach was chosen to minimize the risk of carry-over effects and sequence biases. Simultaneously, we capitalized on the advantages of a within-subject design by altering the pre- to post-insight comparison and the mode of insight (imagination vs. observation) within each participant.”

Furthermore, we included our rationale for choosing a between-subjects approach for the crucial TMS manipulation in the methods section on page 25, lines 601-604:

“We implemented a mixed-design including the within-subject factors link (linked vs. non-linked events), session (pre- vs. post-link), and mode (imagination vs. observation) as well as the between-subjects factor group (cTBS to the angular gyrus vs. sham) to mitigate the risk of carry-over effects and sequence biases of the crucial cTBS manipulation.”

4) The angular gyrus is a heterogeneous region with multiple graded subregions. The one tar-geted in the present study is the ventral AG which has strong connections with the episodic-hippocampal memory system. I was wondering if this might explain why the AG TMS ef-fects on representational changes have been observed for events linked via imagination but not direct observation. Perhaps the stimulation of a more 'visual' AG subregion (see Hum-phreys et al., 2020, Cerebral Cortex) would have resulted in a different (opposite) pattern of results. It would be good to add some comments on this in the discussion.

We appreciate this interesting perspective offered regarding the potential out-comes of our study, particularly in relation to the activation of a more ventral sub region of the angular gyrus. We incorporated this idea into our discussion, alongside considerations regarding the potential effects of a more dorsal angular gyrus stimulation on observation-based linking. However, caution is warranted recognizing the inherent limitations posed by the precision of TMS manipulations, which is further underscored by our electric field simu-lations, utilizing a 10 mm radius. We included this section in the discussion on pages 23-24, lines 546-569:

“Another intriguing aspect to consider is that the stimulated site was situated in the more ventral portion of the angular gyrus, recognized for its stronger connectivity to the episodic hippocampal memory system in contrast to its more dorsal counterpart (Seghier, 2013; Ud-din et al., 2010). This stronger connectivity between the ventral angular gyrus and the hip-pocampus may shed light on the greater impact of cTBS to the angular gyrus on imagina-tion-based insight. Given the angular gyrus’s robust connectivity with other brain regions, including the hippocampus (Seghier, 2013), it is plausible that the observed changes might not solely stem from alterations within the angular gyrus itself, but could also originate from these interconnected regions. This notion may bear particular importance given the re-quired accessibility to the hippocampus during imaginative processes (Benoit & Schacter, 2015; Grob et al., 2023a; Zeidman & Maguire, 2016). Interactions between the angular gyrus and the hippocampus may give rise to rich memory representations (Ramanan et al., 2018). In line with this, recent studies have demonstrated that cTBS to the angular gyrus resulted in enhanced hippocampal connectivity and improved associative memory (Hermiller et al., 2019; Tambini et al., 2018; Wang et al., 2014). However, it should be noted that our study detected impaired associative memory following cTBS to the angular gyrus. Expanding upon this idea, it is conceivable that targeting a more dorsal segment of the angular gyrus might exert a stronger influence on observation-based linking – an aspect that warrants future in-vestigations. Yet, while acknowledging the functional heterogeneity within the angular gy-rus (Humphreys et al., 2020), pinpointing specific sub regions via TMS remains challenging due to its limited focal precision at the millimeter level (Deng et al., 2013; Thielscher & Kammer, 2004), as reinforced by our electric field simulations utilizing a 10 mm radius. Hence, drawing definitive conclusions regarding distinct angular gyrus sub regions requires future research employing rigorous checks to assess the focality of their stimulation.”

5) Regarding the methods section, I have the following specific queries. It is unclear what is the purpose of the coherence and correlation analyses (pages 35, 36). Could the authors pro-vide further clarification on this? These analyses seem not to be mentioned anywhere in the introduction. This should be clarified briefly in the introduction and then in the methods sec-tion. The same for the questionnaires (anxiety, stress, etc): It is unclear the reason for col-lecting this type of data. This should be clarified in the introduction as well.

We agree, and have updated the introduction as follows on page 5, lines 118-122:

“Considering the high connectivity profile of the angular gyrus within the brain (Seghier, 2013), we conducted an EEG connectivity analysis building upon findings from the RSA anal-yses concerning alterations in neural reconfigurations. To establish a link between neural and behavioral findings, we chose a correlational approach to relate observations from these two domains.”

We additionally provided an explanation for including these questionnaires in the introduc-tion on page 5, lines 126-129:

“To control for any group differences beyond the TMS manipulation, we gathered various control variables through questionnaires, including trait- and state-anxiety, depressive symptoms, chronic stress levels, personality dimensions, and imaginative capacities.”

Moreover, we elaborated on the underlying rationale guiding our chosen analytical ap-proaches. Therefore, we specified why we chose to analyze our behavioral data using LMMs on page 34, lines 849-851:

“For our behavioral analyses we opted to employ linear-mixed models (LMM), given their high robustness regarding the underlying distribution and high sensitivity to individual varia-tion (Pinheiro & Bates, 2000; Schielzeth et al., 2020).”

Furthermore, we added an explanation on why we opted for the RSA approach in the methods section on page 37, lines 920-923:

“This method is ideally suited to measure neural representation changes and was specifical-ly chosen as it has been previously identified as the preferred approach for quantifying in-sight-induced neural changes (Grob et al., 2023b; Milivojevic et al., 2015).”

To clarify on the rationale behind our coherence analysis, we incorporated an explanatory sentence in the methods section on page 39, lines 966-967:

“Due to the robust connectivity between the angular gyrus and other brain regions (Petit et al., 2023; Seghier, 2013), we proceeded with a connectivity analysis as a next step.”

6) The preregistration webpage is in German. This is not ideal as it means that the information is available only to German speakers.

This webpage can easily be switched to English by changing the settings in the top right corner:

To address this issue, we included a description of how to set the webpage to English in the methods section on page 25, lines 581-582:

“For translation to English, please adjust the page settings located in the top right corner.”

7) Page 18. 'NIT' and 'MAT' - avoid abbreviations when possible.

We included the full name for the narrative-insight task (NIT) on page 7, line 151, line 153, and line 165, page 8 lines 177-178 and line 187, page 19 on line 427, page 26 on line 615, line 629 and line 632, page 27, line 653, page 30, lines 730-731, page 31, line 754, page 35, line 870, line 873, and page 36 and line 885.

We further included the full name for the multi-arrangements task (MAT) on page 19, lines 428-429.

8) Line 21....we further observed DECREASED...should be replaced with INCREASED, if I am not wrong.

We checked the sentence again and it looks correct to us, since it describes the change for observation-based insight, not imagination-based insight. We clarified that this finding pertains to observation-based linking by modifying the sentence on page 23, lines 525-528, as follows:

“Following cTBS to the angular gyrus, we further observed decreased pattern similarity for non-linked events in the observation-based condition, resembling the pattern change ob-served in the sham group for linked events, which may highlight the role of the angular gy-rus in representational separation during observation-based linking”

Reviewer 3

1) The major claim of the paper is that the angular gyrus is causally involved in insight-driven memory reconfiguration. To the authors' credit, they localized stimulation to the angular gyrus using an anatomical scan, the strength of the estimated electromagnetic field in the angular gyrus correlated with their behavioral results, and there were also brain-behavior correlations involving sensors located in the parietal lobe. However, the minimum evidence needed to claim causality is 1) evidence of a behavioral change (which the authors found) and 2) evidence of target engagement in the angular gyrus. It is also important to show brain-behavior correlations between target engagement and behavior. Although the au-thors stimulated the angular gyrus, that does not mean that rTMS specifically affected this region or that the behavioral results can be attributed to rTMS effects on the angular gyrus. As the authors point out, the angular gyrus has dense connections with other regions such as the hippocampus. In fact, several studies have shown that angular gyrus (or near AG) stimulation affects the hippocampal network (Wang et al., 2014, Science; Freedberg et al. 2019, eNeuro; Thakral et al., 2020, PNAS). EEG also has a poor spatial resolution, so even though the results were attributable to parieto-temporal sensors, this is not sufficient evi-dence to claim that the angular gyrus was modulated. Source localization would be re-quired to reconstruct the signal specifically from the AG. Thus, with the manuscript written as is, the authors can claim that "cTBS to the angular gyrus modulates insight-driven memory reconfiguration," but the current claim is not sufficiently substantiated.

While acknowledging the potential role of the angular gyrus in driving the ob-served changes, we recognize that the available evidence may not be sufficient. Conse-quently, we have introduced several modifications within our manuscript to address this concern.

In the revised Introduction, we now explicitly address the possibility of a stimulation of the hippocampus via the angular gyrus on page 4, lines 84-85:

“Accordingly, previous studies have shown that stimulation of the angular gyrus resulted in altered hippocampal activity (Thakral et al., 2020; Wang et al., 2014).”

Additionally, we included relevant evidence demonstrating previous instances of targeted stimulation of the angular gyrus, which led to alterations in hippocampal connectivity and associative memory. These insights have been included in the discussion on page 20, lines 449-453:

“Interestingly, recent work has additionally indicated that targeting parietal regions with TMS led to alterations in hippocampal functional connectivity, thereby enhancing associa-tive memory (Nilakantan et al., 2017; Tambini et al., 2018; Wang et al., 2014), potentially shedding light on the underlying mechanisms involved.”

Next, we have integrated crucial modifications essential for establishing a conclusive infer-ence of causality in our study. Moreover, we now explore the potential mediation of the effects observed from angular gyrus stimulation through other brain regions, like the hip-pocampus. In addition, we have highlighted prior work where such stimulation coincided with alterations in associative memory. For the updated discussion section, please see pag-es 23-24, lines 538-562:

“Although our study provided evidence suggesting a causal role of the angular gyrus in in-sight-driven memory reconfigurations – highlighted by behavioral changes after cTBS to the angular gyrus, neural changes in left parietal regions, and relevant brain-behavior associa-tions – it is important to acknowledge the limitations imposed by the spatial resolution of EEG. Consequently, the precise source of the observed signal changes in the parietal re-gions remains uncertain, potentially tempering the definitive nature of these findings. Fur-thermore, the differential impact of cTBS to the angular gyrus on neural reconfigurations between events linked via imagination and those linked via observation may be attributed to its crucial role in imaginative processes (Ramanan et al., 2018; Thakral et al., 2017). An-other intriguing aspect to consider is that the stimulated site was situated in the more ven-tral portion of the angular gyrus, recognized for its stronger connectivity to the episodic hippocampal memory system in contrast to its more dorsal counterpart (Seghier, 2013; Ud-din et al., 2010). This stronger connectivity between the ventral angular gyrus and the hip-pocampus may shed light on the greater impact of cTBS to the angular gyrus on imagina-tion-based insight. Given the angular gyrus’s robust connectivity with other brain regions, including the hippocampus (Seghier, 2013), it is plausible that the observed changes might not solely stem from alterations within the angular gyrus itself, but could also originate from these interconnected regions. This notion may bear particular importance given the re-quired accessibility to the hippocampus during imaginative processes (Benoit & Schacter, 2015; Grob et al., 2023a; Zeidman & Maguire, 2016). Interactions between the angular gyrus and the hippocampus may give rise to rich memory representations (Ramanan et al., 2018). In line with this, recent studies have demonstrated that cTBS to the angular gyrus resulted in enhanced hippocampal connectivity and improved associative memory (Hermiller et al., 2019; Tambini et al., 2018; Wang et al., 2014). However, it should be noted that our study detected impaired associative memory following cTBS to the angular gyrus.”

We further replaced terms that imply inhibition of the angular gyrus with a more operation-ally descriptive phrase:

“cTBS to the angular gyrus”

2) The authors frequently claim that cTBS is "inhibitory stimulation" and that inhibition of the angular gyrus caused their effects. There is a common misconception within the cognitive neuroscience literature that stimulation is either "inhibitory" or "excitatory," but there is no such thing as either. The effects of rTMS are dependent on many physiological, state, and trait-specific variables and the location of stimulation. For example, while cTBS does repro-ducibly inhibit behavior supported by the motor cortex (Wilkinson et al., 2010, Cortex; Rosenthal et al., 2009, J Neurosci), cTBS of the posterior parietal cortex reproducibly en-hances hippocampal network functional connectivity and episodic memory (Hermiller et al., 2019, Hippocampus; Hermiller et al., 2020, J Neurosci). The authors reference the Huang et al. (2005) paper as evidence of its inhibitory effects but work in this paper is not sufficient to broadly categorize cTBS as inhibitory. First, Huang et al. stimulated the motor cortex and measured the effects on corticospinal excitability, which is significantly different from what the current authors are measuring. Furthermore, this oft-cited study only included 9 sub-jects. Other studies have found that the effects of theta-burst are significantly more varia-ble when more subjects are used. For example, intermittent theta-burst, which is assumed to be excitatory based on the Huang paper, was found to produce unreliable excitatory ef-fects when more subjects were examined (Lopez-Alonso, 2014, Brain Stimulation). Thus, the a priori assumption that stimulation would be inhibitory is weak and cTBS should not be dis-cussed as "inhibitory."

We agree and included now a statement in the methods section that explicitly states that cTBS effects may be region-specific on page 33, lines 817-819:

“Nonetheless, the effects of cTBS appear to vary based on the targeted region, with cTBS to parietal regions demonstrating the capability to enhance hippocampal connectivity (Hermiller et al., 2019, 2020).”

We further substituted all terminology suggestive of an inhibitory effect with the phrase:

“cTBS to the angular gyrus”.

However, it is important to note, that while other studies (Hermiller et al., 2019; Tambini et al., 2018; Wang et al., 2014) found increased hippocampal connectivity after rTMS to a parie-tal region as well as enhanced associative memory, we observed impaired memory for the linked events. We included this clarification in the discussion on page 24, lines 558-562:

“In line with this, recent studies have demonstrated that cTBS to the angular gyrus resulted in enhanced hippocampal connectivity and improved associative memory (Hermiller et al., 2019; Tambini et al., 2018; Wang et al., 2014). However, it should be noted that our study detected impaired associative memory following cTBS to the angular gyrus.”

3) The hypothesis at the end of the introduction did not strike me as entirely clear. From this hypothesis, it seems that the authors are just comparing the differences in memory and re-configuration during imagination-based insight links. However, the authors also include ob-servation-based links and a non-linking condition, which seem ancillary to the main hy-pothesis. Thus, I am confused about why these extra factors were included and exactly what statistical results would confirm the authors' hypothesis.

We agree, and have clarified our hypotheses on pages 4-5, lines 107-115:

“Considering this involvement of the angular gyrus in imaginative processes, we expected that the effect of cTBS on the change in representational similarity from pre- to post-insight will differ based on the mode of insight – whether this insight was gained via imagination or observation. Specifically, we expected a more pronounced impairment in the neural recon-figurations when insight is gained via imagination, as this function may depend more on an-gular gyrus recruitment than insight gained via observation. Additionally, we expected cTBS to the left angular gyrus to reduce the increase in neural similarity for linked events and in-crease of neural dissimilarity for non-linked events.”

4) Many of the distributions throughout the paper do not look normal. Was normality checked? Are non-parametric stats warranted?

We evaluated and reported the normality assumption in our behavioral anal-yses. Despite the non-normal distribution of our data, we chose to utilize linear-mixed models due to their robust performance even in case of deviations from normal distribu-tions. This update in our methods section can be found on page 36, lines 890-896:

“After outlier correction, we identified non-normality in our data using a Shapiro-Wilk test (narrative-insight task: W = 0.92, p < 0.001; multi-arrangements task: W = 0.94, p < 0.001; forced-choice recognition: W = 0.50, p < 0.001; free recall details: W = 0.85, p < 0.001; free recall naming of linking events: W = 0.94, p < 0.001). However, we mitigated this by employ-ing linear-mixed models (LMMs), recognized for their robustness even with non-normally distributed data (Schielzeth et al., 2020).”

We recalculated the correlational analysis between the RSA data and the behavioral recall of linking events by using the Spearman method on page 13, lines 306-308:

“Furthermore, to address a deviation from the normality assumption, the correlational analysis was repeated using the Spearman method, which indicated an even stronger cor-relation (r(59) = 0.32, p = 0.012).”

We further recalculated the correlation between the change in coherence for linked events and the recall of details for events linked via imagination on page 16, lines 376-378:

“Please note that for addressing a deviation from the normality assumption, the correla-tional analysis was repeated using the Spearman method, which yielded a significant corre-lation of similar strength (r(59) = 0.31, p = 0.015).”

Our EEG analyses , including RSA and coherence analyses, utilized a cluster-based permuta-tion test (Fieldtrip; Oostenveld et al., 2011). These tests do not assume a normal distribu-tion by utilizing empirical sampling for statistical inference. This approach ensures robust-ness without constraints imposed by specific distributional assumptions. Subsequent t-tests, stemming from significant clusters identified in the initial non-parametric analyses, were extensions of the robust non-parametric approach and did not require additional normality testing.

5) Can the authors include more detail about the sham coil? Was it subthreshold? Did the EMF cross the skull?

The sham coil, also obtained from MAG & More GmbH, München, Germany, provided a similar sensory experience; however, the company did not specify any field strength (n.a.) as this coil was purposefully designed to prevent the induction of an elec-tromagnetic field (EMF) capable of penetrating the skull, thereby ensuring it had no impact on the brain. We clarified on this point in the methods section on pages 31-32, lines 772-778:

“Two identically looking but different 70 mm figure-of-eight-shaped coils were used de-pending on the TMS condition: The PMD70-pCool coil (MAG & More GmbH, München, Germany) with a 2T maximum field strength was used for cTBS, while the PMD70-pCool-SHAM coil (MAG & More GmbH, München, Germany), with minimal magnetic field strength, was employed for sham, providing a similar sensory experience, with stimulation pulses being scattered over the scalp and not penetrating the skull.”

6) There are differences between exclusion criteria in pre-registration and report. For example, BMI is an exclusion factor in the report, but not in the pre-registration. Can the authors provide a reason for this deviation?

This discrepancy is due to (partial) participant recruitment from previous fMRI studies conducted in our lab that involved a stress induction protocol (as a structural MRI image was needed for the ‘neuronavigated’ TMS). Owing to the distinct cortisol stress reac-tivity observed in individuals with varying body mass indices (BMIs), participants with a BMI below 19 or above 26 kg/m² were excluded from these studies. To maintain consistency within our sample, only participants meeting these criteria were included. We elaborated on this point in the methods section on page 25, lines 586-592:

“Participants were screened using a standardized interview for exclusion criteria that com-prised a history of neurological and psychiatric disease, medication use and substance abuse, cardiovascular, thyroid, or renal disease, evidence of COVID-19 infection or expo-sure, and any contraindications to MRI examination or TMS. Additionally, participants with a body mass index (BMI) below 19 or above 26 kg/m² were excluded. This decision stemmed from recruiting some participants from prior studies that incorporated stress induction pro-tocols, which imposed this specific criterion (Herhaus & Petrowski, 2018; Schmalbach et al., 2020).”

7) Were impedances monitored and minimized during EEG?

Yes, they were monitored. We clarified this point in the methods section on page 34, lines 845-847:

“We maintained impedances within a range of ± 20 μV using the common mode sense (CMS) and driven right leg (DRL) electrodes, serving as active reference and ground, re-spectively”

8) I think there may be a typo related to the Thakral coordinates. I believe Thakral used MNI coordinates -48,-64, 30, whereas the authors stated they used -48,-67,30. Is this a mistake?

Upon reevaluation of our study coordinates, we identified a slight deviation in our stimulation coordinates compared to those reported by Thakral et al. (2017; +3mm on the y-axis). This variance resulted from the required MNI to Talairach (TAL) transformations necessary for utilizing the neuronavigation software Powermag View! (MAG & More GmbH, München, Germany). Notably, this deviation was consistent across all participants in our study. While TMS is more precise than tDCS, its focality is not as fine-grained down to the millimeter level. Despite this, our electric field simulations, adopting a 10mm radius, ef-fectively encompassed the original coordinates specified by Thakral et al. (2017). This radius ensured coverage over the intended target area, mitigating the impact of this minor devia-tion on the overall study outcomes. We updated the methods section accordingly on page 33, lines 800-806:

“Based on the individual T1 MR images, we created 3D reconstructions of the participants' heads, allowing us to precisely locate the left angular gyrus coordinate (MNI: -48, -67, 30), initially derived from previous work (Thakral et al., 2017), for TMS stimulation. Despite a mi-nor deviation in coordinates due to necessary MNI to Talairach transformations for soft-ware compatibility (Powermag View! by MAG & More GmbH, München, Germany), our methodology ensured precise localization of the angular gyrus target area.”

9) How was the tail of the coil positioned during stimulation? Was it individualized so that the lobes of the coil are perpendicular to the nearest gyrus, as is commonly done?

The coil handle always pointed upwards to maintain optimal positioning with the coil holder. We followed the positioning procedure in the neuronavigation software Powermag View!, which did not indicate any positioning of the coil handle but specified the position and angle of the coil itself. To incorporate this aspect, we updated the legend of figure 2 on page 11, lines 260-261:

“Please note that in the study, the coil handle was oriented upwards; however, in this illus-tration, it has been intentionally depicted as pointing downwards for better visibility pur-poses.”

We further updated the method section on page 33, lines 723-824:

“The coil was positioned tangentially on the head and mechanically fixed in a coil holder, with its handle pointing upwards to maintain its position”

Author Response

We are grateful for the insightful suggestions and comments provided by the reviewers. Your constructive feedback has been valuable, and we are thankful for the opportunity to address each point.

We appreciate both reviewers’ recognition of our devotion to rigorous methodology and experimental control in this study, as evidenced by the comments: “remarkable efforts were made to isolate peripheral confounds”, “a clear strength of the study is the multitude of control conditions … that makes results very convincing”, and “thorough design of the study”. Indeed, we hope to have provided more than solid, but compelling evidence for sound-driven motor inhibitory effects of online TUS. We hope that this will be reflected in the assessment. Our conclusions are supported by multiple experiments across multiple institutions using exemplary experimental control including (in)active controls and multiple sound-sham conditions. This contrasts with the sole use of flip-over sham or no-stimulation conditions used in the majority of work to date. Indeed, the current study communicates that substantiated inferences on the efficacy of ultrasonic neuromodulation cannot be made under insufficient experimental control.

In response to the reviewers' comments, we have substantially changed our manuscript. Specifically, we have open-sourced the auditory masking stimuli and specified them in better detail in the text, we have improved the figures to reflect the data more closely, we have clarified the intracranial doseresponse relationship, we have elaborated in the introduction, and we have further discussed the possibility of direct neuromodulation. We hope that you agree these changes have helped to substantially improve the manuscript.

Public reviews

1.1) Despite the main conclusion of the authors stating that there is no dose-response effects of TUS on corticospinal inhibition, both the comparison of Isppa and MEP decrease for Exp 1 and 2, and the linear regression between MEP decrease (relative to baseline) and the estimated Isppa are significant, arguing the opposite, that there is a dose-response function which cannot be fully attributed to difference in sound (since the relationship in inversed, lower intracranial Isppa leads to higher MEP decrease). These results suggest that doseresponse function needs to be further studied in future studies.

We thank the reviewer for bringing up this point. While we are convinced our study provides no evidence for a direct neuromodulatory dose-response relationship, we have realized that the manuscript could benefit from improved clarity on this point.

A dose-response relationship between TUS intensity and motor cortical excitability was assessed by manipulating free-water Isppa (Figure 4C). Here, no significant effect of free-water stimulation intensity was observed for Experiment I or II, thus providing no evidence for a dose-response relationship (Section 3.2). To aid in clarity, ‘N.S.’ has been added to Figure 4C in the revised manuscript.

However, it is likely that the efficacy of TUS would depend on realized intracranial intensity, which we estimated with 3D simulations for on-target stimulation. These simulations resulted in an estimated intracranial intensity for each applied free-water intensity (i.e., 6.35 and 19.06 W/cm2), for each participant. We then tested whether inter-individual differences in intracranial intensity during on-target TUS affected MEP amplitude. We have realized that the original visualization used to display these data and its explanation was unintuitive. Therefore, we have completely revised Supplementary Figure 6. Because of the substantial length of this section, we have not copied it here. Please see the Supplementary material for the implemented improvements.

In brief, we now show MEP amplitudes on the y-axis, rather than expressing values a %change. This plot depicts how individuals with higher intracranial intensities during ontarget TUS exhibit higher MEP amplitudes. However, this same relationship is observed for active control and sound-sham conditions. If there were a direct neuromodulatory doseresponse relationship of TUS, this would be reflected as the difference between on-target and control conditions changing as the estimated intracranial intensity increases. This was not the case. Further, the fact that the difference between on-target stimulation and baseline changes across intracranial intensities is notable, but this occurs to an equal degree in the control conditions. Therefore, these data cannot be interpreted as evidence for a doseresponse relationship.

We hope the changes in Supplementary Figure 6 will make it clear that there is no evidence for direct intracranial dose-response effects.

1.2) Other methods to test or mask the auditory confound are possible (e.g., smoothed ramped US wave) which could substantially solve part of the sound issue in future studies or experiments in deaf animals etc... 

We agree with the reviewer’s statement. We aimed to replicate the findings of online motor cortical inhibition reported in prior work using a 1000 Hz square wave modulation frequency. While ramping can effectively reduce the auditory confound, as noted in the discussion, this is not feasible for the short pulse durations (0.1-0.3 ms) employed in the current study (Johnstone et al., 2021). We have further clarified this point in the methods section of the revised manuscript as follows:

“While ramping the pulses can in principle mitigate the auditory confound (Johnstone et al., 2021; Mohammadjavadi et al., 2019), doing so for such short pulse durations (<= 0.3 ms) is not effective. Therefore, we used a rectangular pulse shape to match prior work.”

Mitigation of the auditory confound by testing deaf subjects is a valid approach, and has now been added to the revised manuscript in the discussion as follows:

“Alternative approaches could circumvent auditory confounds by testing deaf subjects, or perhaps more practically by ramping the ultrasonic pulse to minimize or even eliminate the auditory confound.”

1.3) Dose-response function is an extremely important feature for a brain stimulation technique. It was assessed in Exp II by computing the relationship between the estimated intracranial intensities and the modulation of corticospinal excitability (Fig. 3b, 3c). It is not clear why data from Experiment I could not be integrated in a global intracranial dose-response function to explore wider ranges of intracranial intensities and MEP variability.

We chose not to combine data from Experiment 1 in a global intracranial dose-response function because TUS was applied at different fundamental frequencies and focal depths (Experiment I: 500 kHz, 35 mm; Experiment II: 250 kHz, 28 mm). We have now explicitly communicated this under Supplementary Figure 6:

“It was not appropriate to combine data from Experiments I and II given the different fundamental frequencies and stimulation depths applied… we ran simple linear models for Experiment II, which had a sufficient sample size (n = 27) to assess inter-individual variability.”

1.4) Furthermore, the dose response function as computed with the MEP change relative to baseline shows a significant effect (6.35W/cm2) or a trend (19.06 W/cm2) for a positive linear relationship. This comparison cannot disentangle the auditory confound from the pure neuromodulatory effect but given the direction of the relationship (lower Isppa associated with larger neuromodulatory effect), it is unlikely that it is driven by sound. This relationship is absent for the Active control condition or the Sound Sham condition, more or less matched for peripheral confound. This needs to be further discussed. 

Please refer to point 1.1

1.5) The clear auditory confound arises from TUS pulsing at audible frequencies, which can be highly subject to inter-individual differences. Did the authors individually titrate the auditory mask to account for this intra- and inter-individual variability in auditory perception? 

In Experiments I-III, the auditory mask was identical between participants. In Experiment IV, the auditory mask volume and signal-to-noise ratio were adjusted per participant. In the discussion we recommend individualized mask titration. However, we do note that masking successfully blinded participants in Experiment II, despite using uniform masking stimuli (Supplementary Figure 5).

1.6) How different is the masking quality when using bone-conducting headphones (e.g., Exp. 1) compared to in-ear headphones (e.g., Exp. 2)?

In our experience, bone conducting headphones produce a less clear, fuzzier, sound than in-ear headphones. However, in-ear headphones block the ear canal and likely result in the auditory confound being perceived as louder. We have included this information in the discussion of the revised manuscript:

“Titrating auditory mask quality per participant to account for intra- and inter-individual differences in subjective perception of the auditory confound would be beneficial. Here, the method chosen for mask delivery must be considered. While bone-conducting headphones align with the bone conduction mechanism of the auditory confound, they might not deliver sound as clearly as in-ear headphones or speakers. Nevertheless, the latter two rely on airconducted sound. Notably, in-ear headphones could even amplify the perceived volume of the confound by obstructing the ear canal.”

1.7) I was not able to find any report on the blinding efficacy of Exp. 1. Do the authors have some data on this? 

We do not have blinding data available for Experiment I. Following Experiment I, we decided it would be useful to include such an assessment in Experiment II.

1.8) Was the possibility to use smoothed ramped US wave form ever tested as a control condition in this set of studies, to eventually reduce audibility? For such fast PRF, for fast PRF, the slope would still need to be steep to stimulate the same power (AUC), it might not be as efficient. 

We indeed tested smoothing (ramping) the waveform. There was no perceptible impact on the auditory confound volume. Indeed, prior research has also indicated that ramping over

such short pulse durations is not effective (Johnstone et al., 2021). Taken together, we chose to continue with a square wave modulation as in prior TUS-TMS studies. We have updated the methods section of the manuscript with the following:

“While ramping the pulses can in principle mitigate the auditory confound (Johnstone et al., 2021; Mohammadjavadi et al., 2019), doing so for such short pulse durations (<= 0.3 ms) is not effective. Therefore, we used a rectangular pulse shape to match prior work.”

Importantly, our research shows that auditory co-stimulation can confound effects on motor excitability, and this likely occurred in multiple seminal TUS studies. While some preliminary work has been done on the efficacy of ramping in humans, future work is needed to determine what ramp shapes and lengths are optimal for reducing the auditory confound.

1.9) There are other models or experiments that need to be discussed in order to clearly disassociate the TUS effect from the auditory confound effect, for instance, testing deaf animal models or participants, or experiments with multi-region recordings (to rule out the effects of the dense structural connectivity between the auditory cortex and the motor cortex). 

The suggestion to consider multi-region recording in future experiments is important. Indeed, the effects of the auditory confound are expected to vary between brain regions. In the primary motor cortex, we observe a learned inhibition, which is perhaps supported by dense structural connectivity with the auditory system. In contrast, in perceptual areas such as the occipital cortex, one might expect tuned attentional effects in response to the auditory cue. We suggest that it is likely that the impact of the auditory confound also operates on a more global network level. It is reasonable to propose that, in a cognitive task for example, the confound will affect task performance and related brain activity, ostensibly regardless of the extent of direct structural connectivity between the auditory cortex and the (stimulated) region of interest.

Regarding the testing of deaf subjects, this has been included in the revised discussion as follows:

“Alternative approaches could circumvent auditory confounds by testing deaf subjects, or perhaps more practically by ramping the ultrasonic pulse to minimize or even eliminate the auditory confound.”

1.10) The concept of stochastic resonance is interesting but traditionally refers to a mechanism whereby a particular level of noise actually enhances the response of non-linear systems to weak sensory signals. Whether it applies to the motor system when probed with suprathreshold TMS intensities is unclear. Furthermore, whether higher intensities induce higher levels of noise is not straightforward neither considering the massive amount of work coming from other NIBS studies in particular. Noise effects are indeed a function of noise intensity, but exhibit an inverted U-shape dose-response relationship (Potok et al., 2021, eNeuro). In general SR is rather induced with low stimulation intensities in particular in perceptual domain (see Yamasaki et al., 2022, Neuropsychologia).  In the same order of ideas, did the authors compare inter-trials variability across the different conditions? 

We thank the reviewer for these insightful remarks. Indeed, stochastic resonance is a concept first formalized in the sensory domain. Recently, the same principles have been shown to apply in other domains as well. For example, transcranial electric noise (tRNS) exhibits similar stochastic resonance principles as sensory noise (Van Der Groen & Wenderoth, 2016). Indeed, tRNS has been applied to many cortical targets, including the motor system. In the current manuscript, we raise the question of whether TUS might engage with neuronal activity following principles similar to tRNS. One prediction of this framework would be that TUS might not modulate excitation/inhibition balance overall, but instead exhibit an inverted U-shape dose-dependent relationship with stochastic noise. Please note, we do not use the ‘suprathreshold TMS intensity’ to quantify whether noise could bring a sub-threshold input across the detection threshold, nor whether it could bring a sub-threshold output across the motor threshold. Instead, we use the MEP read-out to estimate the temporally varying excitability itself. We argue that MEP autocorrelation captures the mixture of temporal noise and temporal structure in corticospinal excitability. Building on the non-linear response of neuronal populations, low stochastic noise might strengthen weakly present excitability patterns, while high stochastic noise might override pre-existing excitability. It is therefore not the overall MEP amplitude, but the MEP timeseries that is of interest to us. Here, we observe a non-linear dose-dependent relationship, matching the predicted inverted U-shape. Importantly, we did not intend to assume stochastic resonance principles in the motor domain as a given. We have now clarified in the revised manuscript that we propose a putative framework and regard this as an open question:

“Indeed, human TUS studies have often failed to show a global change in behavioral performance, instead finding TUS effects primarily around the perception threshold where noise might drive stochastic resonance (Butler et al., 2022; Legon et al., 2018). Whether the precise principles of stochastic resonance generalize from the perceptual domain to the current study is an open question, but it is known that neural noise can be introduced by brain stimulation (Van Der Groen & Wenderoth, 2016). It is likely that this noise is statedependent and might not exceed the dynamic range of the intra-subject variability (Silvanto et al., 2007). Therefore, in an exploratory analysis, we exploited the natural structure in corticospinal excitability that exhibits as a strong temporal autocorrelation in MEP amplitude.”

Following the above reasoning, we felt it critical to estimate noise in the timeseries, operationalized as a t-1 autocorrelation, rather than capture inter-trial variability that ignores the timeseries history and requires data aggregation thereby reducing statistical power. Importantly, we would expect the latter index to capture global variability, putatively masking the temporal relationships which we were aiming to test. The reviewer raises an interesting option, inviting us to wonder if inter-trial variability might be sensitive enough, nonetheless. To this end, we compared inter-trial variability as suggested. This was achieved by first calculating the inter-trial variability for each condition, and then running a three-way repeated measures ANOVA on these values with the independent variables matching our autocorrelation analyses, namely, procedure (on-target/active control)intensity (6.35/19.06)masking (no mask/masked). This analysis did not reveal any significant interactions or main effects.

Author response table 1.

1.11) State-dependency/Autocorrelations: These values were extracted from Exp2 which has baseline trials. Can the authors provide autocorrelation values at baseline, with and without auditory mask?  Can the authors comment on the difference between the autocorrelation profiles of the active TUS condition at 6.35W/cm2 or at 19.06W/cm2. They should somehow be similar to my understanding.  Besides, the finding that TUS induces noise only when sound is present and at lower intensities is not well discussed. 

In the revised manuscript, we have now included baseline in the figure (Figure 4D). Regarding baseline with and without a mask, we must clarify that baseline involves only TMS (no mask), and sham involves TMS + masking stimulus (masked).

The dose-dependent relationship of TUS intensity with autocorrelation is critical. One possible observation would have been that TUS at both intensities decreased autocorrelation, with higher intensities evoking a greater reduction. Here, we would have concluded that TUS introduced noise in a linear fashion.

However, we observed that lower-intensity TUS in fact strengthened pre-existing temporal patterns in excitability (higher autocorrelation), while during higher-intensity TUS these patterns were overridden (lower autocorrelation). This non-linear relationship is not unexpected, given the non-linear responses of neurons.

If this non-linear dependency is driven by TUS, one could expect it to be present during conditions both with and without auditory masking. However, the preparatory inhibition effect of TUS likely depends on the salience of the cue, that is, the auditory confound. In trials without auditory masking, the salience of the confound in highly dependent on (transmitted) intensity, with higher intensities being perceived as louder. In contrast, when trials are masked, the difference in cue salience between lower and higher intensity stimulation in minimized. Therefore, we would expect for any nuanced dose-dependent direct TUS effect to be best detectable when the difference in dose-dependent auditory confound perception is minimized via masking. Indeed, the dose-dependent effect of TUS on autocorrelation is most prominent when the auditory confound is masked.

“In sum, these preliminary exploratory analyses could point towards TUS introducing temporally specific neural noise to ongoing neural dynamics in a dose-dependent manner, rather than simply shifting the overall excitation-inhibition balance. One possible explanation for the discrepancy between trials with and without auditory masking is the difference in auditory confound perception, where without masking the confound’s volume differs between intensities, while with masking this difference is minimized. Future studies might consider designing experiments such that temporal dynamics of ultrasonic neuromodulation can be captured more robustly, allowing for quantification of possible state-dependent or nondirectional perturbation effects of stimulation.”

1.12) Statistical considerations. Data from Figure 2 are considered in two-by-two comparisons. Why not reporting the ANOVA results testing the main effect of TUS/Auditory conditions as done for Figure 3. Statistical tables of the LMM should be reported. 

Full-factorial analyses and main effects for TUS/Auditory conditions are discussed from Section 3.2 onwards. These are the same data supporting Figure 2 (now Figure 3). We would like to note that the main purpose of Figure 2 is to demonstrate to the reader that motor inhibition was observed, thus providing evidence that we replicated motor inhibitory effects of prior studies. A secondary purpose is to visually represent the absence of direct and spatially specific neuromodulation. However, the appropriate analyses to demonstrate this are reported in following sections, from Section 3.2 onwards, and we are concerned that mentioning these analyses earlier will negatively impact comprehensibility.

Statistical tables of the LMMs are provided within the open-sourced data and code reported at the end of the paper, embedded within the output which is accessible as a pdf (i.e., analysis/analysis.pdf).

1.13) Startle effects: The authors dissociate two mechanisms through which sound cuing can drive motor inhibition, namely some compensatory expectation-based processes or the evocation of a startle response. I find the dissociation somehow artificial. Indeed, it is known that the amplitude of the acoustic startle response habituates to repetitive stimulation. Therefore, sensitization can well explain the stabilization of the MEP amplitude observed after a few trials. 

Thank you for bringing this to our attention. Indeed, an acoustic startle response would habituate over repetitive stimulation. A startle response would result in MEP amplitude being significantly altered in early trials. As the participant would habituate to the stimulus, the startle response would decrease. MEP amplitude would then return to baseline levels. However, this is not the pattern we observe. An alternative possibility is that participants learn the temporal contingency between the stimulus and TMS. Here, compensatory expectation-based change in MEP amplitude would be observed. In this scenario, there would be no change in MEP amplitude during early trials because the stimulus has not yet become informative of the TMS pulse timing. However, as participants learn how to predict TMS timing by the stimulus, MEP amplitude would decrease. This is also the pattern we observe in our data. We have clarified these alternatives in the revised manuscript as follows:

“Two putative mechanisms through which sound cuing may drive motor inhibition have been proposed, positing either that explicit cueing of TMS timing results in compensatory processes that drive MEP reduction (Capozio et al., 2021; Tran et al., 2021), or suggesting the evocation of a startle response that leads to global inhibition (Fisher et al., 2004; Furubayashi et al., 2000; Ilic et al., 2011; Kohn et al., 2004; Wessel & Aron, 2013). Critically, we can dissociate between these theories by exploring the temporal dynamics of MEP attenuation. One would expect a startle response to habituate over time, where MEP amplitude would be reduced during startling initial trials, followed by a normalization back to baseline throughout the course of the experiment as participants habituate to the starling stimulus. Alternatively, if temporally contingent sound-cueing of TMS drives inhibition, MEP amplitudes should decrease over time as the relative timing of TUS and TMS is being learned, followed by a stabilization at a decreased MEP amplitude once this relationship has been learned.”

1.14) Can the authors further motivate the drastic change in intensities between Exp1 and 2? Is it due to the 250-500 carrier difference? It this coming from the loss power at 500kHz? 

The change in intensities between Experiments I and II was not an intentional experimental manipulation. Following completion of data acquisition, our TUS system received a firmware update that differentially corrected the 250 kHz and 500 kHz stimulation intensities. In this manuscript, we report the actual free-water intensities applied during our experiments.

1.15) Exp 3: Did 4 separate blocks of TUS-TMS and normalized for different TMS intensities used with respect to baseline. But how different was it. Why adjusting and then re adjusting intensities? 

The TMS intensities required to evoke a 1 mV MEP under the four sound-sham conditions significantly differed from the intensities required for baseline. In the revised appendix, we have now included a figure depicting the TMS intensities for these conditions, as well as statistical tests demonstrating each condition required a significantly higher TMS intensity than baseline.

TMS intensities were re-adjusted to avoid floor effects when assessing the efficacy of ontarget TUS. Sound-sham conditions themselves attenuate MEP amplitude. This is also evident from the higher TMS intensities required to evoke a 1 mV MEP under these conditions. If direct neuromodulation by TUS would have further decreased MEP amplitude, the concern was that effects might not be detectible within such a small range of MEP amplitudes.

1.16) In Exp 4, TUS targeted the ventromedial WM tract. Since direct electrical stimulation on white matter pathways within the frontal lobe can modulate motor output probably through dense communication along specific white matter pathways (e.g., Vigano et al., 2022, Brain), how did the authors ensure that this condition is really ineffective? Furthermore, the stimulation might have covered a lot more than just white matter. Acoustic and thermal simulations would be helpful here as well. 

Thank you for pointing out this possibility. Ultrasonic and electrical stimulation have quite distinct mechanisms of action. Therefore, it is challenging to directly compare these two approaches. There is a small amount of evidence that ultrasonic neuromodulation of white matter tracts is possible. However, the efficacy of white matter modulation is likely much lower, given the substantially lesser degree of mechanosensitive ion channel expression in white matter as opposed to gray matter (Sorum et al., 2020, PNAS). Further, recent work has indicated that ultrasonic neuromodulation of myelinated axonal bundles occurs within the thermal domain (Guo et al., 2022, SciRep), which is not possible with the intensities administered in the current study. Nevertheless, based on Experiment IV in isolation, it cannot be definitively excluded that there TUS induced direct neuromodulatory effects in addition to confounding auditory effects. However, Experiment IV does not possess sufficient inferential power on its own and must be interpreted in tandem with Experiments I-III. Taken together with those findings, it is unlikely that a veridical neuromodulation effect is seen here, given the equivalent or lower stimulation intensities, the substantially deeper stimulation site, and the absence of an additional control condition in Experiment IV. This likelihood is further decreased by the fact that inhibitory effects under masking descriptively scale with the audibility of TUS.

Off-target effects such as unintended co-stimulation of gray matter when targeting white matter is always an important factor to consider. Unfortunately, individualized simulations for Experiment IV are not available. However, the same type of transducer and fundamental frequency was used as in Experiment II, for which we do have simulations. Given the size of the focus and the very low in-situ intensities extending beyond the main focal point, it is incredibly unlikely that effective stimulation was administered outside white matter in a meaningful number of participants. Nevertheless, the reviewer is correct that this can only be directly confirmed with simulations, which remain infeasible due to both technical and practical constraints. We have included the following in the revised manuscript:

“The remaining motor inhibition observed during masked trials likely owes to, albeit decreased, persistent audibility of TUS during masking. Indeed, MEP attenuation in the masked conditions descriptively scale with participant reports of audibility. This points towards a role of auditory confound volume in motor inhibition (Supplementary Fig. 8). Nevertheless, one could instead argue that evidence for direct neuromodulation is seen here. This unlikely for a number of reasons. First, white matter contains a lesser degree of mechanosensitive ion channel expression and there is evidence that neuromodulation of these tracts may occur primarily in the thermal domain (Guo et al., 2022; Sorum et al., 2021). Second, Experiment IV lacks sufficient inferential power in the absence of an additional control and must therefore be interpreted in tandem with Experiments I-III. These experiments revealed no evidence for direct neuromodulation using equivalent or higher stimulation intensities and directly targeting grey matter while also using multiple control conditions. Therefore, we propose that persistent motor inhibition during masked trials owes to continued, though reduced, audibility of the confound (Supplementary Fig. 8). However, future work including an additional control (site) is required to definitively disentangle these alternatives.”

1.17) Still for Exp 4. the rational for the 100% MSO or 120% or rMT is not clear, especially with respect to Exp 1 and 2. Equipment is similar as well as raw MEPs amplitudes, therefore the different EMG gain might have artificially increased TMS intensities. Could it have impacted the measured neuromodulatory effects?

Experiment IV was conducted independently at a different institute than Experiments I-II. In contrast to Experiments I-II, a gel pad was used to couple TUS to the participant’s head. The increased TMS-to-cortex distance introduced by the gel pad necessitates higher TMS intensities to compensate for the increased offset. In fact, in 9/12 participants, the intended intensity at 120% rMT exceeded the maximum stimulator output. In those cases, we defaulted to the maximum stimulator output (i.e., 100% MSO). We have clarified in the revised supplementary material as follows:

“We aimed to use 120% rMT (n =3). However, if this intensity surpassed 100% MSO, we opted for 100% MSO instead (n = 9). The mean %MSO was 94.5 ± 10.5%. The TMS intensities required in this experiment were higher than those required in Experiment I-II using the same TMS coil, though still within approximately one standard deviation. This is likely due to the use of a gel pad, which introduces more distance between the TMS coil and the scalp, thus requiring a higher TMS intensity to evoke the same motor activity.”

Regarding the EMG gain, this did not affect TMS intensities and did not impact the measured neuromodulatory effects. The EMG gain at acquisition is always considered during signal digitization and further analyses.

1.18) Exp. 4. It would be interesting to provide the changes in MEP amplitudes for those subjects who rated "inaudible" in the self-rating compared to the others. That's an important part of the interpretation: inaudible conditions lead to inhibition, so there is an effect. The auditory confound is not additive to the TUS effect. 

Previously, we only provided participant’s ratings of audibility, and showed that conditions that were rated as inaudible more often showed less inhibition, descriptively indicating that inaudible stimulation does not lead to inhibition. This interpretation is in line with our conclusion that the TUS auditory confound acts as a cue signaling the upcoming TMS pulse, thus leading to preparatory inhibition.

We have now included an additional plot and discussion in Supplementary Figure 8 (Subjective Report of TUS Audibility). Here, we show the change in MEP amplitude from baseline for the three continuously masked TUS intensities as in the main manuscript, but now split by participant rating of audibility. Descriptively, less audible sounds result in no marked change or a smaller change in MEP amplitude. This supports our conclusion that direct neuromodulation is not being observed here. When participants were unsure whether they could hear TUS, or when they did hear TUS, more inhibition was observed. However, this is still to a lesser degree than unmasked stimulation which was nearly always audible, and likely also more salient. This also supports our conclusion that these results indicate a role of cue salience rather than direct neuromodulation. Regarding masked conditions where participants were uncertain whether they heard TUS, the sound was likely sufficient to act as a cue, albeit potentially subliminally. After all, preparatory inhibition is not a conscious action undertaken by the participant either. We would also like to note that participants reported perceived audibility after each block, not after each trial, so selfreported audibility was not a fine-grained measurement. The data from Experiment IV suggest that the volume of the cue has an impact on motor inhibition. Taken together with the points mentioned in 1.16, it is not possible to conclude there is evidence for direct neuromodulation in Experiment IV.

1.19) I suggest to re-order sub panels of the main figures to fit with the chronologic order of appearance in the text. (e.g Figure 1 with A) Ultrasonic parameters, B) 3D-printed clamp, C) Sound-TMS coupling, D) Experimental condition). 

We have restructured the figures in the manuscript to provide more clarity and to have greater alignment with the eLife format.

2.1) Although auditory confounds during TUS have been demonstrated before, the thorough design of the study will lead to a strong impact in the field.

We thank the reviewer for recognition of the impact of our work. They highlight that auditory confounds during TUS have been demonstrated previously. Indeed, our work builds upon a larger research line on auditory confounds. The current study extends on the confound’s presence by quantifying its impact on motor cortical excitability, but perhaps more importantly by invalidating the most robust and previously replicable findings in humans. Further, this study provides a way forward for the field, highlighting the necessity of (in)active control conditions and tightly matched sham conditions for appropriate inferences in future work. We have amended the abstract to better reflect these points:

“Primarily, this study highlights the substantial shortcomings in accounting for the auditory confound in prior TUS-TMS work where only a flip-over sham control was used. The field must critically reevaluate previous findings given the demonstrated impact of peripheral confounds. Further, rigorous experimental design via (in)active control conditions is required to make substantiated claims in future TUS studies.”

2.2) A few minor [weaknesses] are that (1) the overview of previous related work, and how frequent audible TUS protocols are in the field, could be a bit clearer/more detailed

We have expanded on previous related work in the revised manuscript:

“Indeed, there is longstanding knowledge of the auditory confound accompanying pulsed TUS (Gavrilov & Tsirulnikov, 2012). However, this confound has only recently garnered attention, prompted by a pair of rodent studies demonstrating indirect auditory activation induced by TUS (Guo et al., 2022; Sato et al., 2018). Similar effects have been observed in humans, where exclusively auditory effects were captured with EEG measures (Braun et al., 2020). These findings are particularly impactful given that nearly all TUS studies employ pulsed protocols, from which the pervasive auditory confound emerges (Johnstone et al., 2021).”

2.3) The acoustic control stimulus can be described in more detail

We have elaborated upon the masking stimulus for each experiment in the revised manuscript as follows:

Experiment I: “In addition, we also included a sound-only sham condition that resembled the auditory confound. Specifically, we generated a 1000 Hz square wave tone with 0.3 ms long pulses using MATLAB. We then added white noise at a signal-to-noise ratio of 14:1. This stimulus was administered to the participant via bone-conducting headphones.”

Experiment II: “In this experiment, the same 1000 Hz square wave auditory stimulus was used for sound-only sham and auditory masking conditions. This stimulus was administered to the participant over in-ear headphones.”

Experiment III: “Auditory stimuli were either 500 or 700 ms in duration, the latter beginning 100 ms prior to TUS (Supplementary Fig. 3.3). Both durations were presented at two pitches. Using a signal generator (Agilent 33220A, Keysight Technologies), a 12 kHz sine wave tone was administered over speakers positioned to the left of the participant as in Fomenko and colleagues (2020). Additionally, a 1 kHz square wave tone with 0.5 ms long pulses was administered as in Experiments I, II, IV, and prior research (Braun et al., 2020) over noisecancelling earbuds.”

Experiment IV: “We additionally applied stimulation both with and without a continuous auditory masking stimulus that sounded similar to the auditory confound. The stimulus consisted of a 1 kHz square wave with 0.3 ms long pulses. This stimulus was presented through wired bone-conducting headphones (LBYSK Wired Bone Conduction Headphones). The volume and signal-to-noise ratio of the masking stimulus were increased until the participant could no longer hear TUS, or until the volume became uncomfortable.”

In the revised manuscript we have also open-sourced the audio files used in Experiments I, II, and IV, as well as a recording of the output of the signal generator for Experiment III:

“Auditory stimuli used for sound-sham and/or masking for each experiment are accessible here: https://doi.org/10.5281/zenodo.8374148.”

2.4) The finding that remaining motor inhibition is observed during acoustically masked trials deserves further discussion.

We agree. Please refer to points 1.16 and 1.18.

2.5) In several places, the authors state to have "improved" control conditions, yet remain somewhat vague on the kind of controls previous work has used (apart from one paragraph where a similar control site is described). It would be useful to include more details on this specific difference to previous work.

In the revised manuscript, we have clarified the control condition used in prior studies as follows:

Abstract:

“Primarily, this study highlights the substantial shortcomings in accounting for the auditory confound in prior TUS-TMS work where only a flip-over sham control was used.”

Introduction:

“To this end, we substantially improved upon prior TUS-TMS studies implementing solely flip-over sham by including both (in)active control and multiple sound-sham conditions.”

Methods:

“We introduced controls that improve upon the sole use of flip-over sham conditions used in prior work. First, we applied active control TUS to the right-hemispheric face motor area, allowing for the assessment of spatially specific effects while also better mimicking ontarget peripheral confounds. In addition, we also included a sound-only sham condition that closely resembled the auditory confound.”

2.6) I also wondered how common TUS protocols are that rely on audible frequencies. If they are common, why do the authors think this confound is still relatively unexplored (this is a question out of curiosity). More details on these points might make the paper a bit more accessible to TUS-inexperienced readers. 

Regarding the prevalence of the auditory confound, please refer to point 2.2.

Peripheral confounds associated with brain stimulation can have a strong impact on outcome measures, often even overshadowing the intended primary effects. This is well known from electromagnetic stimulation. For example, the click of a TMS pulse can strongly modulate reaction times (Duecker et al., 2013, PlosOne) with effect sizes far beyond that of direct neuromodulation. Unfortunately, this consideration has not yet fully been embraced by the ultrasonic neuromodulation community. This is despite long known auditory effects of TUS (Gavrilov & Tsirulnikov, 2012, Acoustical Physics). It was not until the auditory confound was shown to impact brain activity by Guo et al., and Sato et al., (2018, Neuron) that the field began to attend to this phenomenon. Mohammadjavadi et al., (2019, BrainStim) then showed that neuromodulation persisted even in deaf mice, and importantly, also demonstrated that ramping ultrasound pulses could reduce the auditory brainstem response (ABR). Braun and colleagues (2020, BrainStim) were the first bring attention to the auditory confound in humans, while also discussing masking stimuli. This was followed by a study from Johnstone and colleagues (2021, BrainStim) who did preliminary work assessing both masking and ramping in humans. Recently, Liang et al., (2023) proposed a new form of masking colourfully titled the ‘auditory Mondrian’. Further research into the peripheral confounds associated with TUS is on the way.

However, we agree that the confound remains relatively unexplored, particularly given the substantial impact it can have, as demonstrated in this paper. What is currently lacking is an assessment of the reproducibility of previous work that did not sufficiently consider the auditory confound. The current study constitutes a strong first step to addressing this issue, and indeed shows that results are not reproducible when using control conditions that are superior to flip-over sham, like (in)active control conditions and tightly matched soundsham conditions. This is particularly important given the fundamental nature of this research line, where TUS-TMS studies have played a central role in informing choices for stimulation protocols in subsequent research.

We would speculate that, with TUS opening new frontiers for neuroscientific research, there comes a rush of enthusiasm wherein laying the groundwork for a solid foundation in the field can sometimes be overlooked. Therefore, we hope that this work sends a strong message to the field regarding how strong of an impact peripheral confounds can have, also in prior work. Indeed, at the current stage of the field, we see no justification not to include proper experimental control moving forward. Only when we can dissociate peripheral effects from direct neuromodulatory effects can our enthusiasm for the potential of TUS be warranted.

2.7) Results, Fig. 2: Why did the authors not directly contrast target TUS and control conditions? 

Please refer to point 1.1.

2.8) The authors observe no dose-response effects of TUS. Does increasing TUS intensity also increase an increase in TUS-produced sounds? If so, should this not also lead to doseresponse effects? 

We thank the reviewer for this insightful question. Yes, increasing TUS intensity results in an increased volume of the auditory confound. Under certain circumstances this could lead to ‘dose-response’ effects. In the manuscript, we propose that the auditory confounds acts as a cue for the upcoming TMS pulse, thus resulting in MEP attenuation once the cue is informative (i.e., when TMS timing can be predicted by the auditory confound). In this scenario, volume can be taken as the salience of the cue. When the auditory confound is sufficiently salient, it should cue the upcoming TMS pulse and thus result in a reduction of MEP amplitude.

If we take Experiment II as an example (Figure 3B), the 19.06 W/cm2 stimulation would be louder than the 6.35 W/cm2 intensity. However, as both intensities are audible, they both cue the upcoming TMS pulse. One could speculate that the very slight (nonsignificant) further decrease for 19.06 W/cm2 stimulation could owe to a more salient cueing.

One might notice that MEP attenuation is less strong in Experiment I, even though higher intensities were applied. Directly contrasting intensities from Experiments I and II was not feasible due to differences in transducers and experimental design. From the perspective of sound cueing of the upcoming TMS pulse, the auditory confound cue was less informative in Experiment I than Experiment II, because TUS stimulus durations of both 100 and 500 ms were administered, rather than solely 500 ms durations. This could explain why descriptively less MEP attenuation was observed in Experiment I, where cueing was less consistent.

Perhaps more convincing evidence of a sound-based ‘dose-response’ effect comes from Experiment IV (Figure 4B). Here, we propose that continuous masking reduced the salience of the auditory confound (cue), and thus, less MEP attenuation was be observed. Indeed, we see less MEP change for masked stimulation. For the lowest administered volume during masked stimulation, there was no change in MEP amplitude from baseline. For higher volumes, however, there was a significant inhibition of MEP amplitude, though it was still less attenuation than unmasked stimulation. These results indicate a ‘doseresponse’ effect of volume. When the volume (intensity) of the auditory confound was low enough, it was inaudible over the continuous mask (also as reported by participants), and thus it did not act as a cue for the upcoming TMS pulse, therefore not resulting in motor inhibition. When the volume (intensity) was higher, less participants reported not being able to hear the stimulation, so the cue was to a given extent more salient, and in line with the cueing hypothesis more inhibition was observed.

In summary, because the volume of the auditory confound scales with the intensity of TUS, there may be dose-response effects of the auditory confound volume. Along the border of (in)audibility of the confound, as in masked trials of Experiment IV, we may observe dose-response effects. However, at clearly audible intensities (e.g., Experiment I & II), the size of such an effect would likely be small, as both volumes are sufficiently audible to act as a cue for the upcoming TMS pulse leading to preparatory inhibition.

2.9) I wonder if the authors could say a bit more on the acoustic control stimulus. Some sound examples would be useful. The authors control for audibility, but does the control sound resemble the one produced by TUS? 

Please refer to point 2.3.

2.10) The authors' claim that the remaining motor inhibition observed during masked trials is due to persistent audibility of TUS relies "only" on participants' descriptions. I think this deserves a bit more discussion. Could this be evidence that there is a TUS effect in addition to the sound effect? 

Please refer to points 1.16 and 1.18.

Author Response

Thank you for your letter and for the reviewers’ comments concerning our manuscript entitled “The cation channel mechanisms of subthreshold inward depolarizing currents in the VTA dopaminergic neurons and their roles in the depression-like behavior”. These comments are constructive and very helpful for improving our manuscript. We have studied comments carefully and have made provisional revision which we hope meet with approval. We also respond to the reviewer’s comments point by point as following.

Reviewer #1 (Public Review):

Comment 1:

The pharmacological tools used in this study are highly non-selective. Gd3+, used here to block NALCN is actually more commonly used to block TRP channels. 2-APB inhibits not only TRPC channels, but also TRPM and IP3 receptors while stimulating TRPV channels (Bon and Beech, 2013), while FFA actually stimulates TRPC6 channels while inhibiting other TRPCs (Foster et al., 2009).

We agree with the reviewer that the substances mentioned are not specific. Although we performed shRNA experiments against NALCN and TRPC6, we also used more specific pharmacological modulators for these two channels, L703,606 (the antagonist of NALCN)[1] and larixyl acetate (a potent TRPC6 inhibitor)[2]. The results are shown in figure 3E, F and figure 4C, E.

Comment 2:

-The multimodal approach including shRNA knockdown experiments alleviates much of the concern about the non-specific pharmacological agents. Therefore, the author's claim that NALCN is involved in VTA dopaminergic neuron pacemaking is well-supported.

-However, the claim that TRPC6 is the key TRPC channel in VTA spontaneous firing is somewhat, but not completely supported. As with NALCN above, the pharmacology alone is much too non-specific to support the claim that TRPC6 is the TRP channel responsible for pacemaking. However, unlike the NALCN condition, there is an issue with interpreting the shRNA knockdown experiments. The issue is that TRPC channels often form heteromers with TRPC channels of other types (Goel, Sinkins and Schilling, 2002; Strübing et al., 2003). Therefore, it is possible that knocking down TRPC6 is interfering with the normal function of another TRPC channel, such as TRPC7 or TRPC4.

From our single-cell RNA-seq results, TRPC7 and TRPC4 are found not to be present broadly like TRPC6 in the VTA DA neurons. And in experiments using single cell PCR (sFig. 9A), only a very small proportion of TRPC6-positive DA cells (DAT+) expressed TRPC4 (sFig. 9Bi) or TRPC7 (sFig. 9Bii), in consistent with the results of single-cell RNA-seq (Fig.2). Therefore, it is possible that knocking down TRPC6 maybe not interfering with the normal function of another TRPC channel, such as TRPC7 or TRPC4.

Comment 3:

The claim that TRPC6 channels in the VTA are involved in the depressive-like symptoms of CMUS is supported.

• However, the connection between the mPFC-projecting VTA neurons, TRPC6 channels, and the chronic unpredictable stress model (CMUS) of depression is not well supported. In Figure 2, it appears that the mPFC-projecting VTA neurons have very low TRPC6 expression compared to VTA neurons projecting to other targets. However, in figure 6, the authors focus on the mPFC-projecting neurons in their CMUS model and show that it is these neurons that are no longer sensitive to pharmacological agents non-specifically blocking TRPC channels (2-APB, see above comment). Finally, in figure 7, the authors show that shRNA knockdown of TRPC6 channels (in all VTA dopaminergic neurons) results in depressive-like symptoms in CMUS mice. Due to the low expression of TRPC6 in mPFC-projecting VTA neurons, the author's claims of "broad and strong expression of TRPC6 channels across VTA DA neurons" is not fully supported. Because of the messy pharmacological tools used, it cannot be clamed that TRPC6 in the mPFC-projecting VTA neurons is altered after CMUS. And because the knockdown experiments are not specific to mPFC-projecting VTA neurons, it cannot be claimed that reducing TRPC6 in these specific neurons is causing depressive symptoms.

The reason we focused on the mPFC-projecting VTA DA neurons is that this pathway is indicated in depressive-like behaviors of the CMUS model[3-5]. Although mPFC-projecting VTA DA neurons seem have lower level of TRPC6, we reason they are still functional there. However, we do agree with the reviewer that the statement “broad and strong expression of TRPC6 channels across VTA DA neurons" is not fully supported. We have changed the statements based on the reviewer suggestion. Furthermore, we did selectively knockdown TRPC6 in the mPFC-projecting VTA DA neurons, and then studied the behavior (Fig.8).

Comment 4:

It is important to note that the experiments presented in Figure 1 have all been previously performed in VTA dopaminergic neurons (Khaliq and Bean, 2010) including showing that low calcium increases VTA neuron spontaneous firing frequency and that replacement of sodium with NMDG hyperpolarizes the membrane potential.

We agree with reviewer that similar experiments have been performed previously [6] for the flow of our manuscript and for general readers.

Comment 5:

-The authors explanation for the increase in firing frequency in 0 calcium conditions is that calcium-activated potassium channels would no longer be activated. However, there is a highly relevant finding that low calcium enhances the NALCN conductance through the calcium sensing receptor from Dejian Ren's lab (Lu et al., 2010) which is not cited in this paper. This increase in NALCN conductance with low calcium has been shown in SNc dopaminergic neurons (Philippart and Khaliq, 2018), and is likely a factor contributing to the low-calcium-mediated increase in spontaneous VTA neuron firing.

We agree with the reviewer and thanks for the suggestions. A discussion for this has been added.

Comment 6:

-One of the only demonstrations of the expression and physiological significance of TRPCs in VTA DA neurons was published by (Rasmus et al., 2011; Klipec et al., 2016) which are not cited in this paper. In their study, TRPC4 expression was detected in a uniformly distributed subset of VTA DA neurons, and TRPC4 KO rats showed decreased VTA DA neuron tonic firing and deficits in cocaine reward and social behaviors.

We thank the reviewer for the suggestion. The references and a discussion for this has been added.

Comment 7:

• Out of all seven TRPCs, TRPC5 is the only one reported to have basal/constitutive activity in heterologous expression systems (Schaefer et al., 2000; Jeon et al., 2012). Others TRPCs such as TRPC6 are typically activated by Gq-coupled GPCRs. Why would TRPC6 be spontaneously/constitutively active in VTA DA neurons?

In a complex neuronal environment where VTA DA neurons are located, multiple modulatory factors including the GPCRs could be dynamically active, this could lead to the activation of TRP channels including TRPC6.

Comment 8:

A new paper from the group of Myoung Kyu Park (Hahn et al., 2023) shows in great detail the interactions between NALCN and TRPC3 channels in pacemaking of SNc DA neurons.

The reference mentioned has been added. We thank the reviewer.

Reviewer #2 (Public Review):

Comment 1:

These results do not show that TRPC6 mediates stress effects on depression-like behavior. As stated by the authors in the first sentence of the final paragraph, "downregulation of TRPC6 proteins was correlated with reduced firing activity of the VTA DA neurons, the depression-like behaviors, and that knocking down of TRPC6 in the VTA DA neurons confer the mice with depression behaviors." Therefore, the results show associations between TRPC6 downregulation and stress effects on behavior, occlusion of the effects of one by the other on some outcome measures, and cell manipulation effects that resemble stress effects. There is no experiment that shows reversal of stress effects with cell/circuit-specific TRPC6 manipulations. Please adjust the title, abstract and interpretation accordingly.

We agree with the reviewer’s suggestion. The title was changed to ‘’The cation channel mechanisms of subthreshold inward depolarizing currents in the VTA dopaminergic neurons and their roles in the chronic stress-induced depression-like behavior” and the abstract and interpretation were also adjusted accordingly.

Comment 2:

Statistical tests and results are unclear throughout. For all analyses, please report specific tests used, factors/groups, test statistic and p-value for all data analyses reported. In some cases, the chosen test is not appropriate. For example, in Figure 6E, it is not clear how an experiment with 2 factors (stress and drug) can be analyzed with a 1-way RM ANOVA. The potential impact of inappropriate statistical tests on results makes it difficult to assess the accuracy of data interpretation.

We have redone the statistical analysis as suggested by the reviewer and added specific tests used, factors/groups, test statistic and p-value for all data analyses into the figure legends of the revised manuscript.

Comment 3:

Why were only male mice used? Please justify and discuss in the manuscript. Also, change the title to reflect this.

Although most similar previous studies used male mice or rats[7, 8], we do agree with the reviewer that the female animals should also be tested, in consideration possible role of sex hormones, as such we repeated some key experiments on female mice (sFig.1.6.8. and 13).

Comment 4:

Number of recorded cells is very low in Figure 1. Where in VTA did recordings occur? Given the heterogeneity in this brain region, this n may be insufficient. Additional information (e.g., location within VTA, criteria used to identify neurons) should be included. Report the number of mice (i.e., n = 6 cells from X mice) in all figures.

Yes indeed, the number here is not high. More experiments were performed to increase the N/n number. And the location of recorded cells in VTA and the number of used mice is now shown in all figures; criteria to identify neurons is stated in the Methods-Identification of DA neurons and electrophysiological recordings. At the end of electrophysiological recordings, the recorded VTA neurons were collected for single-cell PCR. VTA DA neurons were identified by single-cell PCR for the presence of TH and DAT.

Comment 5:

Authors refer to VTA DA neurons as those that are DAT+ in line 276, although TH expression is considered the standard of DAergic identity, and studies (e.g., Lammel et al, 2008) have shown that a subset of VTA DA neurons have low levels of DAT expression. Authors should reword/clarify that these are DAT-expressing VTA DA neurons.

The study published by Lammel[9] in 2015 has shown the low dopamine specificity of transgene expression in ventral midbrain of TH-Cre mice; on the other hand, DAT-Cre mice exhibit dopamine-specific Cre expression patterns, although DAT-Cre mice are likely to suffer from their own limitations (for example, low DAT expression in mesocortical DA neurons may make it difficult to target this subpopulation, see Lammel et al., 2008[10]).Hence, in our study, the DAT was used as criteria to identify DAT neurons. Of course, TH and DAT were all tested in single-cell PCR to identify whether the recorded cells were DA neurons.

Comment 6:

Neuronal subtype proportions should be quantified and reported (Fig. 1Aii).

Neuronal subtype proportions are now quantified and reported in Fig. 1Aii.

Comment 7:

In addition to reporting projection specificity of neurons expressing specific channels, it would be ideal to report these data according to spatial location in VTA.

The spatial location of recorded cells in VTA are now shown in all figures.

Comment 8:

The authors state that there are a small number of Glut neurons in VTA, then they state that a "significant proportion" of VTA neurons are glutamatergic.

Thanks, “a significant proportion of neurons” has been changed to “less than half of sequenced DA neurons”.

Comment 9:

It is an overstatement that VTA DA neurons are the key determinant of abnormal behaviors in affective disorders.

Thanks, we have amended the statement to that “Dopaminergic (DA) neurons in the ventral tegmental area (VTA) play an important role in mood, reward and emotion-related behaviors”.

Reviewer #3 (Public Review):

Comment 1:

The authors of this study have examined which cation channels specifically confer to ventral tegmental area dopaminergic neurons their autonomic (spontaneous) firing properties. Having brought evidence for the key role played by NALCN and TRPC6 channels therein, the authors aimed at measuring whether these channels play some role in so-called depression-like (but see below) behaviors triggered by chronic exposure to different stressors. Following evidence for a down-regulation of TRPC6 protein expression in ventral tegmental area dopaminergic cells of stressed animals, the authors provide evidence through viral expression protocols for a causal link between such a down-regulation and so-called depression-like behaviors. The main strength of this study lies on a comprehensive bottom-up approach ranging from patch-clamp recordings to behavioral tasks. However, the interpretation of the results gathered from these behavioral tasks might also be considered one main weakness of the abovementioned approach. Thus, the authors make a confusion (widely observed in numerous publications) with regard to the use of paradigms (forced swim test, tail suspension test) initially aimed (and hence validated) at detecting the antidepressant effects of drugs and which by no means provide clues on "depression" in their subjects. Indeed, in their hands, the authors report that stress elicits changes in these tests which are opposed to those theoretically seen after antidepressant medication. However, these results do not imply that these changes reflect "depression" but rather that the individuals under scrutiny simply show different responses from those seen in nonstressed animals. These limits are even more valid in nonstressed animals injected with TRPC6 shRNAs (how can 5-min tests be compared to a complex and chronic pathological state such as depression?). With regard to anxiety, as investigated with the elevated plus-maze and the open field, the data, as reported, do not allow to check the author's interpretation as anxiety indices are either not correctly provided (e.g. absolute open arm data instead of percents of open arm visits without mention of closed arm behaviors) or subjected to possible biases (lack of distinction between central and peripheral components of the apparatus).

We agree with the reviewer that behavior tests we used here is debatable whether they represent a real depression state, and this is an open question that could be discussed from different respective. Since these testes (forced swimming and tail suspension), as the reviewer noted, were “widely observed in numerous publications”, we used these seemly only options to reflect a “depression-like” state. One could argue that since these testes were initially used for testing antidepressants (“validated”), with decreased immobility time as indications of anti-depressive effects, why not an increased immobility time reflect a “depression-like” state. As for anxiety tests, the data concerning the elevated plus-maze are also changed based on the reviewer’s suggestion.

Recommendations for the authors: please note that you control which, if any, revisions, to undertake

Reviewer #1 (Recommendations For The Authors):

Recommendation 1 for improving the paper:

-The paper needs extensive editing for both overall structural clarity and for the high number of typos and grammatical errors.

We thank the reviewer’s suggestion. The revised manuscript has been edited extensively.

Recommendation 2 for improving the paper:

-Retrobeads are often toxic to cells and build up with increasing time. It is surprising that the authors wait 14-21 days for retrobead expression in their target cells. It is also a problem that the mPFC projecting cells have a longer time with the retrobeads than the other projection-targeting cells because the toxicity could be more extensive with the longer wait time thus confounding the results. The authors should repeat some mPFC experiments at the 14 day time point to confirm that the longer time with the beads is not influencing the differential effects in these cells.

According to the methods published by Stephan Lammel and Jochen Roeper, “For sufficient labeling, survival periods for retrograde tracer transport depended on respective injection areas: DS and NAc lateral shell, 7 days; NAc core, NAc medial shell, and BLA, 14 days; and mPFC, 21 days[10]”, we did the experiments related to mPFC projecting cells at the 21 day time point. Consistent with the mentioned above, the labeled mPFC projecting cells at 14 day time point, is not sufficient, compared with this at 21 day time point, which is shown as followings.

Author response image 1.

Confocal images showing the anatomical distribution of mPFC-projecting DA neurons labelled with retrobeads (red) in the VTA after DAT-immunofluorescence (green) staining at different day time point (A, 14d; B, 21d) after retrobeads injection; Scale bars=10 μm.

Recommendation 3 for improving the paper:

-The experiment with FFA in Figure 4E seems weird. Why is there no baseline before the FFA application? And why is the baseline trending downward immediately? The authors should explain why this example experiment is presented differently from all the others.

We apologize for this part that this example time-course is not typical. Since the FFA is not specific antagonist for TRPC6 and actually stimulates TRPC6 channels, we repeated the experiments with a more specific pharmacological modulator for TRPC6, larixyl acetate (LA), and the results are shown in Figure 4C and 4F.

Recommendation 4 for improving the paper:

-It would be much more useful to see exact p values in the text, as it aids in interpreting the 'insignificance' of specific comparisons. Specifically, in Figure 5F, the 2-APB looks like it is having a small effect, and the already low firing rate (due to the TRPC6 knockdown) makes a big effect less likely. It would be useful to know what the actual p value is here (and everywhere).

OK. We now report all P values in the figure legends of the revised version.

Recommendation 5 for improving the paper:

-In the results, it should be explained that the "RMP" of VTA DA neurons was obtained by treating the cells with TTX.

A sentence indicating the presence of TTX when measuring “RMP” is added in the Results part of the revised version.

Recommendation 6 for improving the paper:

-The spacing of the panels in the figures is somewhat odd. The figures could be more compact.

Thanks, we have re-arranged all figures.

Recommendation 7 for improving the paper:

The paper is difficult to read because of significant grammatical errors. Here are some examples by line number, but this list is not at all exhaustive.

We thank the reviewer for pointing out grammatical errors and we corrected them.

Reviewer #2 (Recommendations For The Authors):

Recommendation 1 for improving the paper:

Fix typos: e.g., change HCH to HCN, change EMP to EPM, "these finding", "compact par" should read "pars compacta", "substantial" in line 475 should read "substantia", Incomplete sentences on line 73 and line 107, etc. Also, what is meant by "autonomic" firing activity? What is meant by "expression files"? Change "depression behaviors" to depression-like behaviors. "The HCN" as written in line 69 is a bit misleading, as HCN channels in the heart and brain are different members of a family of channels, although as written in the text, it seems that they are identical. In Figure 2, rearrange order of brain regions (e.g., from "BLA-VTA" to "VTA-BLA"), because as written, it seems that the focus is on projections into the VTA from each brain region, rather than VTA neurons that project to each respective region.

We thank the reviewer for pointing out these errors and we corrected them. Autonomic firing activity has been changed to spontaneous firing activity. Expression files has been changed to expression levels. All the “depression behavior” have been changed to depression-like behaviors. In the Figure 2, all “xx-VTA” have been changed to “VTA-xx”.

Reviewer #3 (Recommendations For The Authors):

Recommendation 1 for improving the paper:

Methodology: as opposed to sFig. 8 where the order through which mice were repeatedly tested is precise, such a key information is lacking in Fig. 6 as well as in the Methods section (for example, when such traumatic stress as forced swimming is performed with regard to the other tests?). Relevant to this point is the possible bias triggered by such chronological testing as exposure to the forced swim test likely affects the behaviors recorded in the other tests. Furthermore, the way this test is conducted is appealing as it is mentioned that the water depth was set to 10 cms which is quite low given that immobility scores might be affected by the ability of mice to stand on their tails.

With regard to the elevated plus-maze, data are erroneously provided. Absolute values regarding open arm behaviors should be provided as percentages of the number of visits (or time spent therein) over the total (open + closed) number of arm visits. Indeed, closed arm visits should also be provided. This variable, also considered an index of locomotor activity, would allow the reader to exclude any effect of locomotion on the exploration in the open field.

As they stand, data in the open field seem to indicate parallel changes at the center(center time) and the periphery (total distance), hence suggesting locomotor effects rather than anxiogenic effects. Data related to the center and the periphery should be clearly distinguished. Lastly, the number of weeks allowed for the mice to recover from surgeries aimed at delivering viruses are not mentioned. This is important as it could have affected the amplitude of the sensitivity to the stressors.

We thank the reviewer for the suggestion. The lack information in Figure 6 and the Methods is now supplied. We apologize for the wrong number of “10 cm” in the forced swimming test, this has been corrected. The data concerning the elevated plus-maze are also changed based on the reviewer’s suggestion. For a possible role of locomotor effect, we tested the mice on the rota-rod test. From the result, there is no difference in locomotor activity between control and depressed-like mice (sFig.10G, sFig.12I and sFig.13G). We modified the experimental procedure timeline in Figure 6 and in the method- AAV for gene knockdown or overexpression and viral construct and injection, we added “Mice were singly housed with enough food and water to recover for 4-5 weeks after injection of virus, before behavior tests and electrophysiological recordings.” to report the number of weeks allowed for the mice to recover from surgeries aimed at delivering virus.

Recommendation 2 for improving the paper:

Results/conclusions: as yet mentioned, the authors make a confusion in the interpretation of their tail suspension tests and forced swimming tests. I acknowledge that such a confusion is frequent but it is important to note that the tests used by the authors were INITIALLY aimed at detecting the antidepressant effects of drugs under investigation. However, it is not because a test reveals such antidepressant properties that they also provide indices of depression. The authors will surely agree that it is unlikely that a 5-min test provides a model of a chronic pathology accounted for by a complex intrication between genetics and environmental factors. I would propose the authors to read for example Molendijk and De Kloet (Eur J Neurosci 2022). I think that the authors should just neutrally mention their results without any interpretation related to depression. On the other hand, what could have been interesting is to test whether the so-called "depressive-like" responses recorded in the study were sensitive to chronic antidepressant treatments. This would have allowed the authors to further suggest some relevance (if any) with depression-like pathologies.

As we discussed above, we again agree with the reviewer’s concern. However, if as stated by the reviewer that “However, it is not because a test reveals such antidepressant properties that they also provide indices of depression”, then the experiments suggested by the reviewer “….. to test whether the so-called "depressive-like" responses recorded in the study were sensitive to chronic antidepressant treatments”

Recommendation 3 for improving the paper:

A close examination of the responses to CMUS or chronic restraint suggests that indeed two populations of animals were detected, possibly sensitive and resilient to these stressors. Did the authors try to examine this possibility?

Based on the results of behavior test in CMUS and CRS, animals might be divided into two populations of animals highly-sensitive and moderately-sensitive ones.

Recommendation 4 for improving the paper:

There are some text changes that need to be performed:

Page 2 line 46: ref 4 uses a social stress model which brings no clearcut evidence for it being a "depression" model. Indeed, this model can also be suggested to be a model of chronic anxiety (Kalueff et al., Science 2006; Chaouloff, Cell tissue Res 2013), hence indicating that VTA dopaminergic neurons might also be involved in anxiety.

page 11, line 329: the references supporting the hypothesis that VTA DA neurons are linked to depression cannot be found in the reference list (10-15 do not correspond to the appropriate references).

page 11, line 3341: reference 47 does not fit with the authors' assertion as it did not include any behavior.

Fig. S8: body weight data are likely provided as changes rather than absolute values (e.g. 8 g)

We agreed with the reviewer’s comments. The line 46“……such as depression states” has been changed to “such as depression- or anxiety-related states”. And we corrected the references in line 329 and 341. Finally, the body weight has been changed to the change in body weight.

References:

1. Um, K.B., et al., TRPC3 and NALCN channels drive pacemaking in substantia nigra dopaminergic neurons. Elife, 2021. 10.

2. Urban, N., et al., Identification and Validation of Larixyl Acetate as a Potent TRPC6 Inhibitor. Mol Pharmacol, 2016. 89(1): p. 197-213.

3. Zhong, P., et al., HCN2 channels in the ventral tegmental area regulate behavioral responses to chronic stress. Elife, 2018. 7.

4. Liu, D., et al., Brain-derived neurotrophic factor-mediated projection-specific regulation of depressive-like and nociceptive behaviors in the mesolimbic reward circuitry. Pain, 2018. 159(1): p. 175.

5. Walsh, J.J. and M.H. Han, The Heterogeneity of Ventral Tegmental Area Neurons: Projection Functions in a Mood-Related Context. Neuroscience, 2014. 282: p. 101-108.

6. Khaliq, Z.M. and B.P. Bean, Pacemaking in dopaminergic ventral tegmental area neurons: depolarizing drive from background and voltage-dependent sodium conductances. J Neurosci, 2010. 30(21): p. 7401-13.

7. Li, L., et al., Selective targeting of M-type potassium K(v) 7.4 channels demonstrates their key role in the regulation of dopaminergic neuronal excitability and depression-like behaviour. Br J Pharmacol, 2017. 174(23): p. 4277-4294.

8. Friedman, A.K., et al., Enhancing depression mechanisms in midbrain dopamine neurons achieves homeostatic resilience. Science, 2014. 344(6181): p. 313-9.

9. Lammel, S., et al., Diversity of transgenic mouse models for selective targeting of midbrain dopamine neurons. Neuron, 2015. 85(2): p. 429-38.

10. Lammel, S., et al., Unique properties of mesoprefrontal neurons within a dual mesocorticolimbic dopamine system. Neuron, 2008. 57(5): p. 760-73.

Author Response

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

Reviewer #1:

This work describes a new and powerful approach to a central question in ecology: what are the relative contributions of resource utilisation vs interactions between individuals in the shaping of an ecosystem? This approach relies on a very original quantitative experimental set-up whose power lies in its simplicity, allowing an exceptional level of control over ecological parameters and of measurement accuracy.

In this experimental system, the shared resource corresponds to 10^12 copies of a fixed single-stranded target DNA molecule to which 10^15 random single-stranded DNA molecules (the individuals populating the ecosystem) can bind. The binding process is cycled, with a 1000x-PCR amplification step between successive binding steps. The composition of the population is monitored via high-throughput DNA sequencing. Sequence data analysis describes the change in population diversity over cycles. The results are interpreted using estimated binding interactions of individuals with the target resource, as well as estimated binding interactions between individuals and also self-interactions (that can all be directly predicted as they correspond to DNA-DNA interactions). A simple model provides a framework to account for ecosystem dynamics over cycles. Finally, the trajectory of some individuals with high frequency in late cycles is traced back to the earliest cycles at which they are detected by sequencing. Their propensities to bind the resource, to form hairpins, or to form homodimers suggest how different interaction modes shape the composition of the population over cycles.

The authors report a shift from selection for binding to the resource to interactions between individuals and self-interactions over the course of cycles as the main drivers of their ecosystem. The outcome of the experiment is far from trivial as the individual resource binding energy initially determines the relative enrichment of individuals, and then seems to saturate. The richness of the population dynamics observed with this simple system is thus comparable to that found in some natural ecosystems. The findings obtained with this new approach will likely guide the exploration of natural ecosystems in which parameters and observables are much less accessible.

My review focuses mainly on the experimental aspects of this work given my own expertise. The introduction exposes very convincingly the scientific context of this work, justifying the need for such an approach to address questions pertaining to ecology. The manuscript describes very clearly and rigorously the experimental setup. The main strengths of this work are (i) the outstanding originality of the experimental approach and (ii) its simplicity. With this setup, central questions in ecology can be addressed in a quantitative manner, including the possibility of running trajectories in parallel to generalize the findings, as reported here. Technical aspects have been carefully implemented, from the design of random individuals bearing flanking regions for PCR amplification, binding selection and (low error) amplification protocols, and sequencing read-out whose depth is sufficient to capture the relevant dynamics.<br /> :<br /> We thank the reviewer for summarizing our work and the main findings in a very clear and effective manner.

One missing aspect in the data analysis is the quantification of the effect of PCR amplification steps in shaping the ecosystem (to be modeled if significant). In addition, as it stands the current work does not fully harness the power of the approach. For instance, with this setup, one can tune the relative contributions of binding selection vs amplification for instance (to disentangle forces that shape the ecosystem). One can also run cycles with new DNA individuals, designed with arbitrarily chosen resource binding vs self-binding, that are predicted to dominate depending on chosen ecological parameters. I have three main recommendations to the authors:

1) PCR amplification steps (and not only binding selection steps) should be taken into account when interpreting the outcome of experiments.

2) More generally, a systematic analysis of the possible modes of propagation of a DNA molecule from one cycle to the next, including those considered as experimental noise, would help with interpreting the results.

3) Testing experimentally the predictions from the analysis and the modelling of results would strengthen the case for this approach.

Despite its conceptual simplicity, our approach has indeed a few experimental handles that enable exploring a relevant variety of conditions much beyond those described in this paper, of which we are very aware. These involve selection vs. amplification or set the stage to explore competition, parasitism or cooperation among specific species, as the reviewer points out, but also introduce mutations and explore the kinetics of evolution in static or dynamic environments. Ongoing experiments are considering some of these conditions. We modified the text to mention more explicitly these possibilities, which are now mentioned in p11 lines 376-378 and lines 416-417. The three points raised by the reviewer helped us to further improve and clarify strengths and limitations of our work, as detailed below.

Regarding the first point, here are my suggestions :

• Run one cycle of just amplification vs 'binding + amplification', or simply increase the number of PCR cycles (and subsample the product) to check whether it impacts the population composition, in particular for sequences with predictions derived from the current analysis.

The point raised by the reviewer is indeed very relevant and not discussed in our manuscript. Prompted by the reviewer’s comment, we performed two new experiments to distinguish resource-binding selection from PCR amplification effects.

First, we performed a negative control experiment in which we performed the “selection step” with bear beads, i.e. beads without with no DNA grafted on them. We then compared the results with the corresponding results of the original experiments on Oligo 1 and 2.

After 6 cycles, the most abundant sequence in the negative dataset has a relative occurrence of 0.05%, whereas the dominant strand in Oligo 1 and Oligo 2 has an abundance of 8% and 16%, respectively, i.e. 40-80 times larger.

This indicates that the drift due to non-specific binding + PCR amplification is at least two orders of magnitude smaller than the selection induced by the affinity with the resource.

This results are now cited in p14 lines 468-470, and described in Appendix 1, Experimental controls.

Second, we tested the effect of PCR amplification on the selection process. We exploited the fact that we have aliquots for each generation of our evolution experiment, which we sampled and saved after PCR and before sequencing. We thus chose a specific generation - specifically generation 9 from Oligo 1 experiments - and performed another PCR round we proceeded directly to sequencing with no beadsselection step. We then compared the ensemble of oligos obtained in this way, which we named Oligo 1 “cycle 9 replica”, with both the original Oligo1 cycle 9, and with Oligo1 cycle 10.

We sampled 20 times 4 x 10^5 sequences from the cycle 9 dataset, from cycle 9 replica and from cycle 10 with a bootstrap approach. To compare the three systems we extracted the fraction of the population of each covered by the 10 most abundant individuals. The results are shown in Figure 2 - Figure Supplement 4. In the figure caption further details on the analysis can be found. The similarity between cycle 9 and cycle 9 replica and the marked difference between cycle 9 replica and cycle 10

indicates that the relevant part of the selection is indeed performed by the resourcebinding mechanism, while drifts induced by PCR play a secondary role.

As a further check, we compared the specific sequences across the 20 samples in cycle 9 and cycle 9 replica datasets and found that the 10 most abundant sequences are almost always the same. In particular, the first 8/9 are always the same, possibly shuffled.

These new pieces of evidence are now cited in p14 lines 483-484 and described in Appendix 1, Experimental controls.

• Sequencing read-out includes the same PCR protocol as the one used for amplification steps, so read-out potentially has an effect on the composition of the ecosystem. Again, varying the number of PCR cycles is a direct way to test this.

The PCR amplification involved in the read-out might have a minor effect on the sequencing outcome but not on the composition of the ecosystem. In fact, the sample that undergoes sequencing is taken from the pool at each cycle, and not inserted back into it. Thus, it does not participate in the following selection steps. This is specified in the text at p3 line 104

• Could self-interactions (hairpins of homodimers) benefit individuals during amplification steps? The role of self-interactions during binding selection steps could also be tested directly over one cycle (again varying the relative weight of the binding vs amplification to disentangle both).

Our choice of conditions for PCR amplification were thought to minimize effects of this type. PCR amplification is carried out at 68 C, a temperature at which, given the level of self and mutual complementarity in the sequences analyzed in the text, hairpins or homodimers should be melted and thus have no effect. This is specified in the text at p. 14 lines 479-480 However, if an effect is present, it gives a disadvantage (rather than an advantage) to self-interacting individuals. For the amplification step we used Q5® Hot Start HighFidelity DNA Polymerase, which does not possess strand displacement activity. Therefore, in theory, if during amplification the polymerase encounters a double strand portion, it stops and synthesizes only a truncated product, which will be then lost during the purification step. In other words, sequences with secondary and/or tertiary structures are less likely to be amplified during the polymerization step. As a consequence, a DNAi that is characterized by this kind of structures, will be negatively selected even in the case of optimal binding to the resource, and will be underrepresented in the pool.

About the second point:

• Regarding the effect of sampling (sequencing read-out), PCR amplification errors: explicitly check the consistency of observations with the expected outcome, in the methods section (right now these aspects are only briefly mentioned in the main text), which would highlight again the level of control and accuracy of the system.

Hoping to have well interpreted the request, we performed a technical replicate sequencing Oligo 1 cycle 9 again and analyzed the sequences that have at least 100 reads (corresponding to 27.42% of the total reads). We find that among the 800 DNA species that have at least 100 reads, 93.6% are found in both replicates. All the nonoverlapping sequences have very low abundance, close to 100.

Moreover, we compare the population size of each DNA species between the two replicas, after having equalized the database sizes. The results are now cited in p14 lines 509-510, In Appendix 1, Experimental Controls and shown in Figure 2-figure supplement 3, where we plot the ratio of the number of reads in the two replicates for each sequence as a function of the number of reads in one. We found an average of 0.965 with a standard deviation of 0.119. High fluctuations are found in the most rare species, as expected.

We think this evaluation indeed strengthens the solidity of our results.

• I have a small concern about target resource accessibility: is there any spacer between the ssDNA and the bead? The methods section does not mention any, and I would expect such a proximity between the target DNA and the bead to yield steric repulsion that impedes interactions with random DNA individuals.

Yes, there is a 12-carbon spacer between the bead and the resource, which was inserted exactly to make the resource more accessible. This information is now available in Table 1 of Supplementary Information detailing the sequences used in the experiment. However, as now described in the text (p8 lines 284-286), we observe that the interaction with the resource is always shifted to the 3', the terminal furthest from the bead, indicating some residual issue of accessibility to the resource sections closest to the bead.

• Regardless of the existence of a spacer, binding of random DNA molecules to beads instead of the target DNA constitutes a potential source of noise (described for now as '1-x' in the IBEE model), which can be probed by swapping targets, selecting without target etc.

This issue is addressed by the test with bare beads described above, in which we found little effects, corresponding to small 1−𝑥 value.

• Is there any recombination potentially occurring during amplification steps? This could be tested with a set of known molecules amplified over 24 amplification steps in a row (no binding step).

It is possible for recombination to occur during the amplification steps. In Appendix 2, the section "By-Product Formation from PCR Amplification", discusses PCR byproducts as aberrant forms of amplification, such as recombination events. We adopted several strategies to limit by-product formation, such as: i) use of “blockers” characterized by a phosphate group at 3’ end (thus inhibiting their usage during the amplification and allowing a better control of the reaction conditions over the PCR cycles), ii) a high annealing temperature (to limit the possibility of a spurious primer annealing to the random region), iii) fewer PCR cycles, iv) a high primer concentration, v) a very short elongation step (all these strategies have been implemented to avoid a possible mispriming event between different DNAi, and the formation of concatemers). However, the formation of by-products is a problem inherent to the technique: in fact, it is a known issue for classical SELEX technology (Tolle et al. 2014), mainly due to the random region within the DNAi. Q5® Hot Start High-Fidelity DNA Polymerase (New England Biolabs, Ipswich, MA, USA) has an error rate of <0.44 x 10-6/base.

In classic SELEX technology, the average number of selection cycles is 10. This limitation is partly due to the increase in PCR by-products. As we can see from Figure 2 Supplementary Figure 1, the percentage of PCR by-products is less than 20% at cycle 12, and then increases dramatically in the following cycles. We are performing a series of experiments with known and limited sequences to verify and better understand the phenomenon for future applications of the SEDES platform. On this issue we decided not to modify the manuscript since we think it is already well discussed in Appendix 1.

And the third point:

• Perform one cycle (or a few cycles) with random DNA individuals, the most frequent individuals at the end of the current experiment, newly designed individuals with higher binding affinity to the target than currently dominating individuals, newly designed individuals with higher propensity to form hairpins or to form homodimers. Such experimental testing of predictions from the data analysis/modeling, typical of a physics approach, would illustrate the level of understanding one can reach with a simple yet powerful experimental setup.

We perfectly agree that the approach we propose and the set of results we obtained call for further investigations that could strengthen analysis and modeling. The final aim we envisage is the understanding, within this simplified approach, of key evolutionary factors such as fitness. Indeed, becoming able to write an explicit fitness function would be a significant new contribution to the understanding of evolutionary processes, even within the limited settings of the ADSE approach, as discussed in the conclusions of the manuscript.

However, undergoing such an analysis is a long and expensive job, which we have started and will be completed in a not immediate future. For this reason, given the already significant body of results we are presenting here, we prefer to keep this paper confined to the study of the evolution of a random DNAi population and discuss in a future contribution the behavior of smaller designed sets of competing, collaborating or parasitic individuals.

Looking ahead, additional stages of investigations will also include mutations - to investigate the kinetics of speciation, and, in an even further stage, the interplay between evolution kinetics and dynamical mutation of resources.

I have a few smaller points:

• It would be very useful to provide the expected dynamic range of binding free energies (in terms of DeltaG and omega): what is the maximum binding free energy for the perfect complement?

The NUPACK-computed binding free energy of a 20 basis-long oligomer complementary to the resource (𝜔=20) is -24.36 Kcal/mol for Oligo1 and -23.08 Kcal/mol for oligo 2. This is the best answer we can offer to the reviewer’s request, since the maximum binding free energy of DNAi individuals (much longer than the target strand) would include contributions from the unpaired bases. Indeed, the values give above are approached by the left tail of the distribution of Fig. 3a, which however includes DNAi self-energies.<br /> The perfect complement binding free energy is now cited in the text as a reference for the dynamical range of DeltaG (p4 lines 151-152).

• How is the number of captured DNA molecules quantified? Is 10^12 measured, estimated, or hypothesized?

The number of sequences was calculated from data obtained from 260 nm absorbance quantification. We have now added this information in the Methods, Selection Phase” section.

Reviewer #2:

Summary:

In this manuscript, the authors introduced ADSE, a SELEX-based protocol to explore the mechanism of emergency of species. They used DNA hybridization (to the bait pool, "resources") as the driving force for selection and quantitatively investigated the factors that may contribute to the survival during generation evolution (progress of SELEX cycle), revealing that besides individual-resource binding, the inter- and intra-individual interactions were also important features along with mutualism and parasitism.

Strengths:

The design of using pure biochemical affinity assay to study eco-evolution is interesting, providing an important viewpoint to partly explain the molecular mechanism of evolution.

Weaknesses:

Though the evidence of the study is somewhat convincing, some aspects still need to be improved, mostly technical issues.

Major:

1) There are a few technical issues that the authors should clarify in the manuscript to make the analysis more transparent:

1.1) To my understanding, it is difficult to guarantee the even distribution of different species (individuals) in the initial individual pool. Even though the authors have shown in Fig. 2a that the top 10 sequences take up ~ 0% in the pool, it remains unclear how abundant these top and bottom representative sequences are, given the huge number of the pool (10E15). Can the author show the absolute number of these sequences in different quantiles? Please show both Oligo sets.<br /> : First, we thank the reviewer for both positive and critical comments that have guided us in reformulating or clarifying some messages of our work.

As for this specific point: 10E15 is a small number compared to 4^50 = 10E30, the number of possible sequences of length 30. Thus, we don’t expect more than one individual per sequence in the initial pool. However, sequencing requires a preparation amplification, which may lead to detecting a few sequences with more than one individual.

Specifically, in the initial pool of Oligo 1, the most abundant individual (of sequence GAACTAAAGGGGCGGTGTCCACTTGCCTGTAGTGGTTATCAGTCCGGTTG)has 3 copies. The 0.7% of the sequences has 2 copies, while the vast majority of strings (99.3% on a sample of about 1.5 x 10E6 sequenced DNAi) is present in one copy only. A similar situation holds for Oligo 2, with 4 DNAi present in 3 copies and the 0.8% of the sequences (in a pool of 2 x 10E6 DNAi) in 2 copies.

It is worth noticing that none of the 10 most abundant species in the last cycle is present in the sample. Indeed, the fraction of the pool which is sequenced is removed from the population that undergoes evolution (as now specified in p2, line 104). We specified in the text (p2, lines 69-70, p3 lines 94-96) the fact that in the initial pool no sequence is expected to be present in more than one individual.

1.2) The author claimed that they used two different oligo sets (Oligo1 and Oligo2) in this study. It is unclear which data was used in the presentation. How reproducible are they? Similar to this concern, how reproducible if the same oligo set was used to repeat the experiment?

The oligo used in the main text was declared in Methods, Replica section. It is now declared also in the main text (p3 lines 106-108 and in the captions of Figure 2, Figure 3 and Figure 4). Reproducibility is addressed in: Figure 2-figure supplement 5; Figure 2-figure supplement 6; Appendix 2: Results of the experimental replica.

It should also be noted that two starting pools of random 50mers are necessarily disjoint sets for the same reason discussed in the previous answer: the probability of common sequences in two 10E15 selections from a 10E30 is negligibly small. Thus, it is expected that each time a new evolution experiment is started, different dominant sequences are found. However, the statistical properties of the DNAi pool during the evolution process of Oligo1 and Oligo2 are similar as discussed in Appendix 2 of the paper.

1.3) PCR and illumina sequencing itself introduced selection bias. How would the analysis eliminate them? The authors only discussed the errors created during PCR cycles (page 3, lines 115-122). However the PCR itself would prefer to amplify some sequences over the others (e.g. with high GC content). Similarly, the illumina sequencing would be difficult to sequence the low complexity sequences. How would this be circumvented?

Yes, both PCR and Illumina sequencing have some known biases in the amplification process (e.g. sequencing of homopolymers or amplification of GC-rich sequences) that are intrinsic to the used techniques. Regarding PCR, we implemented a thermal protocol optimized for our chosen experimental setup, characterized by very short denaturation, annealing and amplification steps performed at high temperatures. Regarding Illumina sequencing, we can’t rule out a bias against specific sequences (e.g, homopolymers), which however should not be captured during the selection step, due to the design of the resource. Also, the libraries subjected to sequencing are characterized by a low complexity: according to the experimental design, the first and last 25 nucleotides are the same for all DNAi, the only differences being in the central 50 nt-long sequence. It is known that a low complexity library might encounter problems during sequencing due to the design of Illumina instruments: nucleotide diversity, especially in the first sequencing cycles, is critical for cluster filtering, optimal run performance and high-quality data generation. To overcome this limitation, the obtained libraries were run together with more complex and diverse library preparations: the ADSE sequences were about 1-2% of the total reads per run, corresponding to only a few million reads.

This discussion is now in Appendix 1, Intrinsic limitations of the molecular approach.

1.4) Some DNA sequences would bind to the beads instead of the resource sequence coated on them. Should the author run the experiment using bead alone as a control?<br /> : We performed a negative control experiment in which we performed the “selection step” with bear beads, i.e. beads without with no DNA grafted on them. We then compared the results with the corresponding results of the original experiments on Oligo 1 and 2.

After 6 cycles, the most abundant sequence in the negative dataset has a relative occurrence of 0.05%, whereas the dominant strand in Oligo 1 and Oligo 2 has an abundance of 8% and 16%, respectively, i.e. 40-80 times larger.

This indicates that the drift due to non-specific binding (+ PCR amplification) is at least two orders of magnitude smaller than the selection induced by the affinity with the resource.<br /> This part is now discussed in Appendix 1, Experimental controls.

2) It would be interesting to study the impact of environmental factors, for example, changing pH, salt concentration, and detergent. Would these factors accelerate/decelerate the evolution?

We agree that the approach we propose and the set of results we obtained call for further investigations. However, performing these additional experiments, which would require a minimum of 6 generations each, is a long and expensive job, which we have started and will not be completed in the near future. For this reason, given the already significant body of results we are presenting here, we prefer to keep this paper confined to the study of the evolution of a random DNAi population in the selected conditions and leave the exploration of new conditions, potentially opening new evolutionary scenarios, to a future contribution. In fact, our aim was to show that through our platform we can indeed observe fundamental elements of evolution in a non-biological system, which, in the set of chosen parameters, we do.

3) The concentration of individual oligo is apparently one of the most important factors in determining the interactions. In later cycles, some oligos become dominant, namely with extremely higher concentrations compared to their concentration in earlier cycles. This would definitely affect its interaction with resources, or self-interaction, or interaction with other oligos in the pool. However, the authors failed to discuss this factor, which may explain the exponential enrichment in later cycles.

We agree with the reviewer that this is an important point, but we disagree that we have not discussed it. We introduce the topic at the end of the “Null Model and Eco-evolutionary Algorithm”, where we comment on the change of the gamma parameter by saying that there must be a shift in the evolution process, first dominated by the interactions with the resources, and in later stages by some other factors (lines 227230) that we then discuss in “Self and mutual DNAi interactions are evolutionary drivers”. In this latter chapter and in the following, we indeed discussed the effects of mutual and self interactions between DNAi.

Indeed, a key point in our paper is the change in the gamma parameter necessary to match the IBEE model to experiments, as it is now more openly stated (p5 lines 217218 where we also mention figure 2-supplement 8 which clearly shows the necessity of a variable gamma). The two regimes enlightened by the gamma value must reflect a change in the competition for the resources and interactions among species. In the first generations, where the diversity of species is large (there are few strings for each species) and binding to the resources generally very week (small <omega>), the affinity with the resource is the main driving force (fast growth of <omega>), while mutual interactions remain too random to favor any species in particular. In the later cycles instead, when <omega> becomes large enough to provide a significant stability to the resource-binding of the majority of species, the dominating species compete more intensively on the basis of their structure and capacity of self-defense, parasitism and mutualism, a condition in which evolution affects more modifications in sequences than in <omega>.

Certainly, our understanding of this shift is based on statistical behavior and it is inferential, based on the study of specific DNAi described in the last part of the manuscript. For a better molecular model, more experiments with selected DNAi competing, cooperating or being parasitic would be necessary, with the final aim of defining a predictive fitness function. Alas, this requires months of further investigation. :

4) The author observed the different behaviors of medium 𝜔 in early and late cycles, referring to Fig 2h. Using the IBEE model, they found out it is the change of gamma. However, the authors did not further discuss the molecular mechanism. It could be very interesting to understand the evolutionary change of these individuals.

This comment might be related to the previous one. It is true that our discussion and understanding of the whole process is statistical, and misses a molecular model to predict the value of gamma.

However, the specific behavior that the reviewer asks about (those in Fig. 2h) is not related to the change in gamma. Even if gamma remains as in the first part of the evolution (gamma = 3), the species with overlap between 6 and 10 would first grow in number and later decrease. Indeed, during the first cycles they have an advantage with respect to the majority of species with lower maximum overlap, a condition that favors their amplification. However, in the second stage of the evolution dominant species with a larger affinity emerge and outcompete the individuals of this class. We added a sentence in the text to clarify this point (p7 lines 227-229).

5) In Figure 2f, some high w become quite missing. Should the authors give some interpretation? It is not observed in cycle 12 though (panel e).

Such an effect is just due to under-sampling. In a pool of 10^n oligomers, any sequence with a given 𝜔 with P(omega) < 10E-n will have a vanishing probability to appear in that sample.<br /> At cycle 12 the overall number of sequenced strands is larger than at cycle 24, due to the growing presence of PCR by-products. Thus, the right tail of the cyan distribution at the last cycle is sampled with less accuracy than at cycle 12. We have added a sentence in the revised manuscript (p5 lines 177-178) to clarify this point.

6) It would be interesting to further explore if another type of selection resource is used, for example protein that binds to particular sequences, i.e. transcription factors. Previous studies have used a large amount of sequence-specific transcription factors to run SELELX. Since the data have existed there, why not explore?

This is an interesting suggestion: can we use data from “ordinary” SELEX favoring specific sequences to explore sequence evolution? Two limitations make us a bit skeptical on this path: first, the consensus sequences of DNA-binding proteins are rather short and typically target dsDNA rather than ssDNA; second, the free energy of interaction is known only for the consensus sequence but not for sequences with all possible mutations with respect to the consensus sequence, making very hard to develop any molecular understanding of the process.

Minor:

1) There is no figure legend or in-text citation of Figure 2b.

2) Please correct "⁃C" with "{degree sign}C" in lines 470, 471, 472, 477 et al.

3) Typos and grammar issues should be corrected. Examples are shown below (but not limited to these only):

• mixed use of past and present tense.

• Line 152, "basis" should be "bases".

• Line 277, "a impediment" should be "an impediment"

• Line 278, "a major deadly threats" should be "major deadly threats"<br /> :<br /> We are sorry for the mistakes, and we have corrected them. Many thanks to the reviewer!

Author Response

We appreciate your consideration of our manuscript entitled “Deciphering molecular heterogeneity and dynamics of neural stem cells in human hippocampal development, aging, and injury” (eLife-RP-RA-2023-89507). We thank all the reviewers for their valuable and thoughtful comments and suggestions. We have carefully considered all the comments and revised our manuscript (eLife-VOR-RA2023-89507) accordingly. You can find our point-by-point responses here. In the revised manuscript, we have addressed most of the issues and concerns raised by the reviewers. We hope that the changes will better illustrate the quality of our sn-RNA data and the criteria of the cell type identification. However, due to the scarcity of stroke and neonatal human brain samples, we cannot strengthen our findings and conclusions by increasing this type of hippocampal tissue for analysis within the expected timeframe. With these improvements and limitations, we would like to ask whether we could get a better judgment from the reviewers.

Reviewer #1 (Public Review):

In this manuscript, Yao et al. explored the transcriptomic characteristics of neural stem cells (NSCs) in the human hippocampus and their changes under different conditions using single-nucleus RNA sequencing (snRNA-seq). They generated single-nucleus transcriptomic profiles of human hippocampal cells from neonatal, adult, and aging individuals, as well as from stroke patients. They focused on the cell groups related to neurogenesis, such as neural stem cells and their progeny. They revealed genes enriched in different NSC states and performed trajectory analysis to trace the transitions among NSC states and towards astroglia and neuronal lineages in silico. They also examined how NSCs are affected by aging and injury using their datasets and found differences in NSC numbers and gene expression patterns across age groups and injury conditions. One major issue of the manuscript is questionable cell type identification. For example, in Figure 2C, more than 50% of the cells in the astroglia lineage clusters are NSCs, which is extremely high and inconsistent with classic histology studies.

We appreciate the concerns raised by Reviewer 1 regarding the cell type identification. We suggest that the identification of the 16 main cell types in our study is accurate, as supported by the differential gene expression and the similarity of transcriptional profiles across species (Figure 1B to D, Figure Supplement 1C to E, and Figure 2A and B).

While we appreciate the reviewer for bringing up the concern regarding the high proportion of NSCs within the astroglia lineage clusters, it is worth mentioning that distinguishing hippocampal qNSCs from astrocytes by transcription profiling poses a significant challenge in the field due to their high transcriptional similarity. From previous global UMAP analysis, AS1 (adult specific) can be separated from qNSCs, but AS2 (NSC-like astrocytes) cannot. Therefore, the data presented in Figure 2C to G aimed to further distinguish the qNSCs from AS2 by using gene set scores analysis. Based on different scores, we categorized qNSC/AS lineages into qNSC1, qNSC2 and AS2. Figure 2C presented the UMAP plot of qNSC/AS2 population from only neonatal sample. We apologize for not clarifying this in the figure legend. We have now clarified this information in the figure legend of Figure 2C. More importantly, we have added UMAP plots and quantifications for other groups in Figure2Supplement 2A and B, including adult, aging, and injure samples. This supplementary figure provides more complete information of the cell type composition and dynamic variations during aging and injury. Although the ratio of NSCs in the astroglia lineage clusters remains higher compared to classic histology studies, the trends indicate a reduction in qNSCs and an increase in astrocytes during aging and injury, which supports that cell type identification by using gene set score analysis is effective, although still not optimal. Combined methods to accurately distinguish between qNSCs and astrocytes are required in the future, and we also discuss this in the corresponding texts.

Major comments:

In Figure 1E, the authors should provide supporting quality control of their snRNAseq dataset in the corresponding supplementary figures. Specifically, they should show that the average number of genes and transcripts detected in each cluster are similar across different conditions. This would rule out the possibility that the stem cell gene enrichment is an artifact of increased global gene expression.

Thanks for the suggestion. We have provided the supporting quality control of our snRNA-seq dataset in Figure1-Supplement 1A, B and F. The detailed data presented in Figure 1-Supplement 1A and Figure 1-source data 1 show that more than 2000 genes per cell were detected in all donor samples and mitochondrial genes accounted for less than 5%, suggesting that most cells were viable before freezing and underwent minimal RNA degradation. The hippocampi were dissected and collected from donors with a short post-mortem interval of about 3-4 hours to ensure low levels of RNA degradation and cellular apoptosis rates in the collected samples. For subsequent transcriptome analysis, we removed cells with fewer than 200 genes or more than 8600 genes (potentially indicating cell debris and doublets) and those with more than 20% of transcripts generated from mitochondrial genes, as shown in Figure 1-Supplement 1A and B. Figure 1-Supplement 1F provides evidence supporting that the average number of genes detected in each neurogenic cell type (AS2/qNSC, pNSC, aNSC, NB and GC) is similar across different conditions. This suggests that the enrichment of stem cell genes is not simply an artifact of increased global gene expression.

In Figure 2A, the authors performed a cross-species comparative analysis of neurogenic cell clusters by integrating their datasets with published datasets from mice, pigs, and macaques. They assigned cell types to the clusters based on their similarity to the same cell group across species. However, they did not address why a previous study by Franjic et al. (Neuron 2022) using the same method and analysis did not detect any neurogenic clusters in human hippocampal and entorhinal cells. This discrepancy could have implications for the validity of their approach and the interpretation of their results. The authors should provide possible explanations for the different outcomes.

We appreciate the valuable feedback provided by the reviewer. In our dataset, we sequenced 24,671 GC nuclei and 92,966 total DG cell nuclei, which also includes neonatal samples. The number of nuclei we sequenced is 4.5 times higher than that of Wang et al. (Cell Research, 2022), who also detected NBs. Thus, it is reasonable to conclude that we were able to detect NBs. Moreover, the presence of these rare cell types has been demonstrated in our study through immunostaining techniques, which provides further evidence. In addition, we downloaded the snRNAseq data from Franjic et al. (Neuron 2022) and mapped the dataset onto our snRNAseq dataset using the “multimodal reference mapping” method. Based on the mapping analysis, astrocytes, qNSCs, and aNSCs were identified in Franjic’s data with varying correlation efficiencies, but neuroblasts or immature neurons could not be detected (Figure 6-figure supplement 11 A to G). Therefore, we speculated that the discrepancies between our study and Franjic’s might be caused by health state differences across hippocampi, which subsequently lead to different degrees of hippocampal neurogenesis and immature neuron maintenance.

In Figure 2C-2J, the authors examined the astroglia lineage clusters to identify NSC subpopulations and their gene features. However, they did not use consistent cell types for the analysis. Some comparisons involved quiescent NSCs (qNSCs) and differentiated astrocytes, while others involved primed NSCs (pNSCs), and active NSCs (aNSCs). This could introduce bias and affect the results. The authors should consistently include all astroglia cell clusters in their analysis, such as q, p, a NSCs and astrocytes.

We understand the concerns raised by the reviewer, and we use different cell types as the starting points for the developmental trajectory for specific reasons. pNSCs represent an intermediate state between quiescence and activation. During embryonic development, pNSCs demonstrate the greatest similarity to RGLs. Subsequently, pNSCs progressively exit the cell cycle and transition into qNSCs during the postnatal stage. These qNSCs have the ability to re-enter the cell cycle upon activation by stimuli. Based on this knowledge, we have set the pNSC population as the root of the developmental trajectory in the neonatal sample, which aligns more closely with the actual developmental process. However, setting qNSCs as the root of the NSC developmental trajectory in the adult injury sample is more fit to the process of adult neurogenesis.

In addition, the authors’ identification of qNSCs, pNSCs and aNSCs is very questionable in Figure 2. For instance, qNSC2 cells in Figure 2G express MBP, PLP1, and MOBP, which are markers of mature oligodendrocytes. They receive low scores in RGL gene module scoring in Figure 2E, even lower than those of astrocytes. These cells are likely misclassified mature oligodendrocytes. In Figure 2H-I, the authors did not present the DEGs in pNSCs and aNSCs, the GO terms of these clusters are very similar. To confirm their results, the authors should either use histology or cite literature that supports the differentiation of pNSCs and aNSCs by these genes.

We appreciate the reviewer’s observation regarding the high expression of oligodendrocyte (OL) genes in the qNSC2 population, and we acknowledge that we currently do not have a clear explanation for this finding. However, despite the expression of OL genes in qNSC2, when we conducted a transcriptional similarity analysis comparing qNSC2 to other cell populations, we still observed a higher similarity between qNSC2 and qNSC1, as well as between qNSC2 and astrocytes, rather than oligodendrocytes. Therefore, qNSC2 are not misclassified mature oligodendrocytes (Figure 2-figure supplement 2C).

Regarding pNSCs and aNSCs, both cell types share similar molecular characteristics, with a key distinction in their proliferation abilities. Notably, aNSCs primarily reside in the S/G2/M phase and highly express the cell cycle-related gene CCND2, reflecting active mitosis. Since its capacity to differentiate into neuroblast/immature granule cells, aNSCs also express a small subset of genes associated with neuronal differentiation, including STMN2, SOX11, and SOX4 (Figure 1C, D, and Figure 2J). As per the reviewer’s request, we have presented the DEGs in pNSCs and aNSCs (Figure 2-figure supplement 2D, Figure 2-source data 2). The results of GO analysis reveal that pNSC is more associated with the Wnt signaling pathway, axonogenesis, and Hippo signaling, while aNSC is more associated with G2/M transition of mitotic cell cycle, neuron projection development, axon development, and dendritic spine organization (Figure2-figure supplement 2E, Figure 2-source data 2).

As Figure 2C illustrates, the authors isolated qNSCs and differentiated astrocytes from the astroglia lineage clusters to identify DEGs. However, more than 50% of the cells in the astroglia lineage clusters are NSCs, which is extremely high and inconsistent with classic histology studies. This could be due to cluster misclassification or over-representation of neonatal NSCs in the NSC cluster. The authors should stratify their data by age groups and provide corresponding UMAP plots and quantification. They should also compare DEGs between NSCs and astrocytes within each age group in all of the analyses, as neonatal, adult, and aging NSCs may have different properties and outputs.

While we appreciate the reviewer for bringing up the concern regarding the high proportion of NSCs within the astroglia lineage clusters, it is worth mentioning that distinguishing hippocampal qNSCs from astrocytes by transcription profiling poses a significant challenge in the field due to their high transcriptional similarity. From previous global UMAP analysis, AS1 (adult specific) can be separated from qNSCs, but AS2 (NSC-like astrocytes) cannot. Therefore, the data presented in Figure 2C to G aimed to further distinguish the qNSCs from AS2 by using gene set scores analysis. Based on different scores, we categorized qNSC/AS lineages into qNSC1, qNSC2 and AS2. Figure 2C presented the UMAP plot of qNSC/AS2 population from only neonatal sample. We apologize for not clarifying this in the figure legend. We have now clarified this information in the figure legend of Figure 2C. More importantly, we have added UMAP plots and quantifications for other groups in Figure2-Supplement 2A and B, including adult, aging, and injure samples. This supplementary figure provides more complete information of the cell type composition and dynamic variations during aging and injury. Although the ratio of NSCs in the astroglia lineage clusters remains higher compared to classic histology studies, the trends indicate a reduction in qNSCs and an increase in astrocytes during aging and injury, which supports that cell type identification by using gene set score analysis is effective, although still not optimal. Combined methods to accurately distinguish between qNSCs and astrocytes are required in the future, and we also discuss this in the corresponding texts. (The same question has been answered in the first part of this letter.)

In Figure 3, the authors discuss the important issues of shared gene expression between interneurons and NB/im-GCs. In the published work (Zhou et al. Nature 2022; Wang et al. Cell Research 2022), however, NBs and im-GCs are not located in the interneuron cluster. This needs to be stated to avoid confusion. Specifically, this suggests the limitation of using a few preselected markers for cell type identification. The author should also examine whether these shared markers are indeed expressed in human interneurons by immunostaining as one application of these markers will be in histology for the field.

Thanks for the reviewer’s comments. We agree that single nucleus transcriptome analysis is capable of effectively distinguishing between immature neurons and interneurons. In our UMAP plot, the NBs and im-GCs are not located in the interneuron cluster, either. When we compared the granule cell lineage which contains NB/immature GC and the interneuron population at the whole transcriptome level between our dataset and published mouse (Hochgerner et al. 2018), macaque and human (Franjic et al. 2022) transcriptome datasets, we found high transcriptomic congruence across different datasets (Figure 3-figure supplement 3A). Specifically, our identified human GABA-INs very highly resembled the well-annotated interneurons in different species (similarity scores > 0.95) (Figure 3-figure supplement 3A). The point we want to convey here is that many markers previously used to identify immature neurons are also expressed in interneurons. Therefore, when using these markers for staining and identification purposes, there is a possibility of mistaking an interneuron for an immature neuron. Hence, when selecting markers, we need to be aware of this and exclude genes that are highly expressed in interneurons as markers for immature neurons. To support our view, we conducted co-immunostainings of DCX (a traditional neuroblast marker) and SST (a typical interneuron marker). Our results demonstrate that SST-positive interneurons are indeed capable of being stained by the traditional neuroblast marker DCX in primates. Please see Figure 3-figure supplement 4A-C.

In Figure 4, the authors' classification of cell subpopulations in the neuronal lineage is not convincing. They claim to have identified two subpopulations of granule cells (GCs) that derive from neuroblasts in Figure 4A-4D. However, this is inconsistent with previous single-cell transcriptomic studies of human hippocampus, which only identified one GC cluster. The differentially expressed genes (DEGs) that they used to distinguish the two GC subpopulations are not supported by prior research. This could be a result of over-classification or technical bias. CALB1 marks mature neurons whereas CALB2 marks immature neurons. However, in Figure 4F, it suggests that CALB1 is expressed in cells that have similar pseudotime scores as CALB2, both of which reside in an intermediate position during the differentiation trajectory. This does not match the known expression patterns of these markers in GCs. The authors should explain this discrepancy and provide additional evidence to support their claims. In addition, for Figure 4F, the authors should address how the different cell fate groups correspond to cell clusters.

We appreciate the concerns raised by the reviewer. Unfortunately, despite trying various strategies to confirm the identity of the two subpopulations of granule cells (GCs) derived from neuroblasts, we were unable to find a clear answer. As a result, we can only provide an objective description of the differences in gene expression and developmental trajectory and speculate that these differences may be related to their degree of maturity but are not aligned on the same trajectory.

Regarding the expression of CALB1 and CALB2, the original Figure 4F did not provide precise positional information for these genes due to the compression of a large amount of gene information. In order to address this, we conducted a separate trajectory analysis specifically for CALB1 and CALB2 (Figure4-figure supplement 6B). The results of this analysis are in line with previous literature reports: CALB2 was found to be enriched in immature neurons, while CALB1 exhibited a delayed expression pattern and was enriched in mature neurons.

The authors compared NSCs in different age groups in Figure 5, but their analysis in Figure S5A-D only included neonatal and aging stages, omitting adult stages. They should perform cross-age analyses with all three stages for consistency.

Thank you for the reviewer's comments. We have now included the differentially expressed genes (DEGs) of the neurogenic lineage in the adult stage. Please see Figure5-supplyment 8.

In Figure 6E, the authors should separate the data by age and calculate the proportion of the re-clustered cell groups, as they did in Figure 6B. In the re-clustered groups, how do the aNSCs and reactive astrocytes change with age?

Thanks for the reviewer's comments. We have removed the previous Figure 6B and recalculated the proportions of the re-clustered cell groups, including reactive astrocytes (AS). The changes in the proportions of qNSC1, qNSC2, pNSC, aNSCs, and reactive astrocytes with age are now shown in Figure 6E of the updated version. We observed that the proportion of aNSCs decreases with age but increases after injury. Reactive astrocytes primarily appear in the injury group, while their proportion is very low in the other groups.

In Figure 6E-H, the authors assert that the aNSC group in stroke injury can produce oligodendrocytes in vivo based on trajectory analysis, which is a bold claim and lacks literature support. Their evidence is insufficient, as it relies on a single in vitro study.

Thanks for the reviewer's comments. We have provided more references to support our claim (e.g., El Waly, Cayre, and Durbec 2018; Parras et al. 2004; Enric Llorens-Bobadilla et al. 2015b; Koutsoudaki et al. 2016). These studies have indicated that under injury conditions, neural stem cells have potentials to differentiate into oligodendrocytes.

In Figure S8 and the Discussion section, they compared their dataset with Zhou et al. (Nature 2022), a published snRNA-seq dataset of the human hippocampus across the lifespan. The authors speculated that the new neurons identified in the EdU in vitro culture analysis in Zhou et al. might be related to epilepsy, but they did not provide any evidence for this claim. To partially validate their speculation, the authors should conduct the same integrative analysis with Ayhan et al. (Neuron 2021), which examined snRNA-seq data from epileptic patient hippocampi, to demonstrate that they could detect the injury-induced aNSC population and injury-associated genes. Furthermore, they should also conduct the same integrative analysis with the other two published human hippocampal datasets, namely Franjic et al. (Neuron 2022) and Wang et al. (Cell Research 2022).

Thanks for the reviewer's comments. As the reviewer’s request, we down loaded the snRNA-seq data from Zhou et al. (Nature 2022), Wang et al (Cell Research, 2022a), Franjic et al. (Neuron 2022) and Ayhan et al. (Neuron 2021) for integrative analysis. Except for the dataset from Zhou et al. (Nature 2022), which utilized machine learning and made it difficult to extract cell type information for fitting with our own data, the datasets from the other three laboratories were successfully mapped onto our dataset. Different levels of correlation were observed, confirming the presence of astrocytes, qNSCs, aNSCs, and NBs (Figure 6-figure supplement 11 E to G).

There are a few minor concerns that the authors could improve upon. In Fig. 5D, HOPX immunostaining pattern doesn't not look like NSCs. In Figure 5B and 6B, the same data were presented twice. And proper statistical tests are missing in Figure 6B.

Thanks for the reviewer's comments. We have added the arrowheads to indicate the typical immunostaining of HOPX immunostaining, which clearly shows its nuclear localization. This observation is consistent with previous reports on the subcellular distribution of HOPX protein. In the updated version, Figure 5B and 6D are distinct and not repetitive. The inclusion of the proportions of reactive astrocytes in Figure 6D provides valuable information about their distribution within the different groups. Unfortunately, statistical tests cannot be conducted for the neonatal and injury samples since only one sample is available in each case.

# Reviewer 2

Major points:

1) The number of sequenced nuclei is lower than the calculated numbers of nuclei required for detecting rare cell types according to a recent meta-analysis of five similar datasets (Tosoni et al., Neuron, 2023). However, Yao et al report succeeding in detecting rare populations, including several types of neural stem cells in different proliferation states, which have been demonstrated to be extremely scarce by previous studies. It would be very interesting to read how the authors interpret these differences.

We appreciate the valuable comments from the reviewer. We understand the reviewer’s concern and have also noticed that according to the computational modeling conducted by Tosoni et al. (Neuron, 2023), at least 21 neuroblast cells (NBs) can be identified out of 30,000 granule cells (GCs) from a total of 180,000 dentate gyrus (DG) cells. In our dataset, we sequenced 24,671 GC nuclei and 92,966 total DG cell nuclei, which also includes neonatal samples. The number of nuclei we sequenced is 4.5 times higher than that of Wang et al. (Cell Research, 2022), who also detected NBs. Therefore, it is reasonable to conclude that we were able to detect NBs. Moreover, the presence of these rare cell types has been demonstrated in our study through immunostaining techniques, which provides further evidence. we have implemented strict quality control measures to support the reliability of our sequencing data. These measures include: 1. Immediate collection of tissue samples after postmortem (3-4 hrs) to ensure the quality of isolated nuclei. 2. Only nuclei expressing more than 200 genes but fewer than 5000-8600 genes (depending on the peak of enrichment genes) were considered. On average, each cell detected around 3000 genes. 3. The average proportion of mitochondrial genes in each sample was approximately 1.8%, with no sample exceeding 5%. The related supplementary information has been included in Figure 1-supplement 1A, B and F, and Figure 1source data 1.

2) The information regarding the donors including in this study is very scarce. Factors such as chronic conditions, medication, lifestyle parameters, inflammatory levels should be provided.

Thanks for the reviewer's comments. We have incorporated additional details about the donors. However, we would like to clarify that information regarding lifestyle parameters has not been collected. Please refer to Figure 1-source data 1 for the updated information.

3) The number of donors included per group is insufficient: neonatal group n=1; adult group n=2; stroke n=1. Although the scarcity and value of each human brain sample is a factor to be considered, the authors must explain why and how the results obtained from individuals can be extrapolated to the population at these low numbers, especially considering that the rate of adult hippocampal neurogenesis is assumed to be very variable across individuals (Tosoni et al., Neuron, 2023).

Thanks for the reviewer's comments. We acknowledge these limitations and understand that the inclusion of a larger number of donors would strengthen the statistical power and generalizability of our findings. However, due to the scarcity of stroke or neonatal human samples, it was not feasible to collect a larger sample size within the expected timeframe. To explain why and how we could identify the rare neurogenic populations, we have shown that the number of cells captured from individual samples and the average number of genes detected per cell are sufficient, indicating overall good sequencing quality (Figure 1-supplement 1A and B, and Figure 1-source data 1). Additionally, we have further confirmed the presence of these cell types with low abundance by integrating immunofluorescence staining (Figure 4E and Figure 6F), cell type-specific gene expression (Figure1 C and D), overall transcriptomic characteristics (Figure 1-supplement 1E), and developmental potential (Figure4 A-D, Figure 6A-D).

4) The definition of primed NSCs (pNSCs) is poor and questionable. "Primed" may be interpreted as a loaded term and the authors only make an effort to follow them into their neurogenic trajectory while figure 4A suggest that they also, if not preferentially judging on the directionality of the RNA velocity vectors, generate astrocytes and quiescent NSCs.

Thanks for the reviewer's comments. We apologize for not clearly explaining the definition of pNSC in our study. We have now included an explanation in the text and added supplementary information to highlight the features of pNSC and aNSC (Figure 2H to J, Figure2-figure supplement 2D and E). The results of GO analysis reveal that pNSC is more associated with the Wnt signaling pathway, axonogenesis, and Hippo signaling, while aNSC is more associated with G2/M transition of mitotic cell cycle, neuron projection development, axon development, and dendritic spine organization (Figure2-figure supplement 2E, Figure 2-source data 2). The pNSCs referred to in this study represent an intermediate state between quiescence and activation. During embryonic development, pNSCs exhibit the greatest similarity to RGLs. Subsequently, pNSCs gradually exit the cell cycle and transition into qNSCs during the postnatal development (Figure 2J). Thus, in Figure 4A, for the neonatal sample analysis, some pNSCs are shown to enter the neurogenic trajectory, while others exit the cell cycle and transition into qNSCs or become astrocytes (AS2) during postnatal development, indicating a bidirectional trajectory.

5) The experimental definition of quiescent NSCs (qNSC1) is poor and questionable. The qNSC1 cluster is defined by the expression of HOXP (page 6), which the authors indicate is a"quiescence NSC gene". However, at least in mice, HOXP collages with BrdU in proliferative NSCs (Deqiang Li et al, Stem Cell Res. 2015).

Thank you for providing the information about the study conducted by Deqiang Li et al (Stem Cell Res. 2015). We have carefully reviewed their findings. They propose that Hopx is specifically expressed in RGL cells, which are predominantly in a quiescent state. Additionally, they observed that Hopx-positive cells are long-term BrdU-label retaining cells, and Hopx-null NSCs show enhanced neurogenesis, as evidenced by an increased number of BrdU-positive cells. These results suggest that high expression of Hopx in NSCs indicates their quiescence. Furthermore, other studies have provided further support for using high expression of the HOPX gene as a marker to identify quiescent NSCs (Jaehoon Shin et al., Cell Stem Cell 2015; Daniel A. Berg et al., Cell 2019)

6) The term quiescent is never defined in the text, and the reader is forced to assume that they refer to the absence of active proliferation genes, most commonly MKI67. Is that what the authors intended? this should be clarified.

Thanks for the reviewer's comments. We apologize for not clearly explaining the definition of qNSC in our study. We have now included an explanation in the text. qNSCs exhibit reversible cell cycle arrest and display a low rate of metabolic activity. However, they still possess a latent capacity to generate neurons and glia when they receive activation signals. They express genes such as GFAP, ALDH1L1, ID4, and HOPX (Figure 2B). The absence or low expression of active proliferation genes is one feature of qNSCs. The main difference lies in the state of the cell cycle and metabolism.

7) They find cell clusters that express the proliferation marker MKI67. however, previous studies have indicated the difficulty of snRNA-seq techniques to detect proliferation marker transcripts, specially MKI67 even in hippocampal samples from human infants (for example see the snRNAseq studies from Wang and from Zhou cited by the authors and previously mentioned meta-analysis).

Thanks for the reviewer's comments. We could detect MKI67 in our snRNA-seq data, albeit with a very low number of cells (not clustered) expressing it. Here, we are providing the feature plot in Author response image 1 to illustrate the expression of MKI67. In our Figure 5C, we compared the expression level of MKI67 in neurogenic lineage among neonatal, adult and aged groups, and observed its high expression in neonatal rather than adult and aged groups. But the fraction of cells expressed MIK67 is still very low. We apologize for the confusion. We did not claim that we identified specific cell clusters expressing MKI67 in our study.

Author response image 1.

8) The authors observe declining numbers of proliferating cells with aging and interpret this as evidence of declining neurogenesis. However, they also observe sustained neuroblast numbers in the aged brains they analyzed. Wouldn't these neuroblast support neurogenesis? This is unclear and should be discussed.

Thanks for the reviewer's question. We will revise the inaccurate description to clarify that the number of proliferating NPCs, rather than immature neurons, is dramatically reduced with aging. This is because, compared to rodents, immature neurons in primates are indeed retained for a longer period and possess the potential to further develop into mature neurons (Kohler, S.J., et al., PNAS, 2011). We have discussed this in the corresponding texts (Figure 5).

9) The authors indicate that they find DCX transcript expression in interneurons. This is a potentially interesting observation. However, the authors should be very clear to state that in most studies that use DCX as a marker of immature granule cells, DCX's expression is detected by immunohistochemistry. Therefore, the fact that DCX transcripts may be present in other immature neurons does not necessarily disqualify its use as a protein maker of immature granule cells. This clarification will help to prevent misinterpretations of the data presented by the authors.

Thanks for the reviewer's suggestion. We have clarified that we observed DCX transcripts present in interneurons in addition to immature neurons by snRNAseq. In this revised version, we conducted co-immunostainings of DCX (a traditional neuroblast marker) and SST (a typical interneuron marker). Our results demonstrate that SST-positive interneurons are indeed capable of being stained by the traditional neuroblast marker DCX in primates. Please see Figure 3-figure supplement 4A-C. The similar result has also been reported by Franjic et al. (Neuron 2022).

Author Response

Reviewer #1 (Public Review):

The goal of the current study was to evaluate the effect of neuronal activity on blood-brain barrier permeability in the healthy brain, and to determine whether changes in BBB dynamics play a role in cortical plasticity. The authors used a variety of well-validated approaches to first demonstrate that limb stimulation increases BBB permeability. Using in vivo-electrophysiology and pharmacological approaches, the authors demonstrate that albumin is sufficient to induce cortical potentiation and that BBB transporters are necessary for stimulus-induced potentiation. The authors include a transcriptional analysis and differential expression of genes associated with plasticity, TGF-beta signaling, and extracellular matrix were observed following stimulation. Overall, the results obtained in rodents are compelling and support the authors' conclusions that neuronal activity modulates the BBB in the healthy brain and that mechanisms downstream of BBB permeability changes play a role in stimulus-evoked plasticity. These findings were further supported with fMRI and BBB permeability measurements performed in healthy human subjects performing a simple sensorimotor task. While there are many strengths in this study, there is literature to suggest that there are sex differences in BBB dysfunction in pathophysiological conditions. The authors only used males in this study and do not discuss whether they would also expect to sex differences in stimulation-evoked BBB changes in the healthy brain. Another minor limitation is the authors did not address the potential impact of anesthesia which can impact neurovascular coupling in rodent studies. The authors could have also better integrated the RNAseq findings into mechanistic experiments, including testing whether the upregulation of OAT3 plays a role in cortical plasticity observed following stimulation. Overall, this study provides novel insights into how neurovascular coupling, BBB permeability, and plasticity interact in the healthy brain.

While there are many strengths in this study, there is literature to suggest that there are sex differences in BBB dysfunction in pathophysiological conditions. The authors only used males in this study and do not discuss whether they would also expect to sex differences in stimulation-evoked BBB changes in the healthy brain.

We agree with the reviewer regarding the importance of examining sex differences on stimulation-evoked BBB changes. To address this issue we have: (1) clarified in the methods section that the human study involved both males and females; (2) added a section to the discussion highlighting the male bias as a key limitation of our animal experiments; and (3) stated that future work should examine whether stimulation-evoked BBB changes differ between makes and females.

Another minor limitation is the authors did not address the potential impact of anesthesia which can impact neurovascular coupling in rodent studies.

We are grateful for this comment and agree with the reviewer that the potential effects of anesthesia should be discussed. We have added the following discussion paragraph:

“A key limitation of our animal experiments is the fact they were performed under anesthesia, due to the complex nature of the experimental setup (i.e., simultaneous cortical imaging and electrophysiological recordings). Anesthetic agents can affect various receptors within the NVU, potentially altering neuronal activity, SEPs, CBF, and vascular responses (Aksenov et al., 2015; Lindauer et al., 1993; Masamoto & Kanno, 2012). To minimize these effects, we used ketamine-xylazine anesthesia, which unlike other anesthetics, was shown to generate robust BOLD and SEP responses to neuronal activation (Franceschini et al., 2010; Shim et al., 2018).”

Reviewer #2 (Public Review):

Summary:

This study builds upon previous work that demonstrated that brain injury results in leakage of albumin across the bloodbrain barrier, resulting in activation of TGF-beta in astrocytes. Consequently, this leads to decreased glutamate uptake, reduced buffering of extracellular potassium, and hyperexcitability. This study asks whether such a process can play a physiological role in cortical plasticity. They first show that stimulation of a forelimb for 30 minutes in a rat results in leakage of the blood-brain barrier and extravasation of albumin on the contralateral but not ipsilateral cortex. The authors propose that the leakage is dependent upon neuronal excitability and is associated with an enhancement of excitatory transmission. Inhibiting the transport of albumin or the activation of TGF-beta prevents the enhancement of excitatory transmission. In addition, gene expression associated with TGF-beta activation, synaptic plasticity, and extracellular matrix are enhanced on the "stimulated" hemisphere. That this may translate to humans is demonstrated by a breakdown in the blood-brain barrier following activation of brain areas through a motor task.

Strengths:

This study is novel and the results are potentially important as they demonstrate an unexpected breakdown of the blood-brain barrier with physiological activity and this may serve a physiological purpose, affecting synaptic plasticity.

The strengths of the study are:

1) The use of an in vivo model with multiple methods to investigate the blood-brain barrier response to a forelimb stimulation.

2) The determination of a potential functional role for the observed leakage of the blood-brain barrier from both a genetic and electrophysiological viewpoint.

3) The demonstration that inhibiting different points in the putative pathway from activation of the cortex to transport of albumin and activation of the TGF-beta pathway, the effect on synaptic enhancement could be prevented.

4) Preliminary experiments demonstrating a similar observation of activity-dependent breakdown of the blood-brain barrier in humans.

Weaknesses:

There are both conceptual and experimental weaknesses.

1) The stimulation is in an animal anesthetized with ketamine, which can affect critical receptors (ie NMDA receptors) in synaptic plasticity.

We agree that the potential effects of anesthesia should be considered. The Discussion was revised to address this point: “A key limitation of our animal experiments is the fact they were performed under anesthesia, due to the complex nature of the experimental setup (i.e., simultaneous cortical imaging and electrophysiological recordings). Anesthetic agents can affect various receptors within the NVU, potentially altering neuronal activity, SEPs, CBF, and vascular responses (Aksenov et al., 2015; Lindauer et al., 1993; Masamoto & Kanno, 2012). To minimize these effects, we used ketamine-xylazine anesthesia, which unlike other anesthetics, was shown to generate robust BOLD and SEP responses to neuronal activation (Franceschini et al., 2010; Shim et al., 2018)”

2) The stimulation protocol is prolonged and it would be helpful to know if briefer stimulations have the same effect or if longer stimulations have a greater effect ie does the leakage give a "readout" of the stimulation intensity/length.

Thank you for this important comment. We are also very curious about the potential relationship between stimulation magnitude/duration and subsequent leakage and have added the following statement to the discussion:

“Future studies should also explore the effects of stimulation magnitude/duration on BBB modulation, as well as the stimulation threshold between physiological and pathological increase in BBB permeability.”

Our current findings indicate that a one-minute stimulation does not affect vascular permeability or SEP and we aim to test additional stimulation paradigms in future studies.

3) For some of the experiments (see below), the numbers of animals are low and the statistical tests used may not be the most appropriate, making the results less clear cut.

We appreciate this comment and have revised the statistical analysis of Figure 1J,K. We now use a nested t-test to test for differences between rats (as opposed to sections). The differences remain significant (EB, p=0.0296; Alexa, p=0.0229). The text was modified accordingly.

4) The experimental paradigms are not entirely clear, especially the length of time of drug application and the authors seem to try to detect enhancement of a blocked SEP.

Thank you for pointing this out. Figures 2&3 were revised for clarification and a ‘Drug Application’ subsection was added to the methods section.

5) It is not clear how long the enhancement lasts. There is a remark that it lasts longer than 5 hours but there is no presentation of data to support this.

Thank you for this comment. As the length of experiments differed between animals, the exact length could not be specifically stated. To clarify this point, we revised the text to indicate that LTP was recorded until the end of each experiment (between 1.5-5 hours, depending on the condition the animal was in). We also added a panel to figure 2 (Figure 2d) with exemplary data showing potentiation 60, 90, and 120 min post stimulation.

6) The spatial and temporal specificity of this effect is unclear (other than hemispheric in rats) and even less clear in humans.

Our animal experiments (using both in vivo imaging and histological analysis) showed no evidence of BBB modulation outside the cortical somatosensory area corresponding to the limbs. We looked at the entirety of the coronal section of the brain and found enhancement solely in the somatosensory area corresponding to limb. The right side of panels h and i in Figure 1 show an x20 magnification of the section, focusing on the enhanced area. The whole section was not shown, as no fluorescence was found outside the magnified area. Moreover, our quantification showed that the enhancement was specific to the contralateral and not ipsilateral somatosensory cortex (Figure 1 j-k).

We agree that temporal specificity needs to be further explored, and we have now stated that in the discussion: “Future studies are needed to explore the BBB modulating effects of additional stimulation protocols – with varying durations, frequencies, and magnitudes. Such studies may also elucidate the temporal and ultrastructural characteristics that may differentiate between physiological and pathological BBB modulation.”

We also agree that larger studies are needed to better understand the specificity of the observed effect in humans, and to account for potential inter-human variability in vascular integrity and brain function due to different schedules, diets, exercise habits, etc.

8) The experimenters rightly use separate controls for most of the experiments but this is not always the case, also raising the possibility that the application of drugs was not done randomly or interleaved, but possibly performed in blocks of animals, which can also affect results.

Thank you for pointing out this lack of clarity. We have now highlighted that drug application was done randomly.

9) Methyl-beta-cyclodextrin clears cholesterol so the effect on albumin transport is not specific, it could be mediating its effect through some other pathway.

We agree that the effect of mβCD may not be specific. To mitigate this issue, we used a very low mβCD concentration (10uM). Notably, this is markedly lower than the concentrations reported by Koudinov et al, showing that cholesterol depletion is observed at 5mM mβCD and not at 2.5mM/5mM (Koudinov & Koudinova, 2001). This point was added to the discussion.

10) Since the breakdown of the blood-brain barrier can be inhibited by a TGF-beta inhibitor, then this implies that TGFbeta is necessary for the breakdown of the blood-brain barrier. This does not sit well with the hypothesis that TGF-beta activation depends upon blood-brain barrier leakage.

Thank you for pointing out this lack of clarity. We have added a discussion paragraph that clarifies our hypothesis: “As mentioned above, albumin is a known activator of TGF-β signaling, and TGF-β has a well-established role in neuroplasticity. Interestingly, emerging evidence suggests that TGF-β also increases cross-BBB transcytosis (Betterton et al., 2022; Kaplan et al., 2020; McMillin et al., 2015; Schumacher et al., 2023). Hence, we propose the following two-part hypothesis for the TGF-β/BBB-mediated synaptic potentiation observed in our experiments: (1) prolonged stimulation triggers TGF-β signaling and increased caveolae-mediated transcytosis of albumin; and (2) extravasated albumin induces further TGF-β signaling, leading to synaptogenesis and additional cross-BBB transport – in a self-reinforcing positive feedback loop. Future research is needed to examine the validity of this hypothesis.

Reviewer #3 (Public Review):

Summary:

This study used prolonged stimulation of a limb to examine possible plasticity in somatosensory evoked potentials induced by the stimulation. They also studied the extent that the blood-brain barrier (BBB) was opened by prolonged stimulation and whether that played a role in the plasticity. They found that there was potentiation of the amplitude and area under the curve of the evoked potential after prolonged stimulation and this was long-lasting (>5 hrs). They also implicated extravasation of serum albumin, caveolae-mediated transcytosis, and TGFb signalling, as well as neuronal activity and upregulation of PSD95. Transcriptomics was done and implicated plasticity-related genes in the changes after prolonged stimulation, but not proteins associated with the BBB or inflammation. Next, they address the application to humans using a squeeze ball task. They imaged the brain and suggested that the hand activity led to an increased permeability of the vessels, suggesting modulation of the BBB.

Strengths:

The strengths of the paper are the novelty of the idea that stimulation of the limb can induce cortical plasticity in a normal condition, and it involves the opening of the BBB with albumin entry. In addition, there are many datasets and both rat and human data.

Weaknesses:

The conclusions are not compelling however because of a lack of explanation of methods and quantification. It also is not clear whether the prolonged stimulation in the rat was normal conditions. To their credit, the authors recorded the neuronal activity during stimulation, but it seemed excessive excitation. Since seizures open the BBB this result calls into question one of the conclusions. that the results reflect a normal brain. The authors could either conduct studies with stimulation that is more physiological or discuss the caveats of using a supraphysiological stimulus to infer healthy brain function.

The conclusions are not compelling however because of a lack of explanation of methods and quantification.

Thank you for this comment. In the revised paper, we expanded the Methods section to better describe the procedures and approaches we used for data analysis.

It also is not clear whether the prolonged stimulation in the rat was normal conditions.

We believe that the used stimulation protocol is within the physiological range (and relevant to plasticity, learning and memory) for the following reasons:

1) In our continuous electrophysiological recordings, we did not observe any form of epileptiform or otherwise pathological activity.

2) Memory/training/skill acquisition experiments in humans often involve similar training duration or longer (Bengtsson et al., 2005), e.g., a 30 min thumb training session performed by (Classen et al., 1998).

3) The levels of SEP potentiation we observed are similar to those reported in:

a) Rats following a 10-minute whisker stimulation (one hour post stimulation, (Mégevand et al., 2009)).

b) Humans following a 15 min task (McGregor et al., 2016).

This important point is now presented in the discussion.

Reviewer #1 (Recommendations For The Authors):

The discussion would benefit from additional discussion of the potential impacts of sex and anesthesia in their findings.

We agree with the reviewer and have added the following paragraph to the discussion:

“A key limitation of our animal experiments is the fact they were performed under anesthesia, due to the complex nature of the experimental setup (i.e., simultaneous cortical imaging and electrophysiological recordings). Anesthetic agents can potentially alter neuronal activity, SEPs, CBF, and vascular responses (Aksenov et al., 2015; Lindauer et al., 1993; Masamoto & Kanno, 2012). To minimize these effects, we used ketaminexylazine anesthesia, which unlike other anesthetics, was shown to maintain robust BOLD and SEP responses to neuronal activation (Franceschini et al., 2010; Shim et al., 2018). Another limitation of our animal study is the potentially non-specific effect of mβCD – an agent that disrupts caveola transport but may also lead to cholesterol depletion (Keller & Simons, 1998). To mitigate this issue, we used a very low mβCD concentration (10uM), orders of magnitude below the concentration reported to deplete cholesterol (Koudinov et al). Lastly, our animal study is limited by the inclusion of solely male rats. While our findings in humans did not point to sex-related differences in stimulation-evoked BBB modulation, larger animals and human studies are needed to examine this question.”

The figure text is quite small.

Thank you for pointing this out, we revised all figures and increased font size for clarity.

Including pharmacological concentrations within the figure legends would improve the readability of the manuscript.

Thank you for this suggestion, the figure legends were modified accordingly.

In methods for immunoassays the 5 groups could be more clear by stating that there are 3 timepoints for stimulation experiments. There is a typo in this section where the 24-hour post is stated twice in the same sentence.

Thank you for pointing this out, the text was modified accordingly.

Reviewer #2 (Recommendations For The Authors):

1) In Figure 1, J and K seem to indicate that in these experiments the statisitics were done per slice and not per animal. This is not a reasonable approach, a repeat measure ANOVA or averaging for each animal are more appropriate statistical approaches.

We thank the reviewer for pointing this out. The statistical analysis for Figure 1j,k was modified. We now use a nested ttest to test for differences between rats and not sections. The differences are still significant (EB, p=0.0296; Alexa, p=0.0229). The manuscript was modified accordingly.

2) In Figure 2, the protocol does not seem to give much idea about time course. There was a stimulation test for 1 minute before and then 1 minute after the 30-minute stimulation train. How was potentiation assessed for the next 5 hours and where are the data?

Potentiation was assessed by repeating 1min test stim every 30 min for the duration of the experiment, we added a panel to show late potentiation, see response above.

3) In Figure 2, there is a notable lack of controls eg the effect of sham stimulation and application of saline. These are important as the drift of response magnitude can be a problem in long experiments.

We did test for the potential presence of response drift, by examining whether SEPs of non-stimulated animals change over time (at baseline, 30 or 60 minutes of recording; n=6). No statistical differences were found. Our analysis focused on using each animal as its own control (i.e., comparing baseline SEP to SEP post albumin perfusion), because SEP studies highlight the importance of comparing each animal to its own baseline, due to the large inter-animal variability (All et al., 2010; Mégevand et al., 2009; Zandieh et al., 2003).

4) Figure 3 a is not clear – were the drugs applied throughout?

Thank you for pointing this out. We have revised Figure 3 a to show that the drugs were applied for 50 min before the stimulation.

5) In Figure 3 panel d is repeated in panel j. This needs correcting

Thank you. This mistake was fixed.

6) In LTP-type experiments usually the antagonist is applied during the stimulation and then washed out. This avoids the problem in this figure in which CNQX effectively blocks transmission and so it is not possible to detect any enhancement if it were there. Eg in panel e, CNQX block transmission, and then the assessment is performed when the AMPA receptors are blocked after 30 minutes of stimulation. If receptors are blocked no enhancement will be detectable. Moreover, surely the question is the ratio of the effect of 30-minute stimulation on the SEP in the presence of CNQX and so the statistics should be done on the fold change in the SEP following 30-minute stimulation in the presence of CNQX.

Thank you. The protocol might have been misrepresented in the original figure. We modified Fig 3a to clarify that the antagonists were indeed washed out upon stimulation start to make sure the receptors are not blocked during the test stimulation following the 30 min stimulation. In addition, we tested for the difference in fold change between 30 min stim, and 30 min stimulation following antagonists wash-in (Fig 3f and Fig S2a).

7) Interesting in Figure f, stimulation, albumin, and AP5 all seem to have the same enhancement of the SEP. Is the lack of effect of 30-minute stimulation in the presence of AP5, a ceiling effect ie AP5 has enhanced the SEP, and no further enhancement from stimulation is possible.

This is a very interesting point that will require further research.

8) SJN seems to block neurotransmission. What is the mechanism? The same analysis as for CNQX should be performed ie what is the fold change not compared to baseline but in the presence of SJN.

Our quantification showed that SJN did not significantly reduce the SEP max amplitude, and we therefore did not include this graph in the figure.

9) Please acknowledge that the effect of mbetaCD is non-specific. There is a large literature on the effects of cholesterol depletion on LTP.

We agree that the effect of mβCD may not be specific. To mitigate this issue, we used a very low mβCD concentration (10µM). Notably, this is markedly lower than the concentrations reported by Koudinov et al, showing that cholesterol depletion is only observed at a concentration of 5mM (Koudinov & Koudinova, 2001). This point is now discussed under the discussion paragraph describing the study’s limitations.

10) k&l seem to have used the same control in which case they should not be analysed separately (they are all part of the same experiment).

We agree with the reviewer and have revised the figure accordingly.

11) The difference in gene expression in Figure 4 would be more convincing if it could be prevented by for example a TGFbeta inhibitor.

We agree and acknowledge the impact such experiments could provide. We plan to incorporate these experiments into our future studies.

12) Figure 5 seems to indicate bilateral and widespread BBB modulation arguing that this may be a non-specific effect. Panel g should look at other neocortical regions eg occipital cortex.

We agree and thank the reviewer for this comment. We revised the figure to include other cortical areas, such as the frontal and occipital cortices (Figure 5g)

Minor comments

1) Paired data eg in Fig 2D are better represented by pairing the dots usually with a line.

2) Please correct the %fold baseline in axes in graphs which show % change for baseline.

3) Figure 4 is not correctly referred to in the text.

We agree with all the points raised by the reviewer and revised the figures and text accordingly.

Reviewer #3 (Recommendations For The Authors):

The conclusions are not compelling however because of a lack of explanation of methods and quantification. It also is not clear whether the prolonged stimulation in the rat was normal conditions. To their credit, the authors recorded the neuronal activity during stimulation, but it seemed excessive excitation. Since seizures open the BBB this result calls into question one of the conclusions. that the results reflect a normal brain. The authors could either conduct studies with stimulation that is more physiological or discuss the caveats of using a supraphysiological stimulus to infer healthy brain function.

Major concerns:

Methods need more explanation. Rationales need more justification. Examples are provided below.

Throughout many sections of the paper, sample sizes and stats are often missing. For stats, please provide p-values and other information (tcrit, U statistic, F, etc.)

Thank you, we added the relevant information where it was missing throughout the manuscript.

For transcriptomics, they might have found changes in BBB-related genes if they assayed vessels but they assayed the cortex.

We agree with the reviewer that this would be a very interesting future direction. The present study could not include this kind of analysis due to lack of access to vasculature isolation methods or single-cell RNA seq.

What were the inclusion/exclusion criteria for the subjects?

Thank you for pointing out this lack of clarity. The methods section (under ‘Magnetic Resonance Imaging’ – ‘Participants’) was expanded to include the following:

“Male and female healthy individuals, aged 18-35, with no known neurological or psychiatric disorders were recruited to undergo MRI scanning while performing a motor task (n=6; 3 males and 3 females). MRI scans of 10 sex- and age- matched individuals (with no known neurological or psychiatric disorders) who did not perform the task were used as control data (n=10; 5 males and 5 females.

Were they age and sex-matched?

They were, indeed, age and sex-matched. This was now clarified in the relevant Methods section.

Were there other factors that could have influenced the results?

Certainly. Human subjects are difficult to control for due to different schedules, diets, exercise habits, and other factors that may impact vascular integrity and brain function. Larger multimodal studies are needed to better understand the observed phenomenon.

Fig. 1. Images are very dim. Text here and in other figures is often too small to see. Some parts of the figures are not explained.

Our apologies. Figures and legends were revised accordingly.

Fig 2a, f. I don't see much difference here- do the authors think there was?

We agree that the difference may not be visually obvious. The quantification of trace parameters (amplitude and area under curve) does, however, reveal a significant SEP difference in response to both stimulation (panels X and y) and albumin (panels z and q).

Fig 3 d and j seem the same.

We thank the reviewer for noticing. This was a copy mistake that was now rectified.

Lesser concerns and examples of text that need explana9on:

Introduction

Insulin-like growth factor is transported. From where to where?

The text was edited to clarify that this was cross-BBB influx of insulin-like growth factor-I.

RMT that underlies the transport of plasma proteins was induced by physiological or non-physiological stimulation.

This was shown without stimulation, in normal physiology of young and aged healthy mice. The text was edited to clarify this point.

What was the circadian modulation that was shown to implicate BBB in brain function?

The text was edited for clarity.

Results

When the word stimulation is used please be specific if whiskers are moved by an experimenter, an electrode is used to apply current, etc.

We have now moved the ‘Stimulation protocol’ section closer to beginning of the Methods and emphasized that we administered electrical stimulation to the forepaw or hindlimb using subdermal needle electrodes.

Please explain how the authors are convinced they localized the vascular response.

The vascular response was localized via: (1) visual detection of arterioles that dilated in response to stimulation (due to functional hyperemia / neurovascular coupling) [figure 1 d]; and (2) quantitative mapping of increased hemoglobin concentration (Bouchard et al., 2009) [Figure 1 b]. This is now mentioned in the methods (under ‘In vivo imaging’) and results (under the ‘Stimulation increases BBB permeability’).

"30 min of limb stimulation" means what exactly? 6 Hz 2mA for 30 min?

Thank you. The text was revised for clarity (Methods under ‘Stimulation protocol’):

“The left forelimb or hind limb of the rat was stimulated using Isolated Scmulator device (AD Instruments) attached with two subdermal needle electrodes (0.1 ms square pulses, 2-3 mA) at 6 Hz frequency. Test stimulation consisted of 360 pulses (60 s) and delivered before (as baseline) and after long-duration stimulation (30 min, referred throughout the text as ‘stimulation’). In control and albumin rats, only short-duration stimulations were performed. Under sham stimulation, electrodes were placed without delivering current.”

Histology that was performed to confirm extravasation needs clarification because if tissue was removed from the brain, and fixed in order to do histology, what is outside the vessels would seem likely to wash away.

Thank you for pointing out the need to clarify this point. The Histology description in the Methods section was revised in the following manner:

“Albumin extravasacon was confirmed histologically in separate cohorts of rats that were anesthetized and stimulated without craniotomy surgery. Assessment of albumin extravasacon was performed using a well-established approach that involves peripheral injection of either labeled-albumin (bovine serum albumin conjugated to Alexa Flour 488, Alexa488-Alb) or albumin-labeling dye (Evans blue, EB – a dye that binds to endogenous albumin and forms a fluorescent complex), followed by histological analysis of brain tissue (Ahishali & Kaya, 2020; Ivens et al., 2007; Lapilover et al., 2012; Obermeier et al., 2013; Veksler et al., 2020). Since extravasated albumin is taken up by astrocytes (Ivens et al., 2007; Obermeier et al., 2013), it can be visualized in the brain neuropil after brain removal and fixation (Ahishali & Kaya, 2020; Ivens et al., 2007; Lapilover et al., 2012; Veksler et al., 2020). Five rats were injected with Alexa488-Alb (1.7 mg/ml) and five with EB (2%, 20 mg/ml, n=5). The injections were administered via the tail vein. Following injection, rats were transcardially perfused with…”

It is not clear why there was extravasacon contralateral but not ipsilateral if there are cortical-cortical connections.

Interpersonally, we also did not observe ipsilateral SEP in response to limb stimulation, with evidence of SEP and BBB permeability only in the contralateral sensorimotor region. This finding is consistent with electrophysiological and fMRI studies showing that peripheral stimulation results in predominantly contralateral potentials (Allison et al., 2000; Goff et al., 1962).

After injection of Evans blue or Alexa-Alb, how was it shown that there was extravasacon?

Extravasalon in cortical sections was visualized using a fluorescent microscope (Figure 1 h-i). Since extravasated albumin is taken up by astrocytes, fluorescent imaging can be used for visualizing and quantifying labeled albumin (Ahishali & Kaya, 2020; Ivens et al., 2007; Knowland et al., 2014). Here is the relevant methods excerpt:

“Coronal sections (40-μm thick) were obtained using a freezing microtome (Leica Biosystems) and imaged for dye extravasacon using a fluorescence microscope (Axioskop 2; Zeiss) equipped with a CCD digital camera (AxioCam MRc 5; Zeiss).”

How is a sham control not stimulated - what is the sham procedure?

In the sham stimulation protocol electrodes were placed, but current was not delivered. A section titled ‘Stimulation protocol’ was added to the methods to clarify this point.

What was the method for photothrombosis-induced ischemia?

The procedure for photothrombosis-induced ischemia is described under the Methods section ‘Immunoassays’ – ‘Enzyme-linked immunosorbent assay (ELISA) for albumin extravasalon’:

“Rats were anesthetilzed and underwent … photothrombosis stroke (PT) as previously described (Lippmann et al., 2017; Schoknecht et al., 2014). Briefly, Rose Bengal was administered intravenously (20 mg/kg) and a halogen light beam was directed for 15 min onto the intact exposed skull over the right somatosensory cortex.”

Fig 1d. All parts of d are not explained.

Thank you for pointing this out. In the revised manuscript, the panels of this figure were slightly reordered, and we made sure all panels are explained in the legend.

e. Is the LFP a seizure? How physiological is this- it does not seem very physiological.

Thank you for your comment. We believe that this activity is not a seizure because it lacks the typical slow activity that corresponds to the “depolarizalon shir” observed during seizures (Ivens et al., 2007; Milikovsky et al., 2019; Zelig et al., 2022).

f. Permeability index needs explanation. How was the area chosen for each rat? Randomly? Was it the same across rats?

We have now revised the Methods section to provide a clearer description of the permeability index calculation and the choice of the imaging area:

“Across all experiments, acquired images were the same size (512 × 512 pixel, ~1x1 mm), centered above the responding arteriole. Images were analyzed offline using MATLAB as described (Vazana et al., 2016). Briefly, image registration and segmentation were performed to produce a binary image, separating blood vessels from extravascular regions. For each extravascular pixel, a time curve of signal intensity over time was constructed. To determine whether an extravascular pixel had tracer accumulation over time (due to BBB permeability), the pixel’s intensity curve was divided by that of the responding artery (i.e., the arterial input function, AIF, representing tracer input). This ratio was termed the BBB permeability index (PI), and extravascular pixels with PI > 1 were identified as pixels with tracer accumulation due to BBB permeability.”

g. For Evans blue and Alexa-Alb was the sample size rats or sections?

Thank you for this question. We revised the statistical analysis for Figure 1j,k to appropriately asses the differences between rats. We used a nested t-test to test for differences between rats (and not sections). The differences remained significant (EB, p=0.0296; Alexa, p=0.0229) and the text was modified accordingly.

h, i, j need more contrast and/or brightness to appreciate the images. Arrows would help. The text is too small to read.

Thank you. This issue was addressed in the revised paper.

To induce potentiation, 6 Hz 2 mA stimuli were used for 30 min. Please justify this as physiological.

Thank you for the comment. We believe that the used stimulation protocol is within the physiological range (and relevant to plasticity, learning and memory) for the following reasons:

1. In our continuous electrophysiological recordings, we did not observe any form of epileptiform or otherwise pathological activity.

2. Memory/training/skill acquisition experiments in humans often involve similar training duration or longer (Bengtsson et al., 2005), e.g., a 30 min thumb training session performed by (Classen et al., 1998).

3. The levels of SEP potentiation we observed are similar to those reported in:

a. Rats following a 10-minute whisker stimulation (one hour post stimulation, (Mégevand et al., 2009)).

b. Humans following a 15 min task (McGregor et al., 2016).

We have revised the Discussion of the paper to clarify this important point.

The test stimulus to evoke somatosensory evoked potentials was 1 min. Was this 6 Hz 2 mA for 1 min? Please justify.

Yes. We chose these parameters as these ranges were shown to induce the largest changes in blood flow (with laserdoppler flowmetry) and summated SEP (Ngai et al., 1999), corresponding with our findings. We also show that these stimulation parameters do not induce changes in BBB permeability nor synaptic potentiation, therefore served as test control.

How long after the 30 min was the test stimulus triggered- immediately? 30 sec afterwards?

The test stimulus was applied 5 min afterwards to allow for BBB imaging protocol (now explained in the Methods section).

How were amplitude and AUC measured? Baseline to peak? For AUC is it the sum of the upward and downward deflections comprising the LFP?

Yes, and yes. This is now clarified in the ‘Analysis of electrophysiological recordings’ section in the Methods.

How was the same site in the somatosensory cortex recorded for each animal?<br /> Potentiation was said to last >5 hrs. How often was it measured? Was potentiation the same for the amplitude and the AUC?

The location of the cranial window over the somatosensory cortex was the same in all rats. The location of the specific responding arteriole may change between animals, but the recording electrode was places around the responding arteriole in the same approaching angle and depth for all animals.

As the length of experiments differed between animals, the exact length could not be specifically stated. We therefore revised the text to clarify that LTP was recorded until the end of each experiment (depending on the animal condition, between 1.5-5 hours) and added a panel to figure 2 (Figure 2f) with exemplary data showing potentiation 120 min (2hr) post stimulation.

Why was 25% of the serum level of albumin selected- does the brain ever get exposed to that much? Was albumin dissolved in aCSF or was aCSF chosen as a control for another reason?

Yes, albumin was dissolved in aCSF and the solution was allowed to diffuse through the brain. The relatively high concentration of albumin was chosen to account for factors that lower its effective tissue concentration:

1. The low diffusion rate of albumin (Tao & Nicholson, 1996).

2. The likelihood of albumin to encounter a degradation site or a cross-BBB efflux transporter (Tao & Nicholson, 1996; Zhang & Pardridge, 2001).

Figure 2.

a. Please show baseline, the stimulus, and aftier the stimulus.

Please point out when there was stimulacon.

What is the inset at the top?

The inset on top is the example trace of the stimulus waveform, the legend of the figure was modified for clarity.

b. Please show when the stimulus artifact occurred. The end of the 1-minute test stimulus period is fine. Why are the SEPs different morphologies? It suggests the different locations in the cortex were recorded.

What is shown is the averaged SEP response over 1min test stimulus, each SEP is time locked to each stimulus. Regarding SEP waveform, it does indeed show different morphology between animals, as sometimes different arterioles respond to the stimulation, and we localize the recording to the responding vessel in each rat. However, in each rat the recording is only from one location. Once the electrode was positioned near the responding arteriole it was not moved.

d, e. What are the stats?

h, i. Add stats. Are all comparisons Wilcoxon? Please provide p values.

The comparisons were performed with the Wilcoxon test. We now state that and provide the exact p values.

j. What was selected from the baseline and what was selected during Albumin and how long of a record was selected?

What program was used to create the spectrogram?

What is meant by changes at frequencies above 200 Hz, the frequencies of HFOs?

The Method section (under ‘Electrophysiology – Data acquisition and analyses’) has been revised for clarification. Spectrogram was created with MATLAB and graphed with Prism. For analysis, we selected a 10 min recorded segment before starting albumin perfusion, and 10 min after terminating albumin perfusion.

When the cortial window was exposed to drugs, what were concentrations used that were selective for their receptor? How long was the exposure?

Was the vehicle tested?

We have revised the Methods section (under ‘Animal preparation and surgical procedures - Drug application’) to clarify the duration and concentration used and justification. All blockers were exposed for 50 min. The vehicle was an artificial cerebrospinal fluid solution (aCSF).

For PSD-95, what was the area of the cortex that was tested?

Were animals acutely euthanized and the brain dissected, frozen, etc?

We have revised the Methods section (under ‘Immunoassays’) for clarity.

What is mbetaCD?

The full term was added to the results section. It is also mentioned in the Methods.

Is SJN specific at the concentration that was chosen? Did it inhibit the SEP?

In the concentration used in our experiments, SJN is a selective TGF-β type I receptor ALK5 inhibitor (see (Gellibert et al., 2004)).

Fig. 3b. It looks like CNQX increased the width of the vessels quite a bit. Please explain.

For AP5, very large vessels were imaged, making it hard to compare to the other data.

The vascular dilation in response to the stimulation under CNQX was similar to that seen under “normal” conditions (i.e. aCSF). As for AP5, in some experiments the responding arteriole was in close proximity to a large venule that cannot be avoidable while imaging. For quantification we always measured arterioles within the same diameter range.

e. Sometimes CNQX did not block the response after 30 min stimulation. Why?

CNQX is washed out before the 30 min stimulation starts, so it is not expected to block the response to stimulation. However, in some cases the response to stimulation was lower in amplitude, likely due to residual CNQX that did not wash out completely.

Regarding DEGs, on the top of p 10 what are the percentages of?

In this analysis we tested in each hemisphere how many genes expressed differentially between 1 and 24 hours post stimulation (either up- or down- regulated). The results were presented as the percentages of differentially expressed genes in each hemisphere (13.2% contralateral, and 7.3% ipsilateral). The text was rephrased for clarity.

Please add a ref for the use of the JSD metric methods and support for its use as the appropriate method. Other methods need explanation/references.

References were added to the text to clarify. The Jensen-Shannon Divergence metric is commonly used to calculate the statistical pairwise distance among two distributions (Sudmant et al., 2015). From comparing a few different distance metric calculations including JSD, our results were similar irrespective of the distance metric applied. Therefore, we demonstrate the variability between paired samples of stimulated and non-stimulated cortex of each animal at two time points following stimulation (24 h vs. 1 h) using JSD.

What synaptic plasticity genes were selected for assay and what were not?

What does "largely unaffected" mean? Some of the genes may change a small amount but have big functional effects.

The selected genes of interest were taken from a large list compiled from previous publications (see (Cacheaux et al., 2009; Kim et al., 2017)) and are well documented in gene ontology databases and tools (e.g., Metascape, (Zhou et al., 2019)).

We agree that the term ‘largely unaffected’ is suboptimal, and we rephrased this section of the results to indicate that “No significant differences were found in BBB or inflammation related genes between the hemispheres”. We also agree that a small number of genes can have big functional effects. Future studies are needed to better understand the genes underlying the observed BBB modulation.

Please note that Slc and ABCs are not only involved in the BBB.

Thank you. We modified the text to no longer specify that these are BBB-specific transporters.

Please explain the choice of the stress ball squeeze task, and DCE.

DCE is a well-established method for BBB imaging in living humans, and it is cited throughout the manuscript. The ball squeeze task was chosen as it is presumed to involve primarily sensory motor areas, without high-level processing (Halder et al., 2005). This is now stated in the discussion.

What is Gd-DOTA?

Gd-DOTA is a gadolinium-based contrast agent (gadoterate meglumine, AKA Dotarem). Text was revised for clarity. Please see the Methods section under ‘Magnetic Resonance Imaging’ - ‘Data Acquisition’.

What does a higher percentage of activated regions mean- how was activacon defined and how were regions counted?

Higher percentage of activated regions refers to regions in which voxels showed significant BOLD changes due to the motor task preformed. The statistical approaches and analyses are detailed in the Methods section under ‘Magnetic Resonance Imaging - Preprocessing of functional data, and fMRI Localizer Motor Task’.

Figure. 4

Was stimulation 1 min or 30 min.?

30 min, Text has been revised for clarity.

What is the Wald test and how were p values adjusted-please add to the Stats section.

The Methods section under ‘Statistical analysis’ was revised to clarify this point.

Is there a reason why p values are sometimes circles and otherwise triangles?

The legend was revised to explain that ”Circles represent genes with no significant differences between 1 and 24 h poststimulation. Upward and downward triangles indicate significantly up- and down- regulated genes, respectively.”

How can a p-value be zero? Please explain abbreviations.

The p-value is very low (~10-10) and therefore appears to be zero due to the scale of the y-axis.

Fig. 5b.

There are unexplained abbreviations.

The x on the ball and hand is not clear relative to the black ball and hand.

Thank you for noticing. We revised the figure for clarity.

c. What was the method used to make an activator map and what is meant by localizer task?

The explanation of the “fMRI Localizer Motor Task” section in the methods was revised for added clarity.

f. What is the measurement "% area" that indicates " BBB modulation"?

Is it in f, the BBB permeable vessels (%)? f. Please explain: "Heatmap of BBB modulated voxels percentage in motor/sensory-related areas of task vs. controls."

The %area measurement indicates the percentage of voxels within a specific brain region that have a leaky BBB. See Methods.

Is Task - the control?

Yes.

Supplemental Fig. 2.

Why is AUC measured, not amplitude?

The amplitude, and now also the AUC are shown in Figure 3.

b. There is no comparison to baseline. The arrowhead points to the start of stimulation but there is no arrowhead marking the end.

In the revised paper we added a grey shade over the stimulation period to better visualize the difference to baseline. In this panel we wanted to show that NMDA receptor antagonist did not block the SEP, while AMPA receptor antagonist did.

c. In the blot there are two bands for PSD95- which is the one that is PSD95? There is no increase in PSD95 uncl 24 hrs but in the graph in d there is. In the blot, there is a strong expression of PSD95 ipsilateral compared to contralateral in the sham-why?

What is the percent change fold?

The PSD-95 is the top and larger band. The lower band was disregarded in the analysis. The example we show may not fully reflect the group statistics presented in panel d. Upon quantification of 8 animals, PSD-95 is significantly higher 30 min and 24 hours post stimulation in the contralateral hemisphere. No significant changes were found in sham animals. The % change fold refers to the AUC change compared to baseline. This panel was now incorporated in Figure 3 (panel h), and the title was corrected to “|AUC|, % change from baseline”.

Supplemental Fig. 4.

a. If ipsilateral and contralateral showed many changes why do the authors think the effects were only contralateral?

Our gene analysis was designed to complement our in vivo and histological findings, by assessing the magnitude of change in differentially expressed genes (DEGs). This analysis showed that: (1) the hemisphere contralateral to the stimulus has significantly more DEGs than the ipsilateral hemisphere; and (2) the DEGs were related to synaptic plasticity and TGF-b signaling. These findings strengthen the hypothesis raised by our in vivo and histological experiments.

Supplemental Fig. 5 includes many processes not in the results. Examples include dorsal cuneate and VPL, dynamin, Kir, mGluR, etc. The top right has numbers that are not mentioned. If the drawings are from other papers they should be cited.

The drawings of Figure 5 are original and were not published before. This hypothesis figure points to mechanisms that may drive the phenomena described in the paper. The legend of the figure was revised to include references to mechanisms that were not tested in this study.

Papers referenced in this letter:

Ahishali, B., & Kaya, M. (2020). Evaluation of Blood-Brain Barrier Integrity Using Vascular Permeability Markers: Evans Blue, Sodium Fluorescein, Albumin-Alexa Fluor Conjugates, and Horseradish Peroxidase. Methods in Molecular Biology, 2367, 87–103. https://doi.org/10.1007/7651_2020_316

Aksenov, D. P., Li, L., Miller, M. J., Iordanescu, G., & Wyrwicz, A. M. (2015). Effects of anesthesia on BOLD signal and neuronal activity in the somatosensory cortex. Journal of Cerebral Blood Flow and Metabolism, 35(11), 1819–1826. https://doi.org/10.1038/jcbfm.2015.130

All, A. H., Agrawal, G., Walczak, P., Maybhate, A., Bulte, J. W. M., & Kerr, D. A. (2010). Evoked potential and behavioral outcomes for experimental autoimmune encephalomyelitis in Lewis rats. Neurological Sciences, 31(5), 595–601. https://doi.org/10.1007/s10072-010-0329-y

Allison, J. D., Meador, K. J., Loring, D. W., Figueroa, R. E., & Wright, J. C. (2000). Functional MRI cerebral activation and deactivation during finger movement. Neurology, 54(1), 135–142. https://doi.org/10.1212/wnl.54.1.135

Bengtsson, S. L., Nagy, Z., Skare, S., Forsman, L., Forssberg, H., & Ullén, F. (2005). Extensive piano practicing has regionally specific effects on white matter development. Nature Neuroscience, 8(9), 1148–1150. https://doi.org/10.1038/nn1516

Betterton, R. D., Abdullahi, W., Williams, E. I., Lochhead, J. J., Brzica, H., Stanton, J., Reddell, E., Ogbonnaya, C., Davis, T. P., & Ronaldson, P. T. (2022). Regula/on of Blood-Brain Barrier Transporters by Transforming Growth Factor-β/Activin Receptor-Like Kinase 1 Signaling: Relevance to the Brain Disposition of 3-Hydroxy-3-Methylglutaryl Coenzyme A Reductase Inhibitors (i.e., Sta/ns). Drug Metabolism and Disposition, 50(7), 942–956. https://doi.org/10.1124/dmd.121.000781

Bouchard, M. B., Chen, B. R., Burgess, S. A., & Hillman, E. M. C. (2009). Ultra-fast multispectral optical imaging of cortical oxygenation, blood flow, and intracellular calcium dynamics. Optics Express, 17(18), 15670. https://doi.org/10.1364/oe.17.015670

Cacheaux, L. P., Ivens, S., David, Y., Lakhter, A. J., Bar-Klein, G., Shapira, M., Heinemann, U., Friedman, A., & Kaufer, D. (2009). Transcriptome profiling reveals TGF-β signaling involvement in epileptogenesis. Journal of Neuroscience, 29(28), 8927–8935. https://doi.org/10.1523/JNEUROSCI.0430-09.2009

Classen, J., Liepert, J., Wise, S. P., Hallett, M., & Cohen, L. G. (1998). Rapid plasticity of human cortical movement representation induced by practice. Journal of Neurophysiology, 79(2), 1117–1123. https://doi.org/10.1152/JN.1998.79.2.1117/ASSET/IMAGES/LARGE/JNP.JA47F4.JPEG

Franceschini, M. A., Radhakrishnan, H., Thakur, K., Wu, W., Ruvinskaya, S., Carp, S., & Boas, D. A. (2010). The effect of different anesthetics on neurovascular coupling. NeuroImage, 51(4), 1367–1377. https://doi.org/10.1016/j.neuroimage.2010.03.060

Gellibert, F., Woolven, J., Fouchet, M. H., Mathews, N., Goodland, H., Lovegrove, V., Laroze, A., Nguyen, V. L., Sautet, S., Wang, R., Janson, C., Smith, W., Krysa, G., Boullay, V., De Gouville, A. C., Huet, S., & Hartley, D. (2004). Identification of 1,5-naphthyridine derivatives as a novel series of potent and selective TGF-β type I receptor inhibitors. Journal of Medicinal Chemistry, 47(18), 4494–4506. https://doi.org/10.1021/jm0400247

Goff, W. R., Rosner, B. S., & Allison, T. (1962). Distribution of cerebral somatosensory evoked responses in normal man. Electroencephalography and Clinical Neurophysiology, 14(5), 697–713. https://doi.org/10.1016/0013-4694(62)90084-6

Halder, P., Sterr, A., Brem, S., Bucher, K., Kollias, S., & Brandeis, D. (2005). Electrophysiological evidence for cortical plasticity with movement repetition. European Journal of Neuroscience, 21(8), 2271–2277. https://doi.org/10.1111/J.1460-9568.2005.04045.X

Ivens, S., Kaufer, D., Flores, L. P., Bechmann, I., Zumsteg, D., Tomkins, O., Seiffert, E., Heinemann, U., & Friedman, A. (2007). TGF-β receptor-mediated albumin uptake into astrocytes is involved in neocortical epileptogenesis. Brain, 130(2), 535–547. https://doi.org/10.1093/brain/awl317

Kaplan, L., Chow, B. W., & Gu, C. (2020). Neuronal regulation of the blood–brain barrier and neurovascular coupling. In Nature Reviews Neuroscience (Vol. 21, Issue 8, pp. 416–432). Nature Research. https://doi.org/10.1038/s41583-020-0322-2

Keller, P., & Simons, K. (1998). Cholesterol is required for surface transport of influenza virus hemagglutinin. Journal of Cell Biology, 140(6), 1357–1367. https://doi.org/10.1083/jcb.140.6.1357

Kim, S. Y., Senatorov, V. V., Morrissey, C. S., Lippmann, K., Vazquez, O., Milikovsky, D. Z., Gu, F., Parada, I., Prince, D. A., Becker, A. J., Heinemann, U., Friedman, A., & Kaufer, D. (2017). TGFβ signaling is associated with changes in inflammatory gene expression and perineuronal net degradation around inhibitory neurons following various neurological insults. Scientific Reports, 7(1), 7711. https://doi.org/10.1038/s41598-017-07394-3

Knowland, D., Arac, A., Sekiguchi, K. J., Hsu, M., Lutz, S. E., Perrino, J., Steinberg, G. K., Barres, B. A., Nimmerjahn, A., & Agalliu, D. (2014). Stepwise Recruitment of Transcellular and Paracellular Pathways Underlies Blood-Brain Barrier Breakdown in Stroke. Neuron, 82(3), 603–617. https://doi.org/10.1016/j.neuron.2014.03.003

Koudinov, A. R., & Koudinova, N. V. (2001). Essen/al role for cholesterol in synaptic plasticity and neuronal degeneration. The FASEB Journal, 15(10), 1858–1860. https://doi.org/10.1096/r.00-0815re

Lapilover, E. G., Lippmann, K., Salar, S., Maslarova, A., Dreier, J. P., Heinemann, U., & Friedman, A. (2012). Periinfarct blood-brain barrier dysfunction facilitates induction of spreading depolarization associated with epileptiform discharges. Neurobiology of Disease, 48(3), 495–506. htttts://doi.org/10.1016/j.nbd.2012.06.024

Lindauer, U., Villringer, A., & Dirnagl, U. (1993). Characterization of CBF response to somatosensory stimulation: Model and influence of anesthetics. American Journal of Physiology - Heart and Circulatory Physiology, 264(4 33-4), 223–1228. https://doi.org/10.1152/ajpheart.1993.264.4.h1223

Lippmann, K., Kamintsky, L., Kim, S. Y., Lublinsky, S., Prager, O., Nichtweiss, J. F., Salar, S., Kaufer, D., Heinemann, U., & Friedman, A. (2017). Epileptiform activity and spreading depolarization in the bloodbrain barrier-disrupted peri-infarct hippocampus are associated with impaired GABAergic inhibition and synaptic plasticity. Journal of Cerebral Blood Flow and Metabolism, 37(5), 1803–1819. https://doi.org/10.1177/0271678X16652631

Masamoto, K., & Kanno, I. (2012). Anesthesia and the quantitative evaluation of neurovascular coupling. In Journal of Cerebral Blood Flow and Metabolism (Vol. 32, Issue 7, pp. 1233–1247). SAGE PublicationsSage UK: London, England. https://doi.org/10.1038/jcbfm.2012.50

McGregor, H. R., Cashaback, J. G. A., & Gribble, P. L. (2016). Functional Plasticity in Somatosensory Cortex Supports Motor Learning by Observing. Current Biology, 26(7), 921–927. https://doi.org/10.1016/j.cub.2016.01.064

McMillin, M. A., Frampton, G. A., Seiwell, A. P., Patel, N. S., Jacobs, A. N., & DeMorrow, S. (2015). TGFβ1 exacerbates blood-brain barrier permeability in a mouse model of hepatic encephalopathy via upregulation of MMP9 and downregulation of claudin-5. Laboratory Investigation, 95(8), 903–913. https://doi.org/10.1038/labinvest.2015.70

Mégevand, P., Troncoso, E., Quairiaux, C., Muller, D., Michel, C. M., & Kiss, J. Z. (2009). Long-term plasticity in mouse sensorimotor circuits after rhythmic whisker stimulation. Journal of Neuroscience, 29(16), 5326– 5335. https://doi.org/10.1523/JNEUROSCI.5965-08.2009

Milikovsky, D. Z., Ofer, J., Senatorov, V. V., Friedman, A. R., Prager, O., Sheintuch, L., Elazari, N., Veksler, R., Zelig, D., Weissberg, I., Bar-Klein, G., Swissa, E., Hanael, E., Ben-Arie, G., Schefenbauer, O., Kamintsky, L., Saar-Ashkenazy, R., Shelef, I., Shamir, M. H., … Friedman, A. (2019). Paroxysmal slow cortical activity in Alzheimer’s disease and epilepsy is associated with blood-brain barrier dysfunction. Science Translational Medicine, 11(521), eaaw8954–eaaw8954. https://doi.org/10.1126/scitranslmed.aaw8954

Ngai, A. C., Jolley, M. A., D’Ambrosio, R., Meno, J. R., & Winn, H. R. (1999). Frequency-dependent changes in cerebral blood flow and evoked potentials during somatosensory stimulation in the rat. Brain Research, 837(1–2), 221–228. https://doi.org/10.1016/S0006-8993(99)01649-2

Obermeier, B., Daneman, R., & Ransohoff, R. M. (2013). Development, maintenance and disruption of the blood-brain barrier. In Nature Medicine (Vol. 19, Issue 12, pp. 1584–1596). Nature Publishing Group. https://doi.org/10.1038/nm.3407

Schoknecht, K., Prager, O., Vazana, U., Kamintsky, L., Harhausen, D., Zille, M., Figge, L., Chassidim, Y., Schellenberger, E., Kovács, R., Heinemann, U., & Friedman, A. (2014). Monitoring stroke progression: In vivo imaging of cortical perfusion, blood-brain barrier permeability and cellular damage in the rat photothrombosis model. Journal of Cerebral Blood Flow and Metabolism, 34(11), 1791–1801. https://doi.org/10.1038/jcbfm.2014.147

Schumacher, L., Slimani, R., Zizmare, L., Ehlers, J., Kleine Borgmann, F., Fitzgerald, J. C., Fallier-Becker, P., Beckmann, A., Grißmer, A., Meier, C., El-Ayoubi, A., Devraj, K., Mittelbronn, M., Trautwein, C., & Naumann, U. (2023). TGF-Beta Modulates the Integrity of the Blood Brain Barrier In Vitro, and Is Associated with Metabolic Alterations in Pericytes. Biomedicines, 11(1), 1–19. https://doi.org/10.3390/biomedicines11010214

Shim, H. J., Jung, W. B., Schlegel, F., Lee, J., Kim, S., Lee, J., & Kim, S. G. (2018). Mouse fMRI under ketamine and xylazine anesthesia: Robust contralateral somatosensory cortex ac/va/on in response to forepaw stimulation. NeuroImage, 177, 30–44. https://doi.org/10.1016/J.NEUROIMAGE.2018.04.062

Sudmant, P. H., Alexis, M. S., & Burge, C. B. (2015). Meta-analysis of RNA-seq expression data across species, tissues and studies. Genome Biology, 16(1), 287. https://doi.org/10.1186/s13059-015-0853-4

Tao, L., & Nicholson, C. (1996). Diffusion of albumins in rat cortical slices and relevance to volume transmission. Neuroscience, 75(3), 839–847. https://doi.org/10.1016/0306-4522(96)00303-X

Vazana, U., Veksler, R., Pell, G. S., Prager, O., Fassler, M., Chassidim, Y., Roth, Y., Shahar, H., Zangen, A., Raccah, R., Onesti, E., Ceccanti, M., Colonnese, C., Santoro, A., Salvati, M., D’Elia, A., Nucciarelli, V., Inghilleri, M., & Friedman, A. (2016). Glutamate-mediated blood–brain barrier opening: Implications for neuroprotection and drug delivery. Journal of Neuroscience, 36(29), 7727–7739. https://doi.org/10.1523/JNEUROSCI.0587-16.2016

Veksler, R., Vazana, U., Serlin, Y., Prager, O., Ofer, J., Shemen, N., Fisher, A. M., Minaeva, O., Hua, N., SaarAshkenazy, R., Benou, I., Riklin-Raviv, T., Parker, E., Mumby, G., Kamintsky, L., Beyea, S., Bowen, C. V., Shelef, I., O’Keeffe, E., … Friedman, A. (2020). Slow blood-to-brain transport underlies enduring barrier dysfunction in American football players. Brain, 143(6), 1826–1842. https://doi.org/10.1093/brain/awaa140

Zandieh, S., Hopf, R., Redl, H., & Schlag, M. G. (2003). The effect of ketamine/xylazine anesthesia on sensory and motor evoked potentials in the rat. Spinal Cord, 41(1), 16–22. https://doi.org/10.1038/sj.sc.3101400

Zelig, D., Goldberg, I., Shor, O., Ben Dor, S., Yaniv-Rosenfeld, A., Milikovsky, D. Z., Ofer, J., Imtiaz, H., Friedman, A., & Benninger, F. (2022). Paroxysmal slow wave events predict epilepsy following a first seizure. Epilepsia, 63(1), 190–198. https://doi.org/10.1111/epi.17110

Zhang, Y., & Pardridge, W. M. (2001). Mediated efflux of IgG molecules from brain to blood across the blood– brain barrier. Journal of Neuroimmunology, 114(1–2), 168–172. https://doi.org/10.1016/S01655728(01)00242-9

Zhou, Y., Zhou, B., Pache, L., Chang, M., Khodabakhshi, A. H., Tanaseichuk, O., Benner, C., & Chanda, S. K. (2019). Metascape provides a biologist-oriented resource for the analysis of systems-level datasets. Nature Communications, 10(1), 1–10. https://doi.org/10.1038/s41467-019-09234-6

Author Response

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

eLife assessment

This study presents a valuable finding for the treatment of PCCs by sequencing 16 tumor specimens from five patients with pheochromocytomas by single-cell transcriptomics and proposing a new molecular classification criterion based on the sequencing results and characterization of tumor microenvironmental features. The evidence supporting the claims of the authors is solid, although the inclusion of more patient samples would strengthen the study's conclusions. The work will be of interest to clinicians or medical biologists working on rare pheochromocytomas (PCCs).

Firstly, we sincerely appreciate the positive feedback from the editor and extend our gratitude to the three reviewers for their meticulous review and valuable comments. Our detailed responses to each recommendation are outlined below.

Response to reviewers’ recommendations

Reviewer #1 (Recommendations for The Authors):

1) Transcriptomal clonal dynamics of different PCCs is well written. However for conclusion sample size needs to be more.

Acknowledging the rarity of PCCs with an incidence of approximately 0.2 to 0.6 cases per 100,000 person-years (Farrugia & Charalampopoulos, 2019; Neumann et al, 2019), our study recognizes the limitation in sample size, as discussed in the limitations section (Page 22). In response to this concern, we are committed to undertaking further research with an expanded sample size to bolster the robustness of our conclusions, seeking a more comprehensive understanding of tumor microenvironment characterization and molecular classification in PCCs. We appreciate the valuable guidance provided by the reviewer.

2) Clinical, biochemistry data of 5 cases can be analysed. Any findings in different categories as per postulated classification can be noted for further studies. Example: epinephrine levels

We have now included the clinical information of 5 PCC patients, encompassing signs and symptoms, the tumor size, and laboratory test results in the revised manuscript as Supplemental Table S3 (Page 11-12). Notably, our analysis revealed that the kinase-type PCC patient (P4) exhibited higher blood pressures and plasma levels of catecholamine metabolites (3-methoxytyramine and normetanephrine) compared to metabolism-type PCC patients (P1-P3, and P5). This observation aligns with the elevated expression of phenylethanolamine N-methyltransferase (PNMT), an enzyme involved in the biosynthesis of catecholamine and linked to hypertension, in P4, as identified in the scRNA-seq data (Figure 4B and 4D) (Kennedy et al, 1993; Konosu-Fukaya et al, 2018; Nguyen et al, 2015). As suggested, we plan to conduct further research to explore the correlation of our molecular classification with plasma levels of catecholamine metabolites, and the relevant points have been discussed in the revision (Page 20).

We would like to take this chance to again thank the reviewer for the careful review and very helpful guidance about how to improve our study.

References for Reviewer #1:

Farrugia FA, Charalampopoulos A (2019) Pheochromocytoma. Endocrine regulations 53: 191-212 Neumann HPH, Young WF, Jr., Eng C (2019) Pheochromocytoma and Paraganglioma. The New England journal of medicine 381: 552-565

Kennedy B, Elayan H, Ziegler MG (1993) Glucocorticoid hypertension and nonadrenal phenylethanolamine N-methyltransferase. Hypertension (Dallas, Tex : 1979) 21: 415419

Konosu-Fukaya S, Omata K, Tezuka Y, Ono Y, Aoyama Y, Satoh F, Fujishima F, Sasano H, Nakamura Y (2018) Catecholamine-Synthesizing Enzymes in Pheochromocytoma and Extraadrenal Paraganglioma. Endocrine pathology 29: 302309

Nguyen P, Khurana S, Peltsch H, Grandbois J, Eibl J, Crispo J, Ansell D, Tai TC (2015) Prenatal glucocorticoid exposure programs adrenal PNMT expression and adult hypertension. The Journal of endocrinology 227: 117-127

Reviewer #2 (Recommendations for The Authors):

1) Please revise all references to "malignant potential", "malignant behavior", etc. throughout the article, including the abstract and introduction, and replace them with the word "metastasis" as appropriate. Since all PCCs are malignant non-epithelial neuroendocrine neoplasms originating from the paraganglia, which are themselves malignant tumors, it is unacceptable to describe them as "malignant potential" or "malignant potential". Please review the 2022 WHO/IARC classification and description of pheochromocytoma/paraganglioma (reference: Mete O, Asa SL, Gill AJ, Kimura N, de Krijger RR, Tischler A. Overview of the 2022 WHO Classification of Paragangliomas and Pheochromocytomas. Endocr Pathol. 2022;33(1):90-114. doi:10.1007/s12022-022-09704-6).

As suggested, we have replaced all occurrences of “malignant potential” or “malignant behavior” with “metastasis” throughout the revised manuscript. We have also included a citation to the 2022 WHO/IARC classification for further clarity.

• Similarly, it is not advisable to use the PASS score to predict "malignant" PCC; this type of scoring system evaluates the "metastasis risk" or the "metastasis potential" of PCC.

We appreciate the reviewer for this insight and have revised our statements accordingly.

• Also, "MALIGNANT CHAFFIN CELLS" needs to be modified; in fact, it is the "tumor cell of PCC" that the authors are trying to express.

As suggested, we have amended the term “malignant chromaffin cells” to “PCC cells” in the revised manuscript (Page 9-10).

2) How does the PASS score specifically relate to intra-tumor heterogeneity as reflected by scRNA-seq? In fact, the PASS score evaluates the histological or pathological invasiveness of PCC, and different sections of the same tumor tissue may have different histological manifestations, which may affect the score; however, scRNA-seq analyzes the cellular composition of the tumor, which is not the same as the information reflected by the PASS score. Both represent different levels and dimensions of intra-tumor heterogeneity and should be analyzed together. Please specifically list, one by one, the proportion of each item score of the PASS system and cell type of scRNA-seq for each sample and the results of the comparisons with each other to better present the conclusions.

As suggested, we have included the proportion of each item score from the PASS system in the revised manuscript as Supplemental Table S2 (Page 8). Integrating this data with the cell type composition of each sample from Figure 2B, our analysis suggests that intra-tumor heterogeneity, as assessed by the PASS system, is more extensive compared to scRNA-seq. We concur with the reviewer’s judgement that scRNA-seq analysis and PASS score represent different levels and dimensions of intratumor heterogeneity, and we have adjusted our claim throughout the revised manuscript accordingly (Page 8, 9, and 19).

3) Where is the specific mutation site of the VHL gene in patient 5? Please advise.

The VHL gene mutation site, c.499C>T (missense mutation), in patient 5 was identified through whole exome sequencing (WES) analysis. We have now added the information to Supplemental Table S1 in the revised manuscript (Page 6).

4) Please revise Supplementary Figure 1, the scale should not appear in the picture of the staining result of P5.

As suggested, we have adjusted the position of the scale bar.

Author response image 1.

Hematoxylin-eosin staining and immunohistochemistry staining of CGA marker in formalin-fixed paraffin-embedded PCC tissue sections matched to scRNA-seq specimens. Scale bar, 100 μm.

5) What were the clinical presentation and biochemical findings in the five patients?

The information regarding tumor sizes, signs and symptoms, and plasma levels of catecholamine metabolites [3-methoxytyramine (3-MT), metanephrine (MN), and normetanephrine (NMN)] has been added to the revised manuscript as Supplemental Table S3 (Page 11-12).

• Were there any preoperative symptoms of hypertension?

With the exception of P2, preoperative symptoms of hypertension were observed in all PCC patients. The information has been added to the revised manuscript as Supplemental Table S3 (Page 11-12).

• What was the size and catecholamine secretion phenotype of each tumor? What was the relationship between these data and the scRNA-seq results?

The secretion phenotype showed that the kinase-type PCC patient (P4) exhibited higher plasma levels of catecholamine metabolites (3-methoxytyramine and normetanephrine) compared to metabolism-type PCC patients (P1-P3, and P5). This observation aligns with the elevated expression of phenylethanolamine Nmethyltransferase (PNMT), an enzyme involved in the biosynthesis of catecholamine and linked to hypertension, in P4, as identified in the scRNA-seq data (Figure 4B and 4D) (Kennedy et al, 1993; Konosu-Fukaya et al, 2018; Nguyen et al, 2015). Meanwhile, we have not observed the correlation between tumor sizes and molecular classification. We have now included tumor sizes and laboratory test results of 5 PCC patients in the revised manuscript as Supplemental Table S3 (Page 11-12), and the relevant points have been discussed in the revision (Page 20).

6) Please revise Figure 1A, the meaning shown in the figure appears to dissociate the tissues of the patient's normal adrenal glands, which can be misleading.

We appreciate the reviewer for raising this concern. The schematic in Figure 1A has been revised accordingly.

Author response image 2.

(1A) Schematic of the experimental pipeline. 11 tumor specimens and 5 adjacent normal adrenal medullary specimens were isolated from 5 PCC patients, dissociated into single-cell suspensions, and analyzed using 10x Genomics Chromium droplet scRNA-seq.

• Please revise the figure note for Figure 1B, where the symbol (B) appears twice.

As suggested, we have revised the figure legends for Figure 1B and 1C (Page 42).

7) Please indicate in the figure legends and text what exactly is meant by "adjacent specimens"? medulla? cortex? normal tissue? I believe the authors mean adjacent normal adrenal medullary tissue, please check the article.

As suggested, we have revised the term “adjacent specimens” to “adjacent normal adrenal medullary tissues” throughout the revised manuscript.

8) Please review the pathologic diagnostic criteria of this study in light of the 2022 WHO/IARC guidelines for pathologic diagnosis: "For the pathological diagnosis, the inclusion criteria were neuroendocrine neoplasm originating from the adrenal medulla and retroperitoneal origin, i.e. pheochromocytoma and paraganglioma, with consistent morphologic and immunohistochemical confirmation in relevant cases and positivity for chromogranin A and synaptophysin. The exclusion criteria were adrenocortical neoplasm and metastatic tumors." It is not rigorous enough to diagnose a tumor as PCC based on positive CgA immunohistochemical staining results alone.

We have revised the statements about pathologic diagnostic criteria in accordance with the suggestion and have cited the reference (Page 6).

We would like to express our gratitude to the reviewer for the thorough review and invaluable guidance provided to enhance the quality of our study.

References for Reviewer #2:

Kennedy B, Elayan H, Ziegler MG (1993) Glucocorticoid hypertension and nonadrenal phenylethanolamine N-methyltransferase. Hypertension (Dallas, Tex: 1979) 21: 415419

Konosu-Fukaya S, Omata K, Tezuka Y, Ono Y, Aoyama Y, Satoh F, Fujishima F, Sasano H, Nakamura Y (2018) Catecholamine-Synthesizing Enzymes in Pheochromocytoma and Extraadrenal Paraganglioma. Endocrine pathology 29: 302309

Nguyen P, Khurana S, Peltsch H, Grandbois J, Eibl J, Crispo J, Ansell D, Tai TC (2015) Prenatal glucocorticoid exposure programs adrenal PNMT expression and adult hypertension. The Journal of endocrinology 227: 117-127

Reviewer #3 (Recommendations For The Authors):

I have several concerns and suggestions, which if addressed would improve the manuscript.

1) The statements of “plasmas” in the manuscript and figures are confusing, which should be revised as “plasma cells”.

As suggested, we have revised the terminology from “plasmas” to “plasma cells” throughout the revised manuscript and figures.

2) The marker genes used for defining plasma cells (IGHG1 and IGLC2) showed low expressing percentage in Figure 1D. Please consider providing other genes as the marker of plasma cells.

As suggested, we performed additional analysis to pinpoint marker genes for accurate definition of plasma cells. Applying stricter statistical criteria (cut-off pvalue < 0.05, log2 fold change ≥ 1.5, and expressing percentage ≥ 0.6), we identified XBP1 (a transcription factor playing key roles in the final stages of plasma cell development) and IGKC (a type of light-chain immunoglobulins) (Todd et al, 2009; Poulsen et al, 2002) as top significant differentially expressed genes (DEGs) suitable for defining plasma cells. These data are now presented as Figure 1D in the revised manuscript (Page 7).

Author response image 3.

(1D) Dot plot of representative marker genes for each cell type. The color scale represents the average marker gene expression level; dot size represents the percentage of cells expressing a given marker gene.

3) The statement “Our clustering and cell type annotation analysis identified diverse adrenal cells, stromal cells, and immune cells within the PCC microenvironment” seems not be exhibited in Figure 1, so the clustering result of adrenal cells, stromal cells, and immune cells need to be added.

As suggested, we performed clustering analysis for adrenal cells, stromal cells, and immune cells (including lymphocytes and myeloid cells), and visualized by the Uniform Manifold Approximation and Projection (UMAP) plot. These data have been added to the revised manuscript as Supplemental Figure S3 (Page 8).

Author response image 4.

Integration Analysis across 5 PCC Patients Revealing the Cell Type Composition of the PCC Microenvironment. UMAP plot depicting the distribution of adrenal cells, stromal cells, and immune cells (including lymphocytes and myeloid cells) within the PCC microenvironment.

4) Given the classification of “metabolism-type PCCs” and “kinase-type PCCs” have not been presented in Figure 2D, the statement “Combined with our findings of a higher proportion of neutrophils and monocyts/macrophages in metabolism-type as compared with kinase-type” in Result 6 should be supported by using additional data.

As suggested, we performed additional analysis to evaluate the proportion of neutrophils and monocytes/macrophages in metabolism-type and kinasetype PCC patients. These data have been added to the revised manuscript as Supplemental Figure S4 (Page 14).

Author response image 5.

The frequency distribution of cell types within the microenvironment of metabolism-type and kinase-type PCC patients.

5) What makes the difference of scRNA-seq analysis and multispectral immunofluorescent staining in judging the immune escape of PCCs? Please provide an explanation.

We appreciate the reviewer's concern. scRNA-seq lacks spatial details, and multispectral immunofluorescent staining is constrained in the number of detected proteins. To address this, we employed both methods for analysis. scRNA-seq revealed limited communication between tumor and T cells, with lower HLA-I expression in kinase-type PCCs compared to metabolism-type PCCs. This was supported by multispectral staining using antibodies against CD4+ T cells, CD8+ T cells, M1 macrophages, or M2 macrophages markers, indicating sparse immune cell infiltration around tumor cells, mainly in the stroma (Figure 7A and 7B). This dual approach strengthens our understanding of immune escape in both PCC types. The explanation has been added to the revised manuscript (Page 21).

6) Figure 7G missed the scale bar for the staining results of marker proteins. Please add the scale bar into the figure.

As suggested, we have added to the scale bar accordingly.

7) In the method part of the manuscript, the authors should describe the minimum and maximum number used for quality control of the number of genes and the percentage of mitochondrial genes.

For quality control, we established a minimum threshold of no less than 200 genes and a maximum threshold of no more than 5000 genes. Additionally, the quality control process included a maximum threshold of 30% for mitochondrial genes. These specific criteria have been added to the methods section of the revised manuscript (Page 25-26).

We express our gratitude to the reviewer for their supportive recommendations and invaluable guidance on enhancing the rigor of our data.

References for Reviewer #3:

Todd DJ, McHeyzer-Williams LJ, Kowal C, Lee AH, Volpe BT, Diamond B, McHeyzer-Williams MG, Glimcher LH (2009) XBP1 governs late events in plasma cell differentiation and is not required for antigen-specific memory B cell development. The Journal of experimental medicine 206: 2151-2159

Poulsen TS, Silahtaroglu AN, Gisselø CG, Tommerup N, Johnsen HE (2002) Detection of illegitimate rearrangements within the immunoglobulin light chain loci in B cell malignancies using end sequenced probes. Leukemia 16: 2148-2155

Author Response

Reviewer #1 (Public Review)

Midbrain dopamine neurons have attracted attention as a part of the brain's reward system. A different line of research, on the other hand, has shown that these neurons are also involved in higher cognitive functions such as short-term memory. However, these neurons are thought not to encode short-term memory itself because they just exhibit a phasic response in short-term memory tasks, which cannot seem to maintain information during the memory period. To understand the role of dopamine neurons in short-term memory, the present study investigated the electrophysiological property of these neurons in rodents performing a T-maze version of a short-term memory task, in which a visual cue indicated which arm (left or right) of the T-maze was associated with a reward. The animal needed to maintain this information while they were located between the cue presentation position and the selection position of the T-maze. The authors found that the activity of some dopamine neurons changed depending on the information while the animals were located in the memory position. This dopamine neuron modulation was unable to explain the motivation or motor component of the task. The authors concluded that this modulation reflected the information stored as short-term memory.

I was simply surprised by their finding because these dopamine neurons are similar to neurons in the prefrontal cortex that store memory information with sustained activity. Dopamine neurons are an evolutionally conserved structure, which is seen even in insects, whereas the prefrontal cortex is developed mainly in the primate. I feel that their findings are novel and would attract much attention from readers in the field. But the authors need to conduct additional analyses to consolidate their conclusion.

We thank reviewer #1 for the positive assessment and for the valuable and constructive comments on our manuscript.

Reviewer #1 (Recommendations to The Authors)

(1) The authors found the dopamine neuron modulation that reflected the memory information during the delay period. Here the dopamine neuron activity was aligned by the position, not by time, in which the animals needed to maintain the information. Usually, the activity was aligned by time, and many studies found that dopamine neurons exhibited a short duration burst in response to rewards and behaviorally relevant stimuli including visual cues presented in short-term memory tasks. For comparison, I (and probably other readers) want to see the time-aligned dopamine neuron modulation that reflected the memory information. Did the modulation still exist? Did it have a long duration? The authors just showed the time-aligned "population" activity that exhibited no memory-dependent modulation.

We agree that the point raised by the reviewer is important. To address this question, we added a new paragraph to the Methods section titled “Methodological considerations” (in line 793 of the revised manuscript), where we explain the caveats of using time alignment in the T-maze task study. We also created a new sup figure 5 to clarify our argument. As the figure shows, we did not observe major differences in the firing rates when they were arranged by position or time. More importantly, we did not detect brief bursts of activity in response to the visual cue which could reflect an RPE signaling scheme. Our interpretation is that in the T-maze task, DA neurons encode “miniature” RPE signals between successive states in the T-maze, which are hard to detect, especially when neurons receive a continuous sensory input during trials.

(2) Several studies have reported that dopamine neurons at different locations encode distinct signals even within the VTA or SNr. Were the locations of dopamine neurons maintaining the memory information different from those of other dopamine neurons?

We thank the reviewer’s comment. Indeed, there is evidence from recent studies demonstrating that DA neurons form functional and anatomical clusters in the VTA and SN. Following the reviewer’s advice, we report the anatomical structure of memory and non-memory-specific neurons in the revised manuscript. You can read these results in the paragraph “Anatomical organization of trajectory-specific neurons.” in the “Results” section (in line 383 of the revised manuscript) and in the new sup figure 11. We only observed a clear functional-anatomical segregation in GABA neurons, but not in DA neurons. But we should note that the absence of segregation in the DA neurons could be accounted for by the fact that we recorded mostly from the lateral VTA, therefore we do not have any numbers from the medial VTA.

(3a) Did the dopamine neurons maintaining the memory information respond to reward?

We believe that we have already provided the data that can partially answer this question by correlating the firing rate difference between the reward and memory delay sections. This result was described in the “Neuronal activities in delay and reward are unrelated.” paragraph and in Figure 6. Moreover, motivated by the reviewer’s question, we also performed additional analysis, which is included in the revised manuscript. Briefly, we clustered significant responses between the memory delay and reward sections (Category 1: Left-signif, R-signif or No-signif / Category 2: Memory delay or Reward). We discovered that only a very small number of neurons showed the same significant trajectory preference in the memory delay and reward sections (i.e., significant preference for left trials in the memory delay and significant preference for the left reward). In fact, more significant neurons showed a preference for opposite trajectories (i.e. significant preference for left trials in memory delay and a significant preference for right rewards). A description of the new results is included in the “Neuronal activities in delay and reward are unrelated.” paragraph (in line 349 of the revised manuscript) and in the new supplementary Figure 11.

(3b) Did they encode reward prediction error? The relationship between the present data and the conventional theory may be valuable.

We understand that the readers of this study will come up with the question of how memory-specific activities are related to RPE signaling. However, the T-maze task we used in this research was designed for studying working memory and was not adequate to extract information about the RPE signaling of DA neurons.

RPE signaling is mainly studied in Pavlovian conditioning. These are low-dimensional tasks with usually four (4) states (state1: ITI, state2: trial start, state3: stimulus presentation, state4: reward delivery). Evidence of RPE signaling is extracted from the firing activity of states 3 and 4 (which is theorized to be related to the difference in the values for states 3 and 4).

However, in the T-maze task, the number of states is hard to define and practically countless. In these conditions, it has been suggested that numerous small RPEs are signaled while the mice navigate the maze; Thus, they are very difficult to detect. To our knowledge, only Kim et al 2020, Cell, vol183, pg1600, managed to detect the RPE signaling activity of DA neurons while mice were teleported in a virtual corridor.

Another confounding factor in extracting RPE signals in the T-maze task is that the environment is high-dimensional and DA neurons are multitasking. Therefore, it is likely that RPE signaling could be masked by other parallel encoding schemes.

We have added these descriptions in the “Methodological considerations” (in line 793 of the revised manuscript).

(4) Did the dopamine neurons maintaining the memory information (left or right) prefer a contralateral direction like neurons in the motor cortex?

We thank the reviewer for this comment. Indeed, the majority of the memory-specific DA neurons showed a preference for the contralateral direction. We report this result in the legend of the new sup fig 10 (in line 1668 of the revised manuscript).

(5) As shown in Table S2, the proportion of GABA neurons maintaining the memory information (left or right during delay) was much larger than that of dopamine neurons. It seems to be strange because the main output neurons in the VTA are dopaminergic. What is the role of these GABA neurons?

We thank the reviewer for pointing this out. The present study shows that in both populations a sizeable portion of neurons show memory-specific encoding activities. However, the percentage of memory-encoding GABA neurons is more than twice as large as in the DA neurons. Moreover, we show that GABA neurons are functionally and anatomically segregated.

From this evidence, one could raise the hypothesis that the GABA neurons have a primary role and that the activity of DA neurons is a collateral phenomenon, triggered in a sequence of events within the VTA network. To characterize the (1) role and (2) importance of GABA neurons in memory-guided behavior, one should first identify the afferent and efferent projections of these cells in great detail. Unfortunately, we do not provide anatomical evidence.

So far, with the electrophysiological data we have collected (unit and field recordings), we can address an alternative hypothesis. It has been reported earlier (but we have also observed) that the VTA circuit engages in behaviorally related network oscillations which range from 0.4Hz up to 100Hz. Converging evidence from different brain regions, in vitro preparations but also in vivo recordings agree that local networks of inhibitory neurons are crucial for the generation, maintenance, and spectral control of network oscillations. Ongoing analysis, which we hope will lead to a publication, is looking for the behavioral correlates of network oscillations on the T-maze task, as well as the correlation of single-unit firing activity to the field oscillations. We expect to detect a higher field-unit coherence in GABA neurons, which could explain their stronger engagement in memory-specific encoding activity.

The potential role of GABA neurons in network oscillations is discussed in the revised manuscript in a newly added paragraph in line 564.

Reviewer #2 (Public Review)

The authors phototag DA and GABA neurons in the VTA in mice performing a t-maze task, and report choice-specific responses in the delay period of a memory-guided task, more so than in a variant task w/o a memory component. Overall, I found the results convincing. While showing responses that are choice selective in DA neurons is not entirely novel (e.g. Morris et al NN 2006, Parker et al NN 2016), the fact that this feature is stronger when there is a memory requirement is an interesting and novel observation.

I found the plots in 3B misleading because it looks like the main result is the sequential firing of DA neurons during the Tmaze. However, many of the neurons aren't significant by their permutation test. Often people either only plot the neurons that are significant, or plot with cross-validation (ie sort by half of the trials, and plot the other half).

Relatedly, the cross-task comparisons of sequences (Fig, 4,5) are hampered by the fact that they sort in one task, then plot in the other, which will make the sequences look less robust even if they were equally strong. What happens if they swap which task's sequences they use to order the neurons? I do realize they also show statistical comparisons of modulated units across tasks, which is helpful.

We thank reviewer #2 for the valuable and constructive comments on our manuscript. If, as the reviewer commented, the rate differences between left and right trajectories were only the result we want to claim, there may be a way to show only those whose left and right are significant. However, the sequential activity is also one of the points we wanted to display. We did not emphasize this result because it has already been shown by Engelhard et al. 2019. However, after reading the reviewer's comments, we decided to add a few lines in the "Results" (in lines 205 - 215 of the revised manuscript) and "Discussion" (in line 453 of the revised manuscript) describing the sequential activity of the VTA circuit. In those lines, we explained that DA activity is position-specific (resulting in sequential activity) and that a fraction of them also have left-right specificity.

Overall, the introduction was scholarly and did a good job covering a vast literature. But the explanation of t-maze data towards the end of the introduction was confusing. In Line 87, I would not say "in the same task" but "in a similar task" because there are many differences between the tasks in question.

We thank the reviewer for pointing out this mistake. In the revised manuscript, we replaced “in the same task” with “in a similar task” (in line 85 of the revised manuscript).

And not clear what is meant by "by averaging neuronal population activities, none of these computational schemes would have been revealed. " There was trial averaging, at least in Harvey et al. I thought the main result of that paper related to coding schemes was that neural activity was sequential, not persistent. I think it would help the paper to say that clearly.

We admit that this sentence leaves room for misunderstanding. We were mainly referring to DA studies using microdialysis or fiber photometry techniques. We decided to delete this sentence in the revised manuscript.

Also, I'm not aware it was shown that choice selectivity diminishes when the memory demand of the task is removed - please clarify if that is true in both referenced papers.

The reviewer’s remark is correct. None of these reports show explicitly that memory-specific activities are diminished without the memory component. Therefore, we deleted this sentence in the revised manuscript.

If so, an interpretation of this present data could be found in Lee et al biorxiv 2022, which presents a computational model that implies that the heterogeneity in the VTA DA system is a reflection of the heterogeneity found in upstream regions (the state representation), based on the idea that different subsets of DA neurons calculate prediction errors with respect to different subsets of the state representation.

We thank the reviewer for sharing this interpretation. We agree that this theory would support our results. In the revised manuscript we briefly discuss the Lee et al. report (in line 460 of the revised manuscript).

I am surprised only 28% of DA neurons responded to the reward - the reward is not completely certain in this task. This seems lower than other papers in mice (even Pavlovian conditioning, when the reward is entirely certain). It would be helpful if the authors comment on how this number compares to other papers.

In Pavlovian conditioning, neuronal responses to rewards are compared to a relatively quiet period of firing activity (usually the inter-trial interval epoch). As the reviewer pointed out, in the present study, the number of DA neurons responding to reward is smaller compared to the earlier studies. We hypothesize that this is due to our comparison method. We compared the post-reward response to an epoch when the animal was running along the side arms and the majority of neurons were highly active, instead of comparing it to a quiescent baseline epoch.

Reviewer #2 (Recommendations to The Authors)

Can you clarify what disparity you are referring to here? "Disparities between this 438 and our study in the proportions of modulated neurons could be attributed to the 439 different recording techniques applied as well as the maze regions of interest; for 440 example, Engelhard et al. analyzed neuronal firing activities in the visual-cue period 441 (Engelhard et al., 2019), whereas we focused on memory delay.". Is it the fact that Engelhard et al did not report choice-selective activity? They did report cue-side-selective activity, with some neurons responsive to cues on one side, and other neurons responsive to cues on the other side. Because there are more cues on the left when the mouse turns left, these neurons do indeed have choice-selective responses.

We thank the reviewer for this comment. We agree that we need to clarify further our argument. As the reviewer pointed out, Engelhard et al identified choice-specific DA neurons. However, they reported the encoding properties of DA neurons only in the visual-cue period and the reward period. Remarkably, although the task has a memory delay, they did not report the neuronal firing activities for this delay period. Instead, in the present study we dedicated most of our analysis to characterizing the firing properties of VTA neurons in the delay period.

Also, in response to your comment, we edited the paragraph where we describe the disparities between our study and Engelhard et al (in line 466 in the revised manuscript).

I don't think this sentence of intro is needed since it doesn't really contain new info: "Therefore, we looked for hints 116 of memory-related encoding activities in single DA and GABA neurons by 117 characterizing their firing preference for opposite behavioral choices.".

We agree with the reviewer. Therefore, we deleted this sentence in the revised manuscript.

I didn't understand this line of discussion: "Our evidence does not question the validity of this computational model, since we do not provide evidence of how the selective preference for one response over the other translates into the release site.".

The gating theory is based on experimental evidence of neuronal firing activities of DA neurons but also takes into consideration (to a lesser degree) the pre- and post-synaptic processes at the DA release sites (inverted U-shape of D1R activity). We thought that the reader may come to the conclusion that we question the validity of the gating theory. But this is not our intention, especially when we do not provide important evidence such as (1) the projection sites of DA and GABA neurons and (2) the sequence of events that take place at the synaptic triads following the DA and GABA release.

After reading your comment we came to the conclusion that this sentence should be omitted because it is not within the scope of this study to question the validity of the gating theory. Instead, we dedicated a few lines of text to explaining which components of the gating theory (“update”, “maintenance & manipulation” and “motor preparation”) could be attributed to the trajectory-specific activities in the memory delay of the T-maze task. (section “Activities of midbrain DA neurons in short-term memory” in line 417 of the revised manuscript).

In 1B, please illustrate when the light pulses are on & off?

Following the reviewer’s instruction, we added colored bars on top of the raster plots in Figure 1B, indicating the light induction conditions.

In legend for 6C, please clarify it's a correlation between the difference in R and L choice activity across the epochs (if my understanding is correct).

The reviewer’s understanding is correct. We took this advice into consideration to further clarify the methods of analysis that led to the plot in Figure 6C (in line 1246 in the revised manuscript).

Author Response

We thank you for the time you took to review our work and for your feedback!

The major changes to the manuscript are:

1. We have extended the range of locomotion velocity over which we compare its dependence with cholinergic activity in Figures 2E and S2H.

2. We have quantified the contributions of cholinergic stimulation on multiplicative and additive gains on visual responses (Figure S7).

3. We have provided single cell examples for the change in latency to visual response (Figure S12).

4. We have added an analysis to compare layer 2/3 and layer 5 locomotion onset responses as a function of visuomotor condition (Figure S8).

A detailed point-by-point response to all reviewer concerns is provided below.  

Reviewer #1 (Public Review):

The paper submitted by Yogesh and Keller explores the role of cholinergic input from the basal forebrain (BF) in the mouse primary visual cortex (V1). The study aims to understand the signals conveyed by BF cholinergic axons in the visual cortex, their impact on neurons in different cortical layers, and their computational significance in cortical visual processing. The authors employed two-photon calcium imaging to directly monitor cholinergic input from BF axons expressing GCaMP6 in mice running through a virtual corridor, revealing a strong correlation between BF axonal activity and locomotion. This persistent activation during locomotion suggests that BF input provides a binary locomotion state signal. To elucidate the impact of cholinergic input on cortical activity, the authors conducted optogenetic and chemogenetic manipulations, with a specific focus on L2/3 and L5 neurons. They found that cholinergic input modulates the responses of L5 neurons to visual stimuli and visuomotor mismatch, while not significantly affecting L2/3 neurons. Moreover, the study demonstrates that BF cholinergic input leads to decorrelation in the activity patterns of L2/3 and L5 neurons.

This topic has garnered significant attention in the field, drawing the interest of many researchers actively investigating the role of BF cholinergic input in cortical activity and sensory processing. The experiments and analyses were thoughtfully designed and conducted with rigorous standards, leading to convincing results which align well with findings in previous studies. In other words, some of the main findings, such as the correlation between cholinergic input and locomotor activity and the effects of cholinergic input on V1 cortical activity, have been previously demonstrated by other labs (Goard and Dan, 2009; Pinto et al., 2013; Reimer et al., 2016). However, the study by Yogesh and Keller stands out by combining cutting-edge calcium imaging and optogenetics to provide compelling evidence of layerspecific differences in the impact of cholinergic input on neuronal responses to bottom-up (visual stimuli) and top-down inputs (visuomotor mismatch).

We thank the reviewer for their feedback.

Reviewer #2 (Public Review):

The manuscript investigates the function of basal forebrain cholinergic axons in mouse primary visual cortex (V1) during locomotion using two-photon calcium imaging in head-fixed mice. Cholinergic modulation has previously been proposed to mediate the effects of locomotion on V1 responses. The manuscript concludes that the activity of basal forebrain cholinergic axons in visual cortex provides a signal which is more correlated with binary locomotion state than locomotion velocity of the animal. Cholinergic axons did not seem to respond to grating stimuli or visuomotor prediction error. Optogenetic stimulation of these axons increased the amplitude of responses to visual stimuli and decreased the response latency of layer 5 excitatory neurons, but not layer 2/3 neurons. Moreover, optogenetic or chemogenetic stimulation of cholinergic inputs reduced pairwise correlation of neuronal responses. These results provide insight into the role of cholinergic modulation to visual cortex and demonstrate that it affects different layers of visual cortex in a distinct manner. The experiments are well executed and the data appear to be of high quality. However, further analyses are required to fully support several of the study's conclusions.

We thank the reviewer for their feedback.

1) In experiments analysing the activity of V1 neurons, GCaMP6f was expressed using a ubiquitous Ef1a promoter, which is active in all neuronal cell types as well as potentially non-neuronal cells. The manuscript specifically refers to responses of excitatory neurons but it is unclear how excitatory neuron somata were identified and distinguished from that of inhibitory neurons or other cell types.

This might be a misunderstanding. The Ef1α promoter has been reported to drive highly specific expression in neurons (Tsuchiya et al., 2002) with 99.7% of labeled cells in layer 2/3 of rat cortex being NeuN+ (a neuronal marker), with only 0.3% of labeled cells being GFAP+ (a glial marker) (Yaguchi et al., 2013). This bias was even stronger in layer 5 with 100% of labeled cells being NeuN+ and none GFAP+ (Yaguchi et al., 2013). The Ef1α promoter in an AAV vector, as we use it here, also biases expression to excitatory neurons. In layer 2/3 of mouse visual cortex, we have found that 96.8% ± 0.7% of labeled neurons are excitatory three weeks after viral injection (Attinger et al., 2017). Similar results have also been found in rats (Yaguchi et al., 2013), where on expressing GFP under Ef1a promoter delivered using Lenti virus, 95.2% of labeled neurons in layer 2/3 were excitatory and 94.1% in layer 5 were excitatory. These numbers are comparable to the ones obtained with promoters commonly used to target expression to excitatory neurons. To do this, typically two variants of promoters based on the transcription start region of CaMKIIα gene have been used. The first, the CaMKIIα-0.4 promoter, results in 95% excitatory specificity (Scheyltjens et al., 2015). The second, the CaMKIIα-1.3 promoter, results in only 82% excitatory specificity (Scheyltjens et al., 2015), and is thus not far from chance. We have clarified this in the manuscript. Nevertheless, we have removed the qualifier “excitatory” when talking about neurons in most instances, throughout the manuscript.

2) The manuscript concludes that cholinergic axons convey a binary locomotion signal and are not tuned to running speed. The average running velocity of mice in this study is very slow - slower than 15 cm/s in the example trace in Figure 1D and speeds <6 cm/s were quantified in Figure 2E. However, mice can run at much faster speeds both under head-fixed and freely moving conditions (see e.g. Jordan and Keller, 2020, where example running speeds are ~35 cm/s). Given that the data in the present manuscript cover such a narrow range of running speeds, it is not possible to determine whether cholinergic axons are tuned to running speed or convey a binary locomotion signal.

Our previous analysis window of 0-6.25 cm/s covered approximately 80% of all data. We have increased the analysis window to 0-35 cm/s that now covers more than 99% of the data (see below). Also, note that very high running speeds are probably overrepresented in the Jordan and Keller 2020 paper as mice had to be trained to run reliably before all experiments given the relatively short holding times of the intracellular recordings. The running speeds in our current dataset are comparable to other datasets we have acquired in similar experiments.

Figure 2E has now been updated to reflect the larger range of data. Please note, as the number of mice that contribute to the data now differs as a function of velocity (some mice run faster than others), we have now switched to a variant of the plot based on hierarchical bootstrap sampling (see Methods). This does not overtly change the appearance of the plot. See Author response image 1 for a comparison of the original plot, the extended range without bootstrap sampling, and the extended range with bootstrap sampling currently used in the paper.

Author response image 1.

Average activity of cholinergic axons as a function of locomotion velocity. (A) As in the previous version of the manuscript. (B) As in A, but with the extended velocity range. (C) As in B, but using hierarchical bootstrap sampling to estimate median (red dots) and 95% confidence interval (shading) for each velocity bin.

3) The analyses in Figure 4 only consider the average response to all grating orientations and directions. Without further analysing responses to individual grating directions it is unclear how stimulation of cholinergic inputs affects visual responses. Previous work (e.g. Datarlat and Stryker, 2017) has shown that locomotion can have both additive and multiplicative effects and it would be valuable to determine the type of modulation provided by cholinergic stimulation.

We thank the reviewer for this suggestion. To address this, we quantified how cholinergic stimulation influenced the orientation tuning of V1 neurons. The stimuli we used were full field sinusoidal drifting gratings of 4 different orientations (2 directions each). For each neuron, we identified the preferred orientation and plotted responses relative to this preferred orientation as a function of whether the mouse was running, or we were stimulating cholinergic axons. Consistent with previous work, we found a mixture of a multiplicative and an additive components during running. With cholinergic axon stimulation, the multiplicative effect was stronger than the additive effect. This is now quantified in Figure S7.

4) The difference between the effects of locomotion and optogenetic stimulation of cholinergic axons in Figure 5 may be confounded by differences in the visual stimulus. These experiments are carried out under open-loop conditions, where mice may adapt their locomotion based on the speed of the visual stimulus. Consequently, locomotion onsets are likely to occur during periods of higher visual flow. Since optogenetic stimulation is presented randomly, it is likely to occur during periods of lower visual flow speed. Consequently, the difference between the effect of locomotion and optogenetic stimulation may be explained by differences in visual flow speed and it is important to exclude this possibility.

We find that in general locomotion is unaffected by visual flow in open loop conditions in this type of experiment (in this particular dataset, there was a small negative correlation between locomotion and visual flow in the open loop condition, Author response image 2).

Author response image 2.

Correlation between visual flow and locomotion in open loop conditions. Average correlation of locomotion velocity and visual flow speed in open loop for all mice in Figure 5. Each dot is an imaging site. In the open loop, the correlation between locomotion and visual flow speed is close to zero, but significantly negative in this dataset.

However, to directly address the concern that our results are influenced by visual flow, we can restrict our analysis only to locomotion onsets that occurred in absence of visual flow (Author response image 3A and R3B). These responses are not substantially different from those when including all data (Figures 5A and 5B). Thus, the difference between the effect of locomotion and optogenetic stimulation cannot be explained by differences in visual flow speed.

Author response image 3.

Open loop locomotion onset responses without visual flow. (A) Average calcium response of layer 2/3 neurons in visual cortex to locomotion onset in open loop in the absence of visual flow. Shading indicates SEM. (B) As in A, but for layer 5 neurons.

5) It is unclear why chemogenetic manipulations of cholinergic inputs had no effect on pairwise correlations of L2/3 neuronal responses while optogenetic stimulation did.

This is correct – we do not know why that is the case and can only speculate. There are at least two possible explanations for this difference:

1) Local vs. systemic. The optogenetic manipulation is relatively local, while the chemogenetic manipulation is systemic. It is not clear how cholinergic release in other brain regions influences the correlation structure in visual cortex. It is conceivable that a cortex-wide change in cholinergic release results in a categorically different state with a specific correlation structure in layer 2/3 neurons different from the one induced by the more local optogenetic manipulation.

2) Layer-specificity of activation. Cholinergic projections to visual cortex arrive both in superficial and deep layers. We activate the axons in visual cortex optogenetically by illuminating the cortical surface. Thus, in our optogenetic experiments, we are primarily activating the axons arriving superficially, while in the chemogenetic experiment, we are likely influencing superficial and deep axons similarly. Thus, we might expect a bias in the optogenetic activation to influencing superficial layers more strongly than the chemogenetic activation does.

6) The effects of locomotion and optogenetic stimulation on the latency of L5 responses in Figure 7 are very large - ~100 ms. Indeed, typical latencies in mouse V1 measured using electrophysiology are themselves shorter than 100 ms (see e.g. Durand et al., 2016). Visual response latencies in stationary conditions or without optogenetic stimulation appear surprisingly long - much longer than reported in previous studies even under anaesthesia. Such large and surprising results require careful analysis to ensure they are not confounded by artefacts. However, as in Figure 4, this analysis is based only on average responses across all gratings and no individual examples are shown.

This is correct and we speculate this is the consequence of a combination of different reasons.

1) Calcium imaging is inherently slower than electrophysiological recordings. While measuring spiking responses using electrophysiology, response latencies of on the order of 100 ms have indeed been reported, as the reviewer points out. Using calcium imaging these latencies are typically 4 times longer (Kuznetsova et al., 2021). This is likely a combination of a) calcium signals that are slower than electrical changes, b) delays in the calcium sensor itself, and c) temporal sampling used for imaging that is about 3 orders of magnitude slower than what typically used for electrophysiology.

2) Different neurons included in analysis. The calcium imaging likely has very different biases than electrophysiological recordings. Historically, the fraction of visually responsive neurons in visual cortex based on extracellular electrophysiological recordings has been systematically overestimated (Olshausen and Field, 2005). One key contributor to this is the fact that recordings are biased to visually responsive neurons. The criteria for inclusion of “responsive neurons” strongly influences the “average” response latency. In addition, calcium imaging has biases that relate to the vertical position of the somata in cortex. Both layer 2/3 and layer 5 recordings are likely biased to superficial layer 2/3 and superficial layer 5 neurons. Conversely, electrical recordings are likely biased to layer 4 and layer 5 neurons. Thus, comparisons at this level of resolution between data obtained with these two methods are difficult to make.

We have added example neurons as Figure S12, as suggested.  

Reviewer #1 (Recommendations For The Authors):

While the study showcases valuable insights, I have a couple of concerns regarding the novelty of their research and the interpretation of results. By addressing these concerns, the authors can clarify the positioning of their research and strengthen the significance of their findings.

(Major comments)

1) Page 1, Line 21: The authors claim, "Our results suggest that acetylcholine augments the responsiveness of layer 5 neurons to inputs from outside of the local network, enabling faster switching between internal representations during locomotion." However, it is not clear which specific data or results support the claim of "switching between internal representations." Overall, their study primarily presents responses averaged across all neurons imaged, lacking a detailed exploration of individual neuron response patterns. Population analysis, such as PCA and decoding, can be used to assess the encoding of each stimulus by V1 neurons - "internal representation."<br /> To strengthen their claim regarding "switching between internal representations," the authors could consider an experiment measuring the speed at which the population activity pattern A transitions to the population activity pattern B when the visual stimulus switches from A to B. Such experiments would significantly enhance the impact of their study, providing a clearer understanding of how BF cholinergic input influences the dynamic representation of stimuli during locomotion.

We thank the reviewer for bringing this up. That acetylcholine enables a faster switching between internal representations in layer 5 is a speculation. We have attempted to make this clearer in the discussion. Our speculation is based on the finding that the population response in layer 5 to sensory input is faster under high levels of acetylcholine (Figures 4D and 7B). In line with the reviewer’s intuition, the neuronal response to a change in visual stimulus, in our experiment from a uniform grey visual stimulus to a sinusoidal grating stimulus, is indeed faster. Based on evidence in favor of layer 5 encoding internal representation (Heindorf and Keller, 2023; Keller and Mrsic-Flogel, 2018; Suzuki and Larkum, 2020), we interpret the decrease in latency of the population response as a faster change in internal representation. We are not sure a decoding analysis would add much to this, given that a trivial decoder simply based on mean population response would already find a faster transition. We have expanded on our explanation of these points in the manuscript.

2) Page 4, Line 103: "..., a direct measurement of the activity of cholinergic projection from basal forebrain to the visual cortex during locomotion has not been made." This statement is incorrect. An earlier study by Reimer et al. indeed imaged cholinergic axons in the visual cortex of mice running on a wheel. They found that "After walking onset, ... ACh activation, and a large pupil diameter, were sustained throughout the walking period in both cortical areas V1 and A1." Their findings are very similar to the results presented by Yogesh and Keller - that is, BF cholinergic axons exhibited locomotion statedependent activity. The authors should clarify the positioning of this study relative to previous studies.

Reimer, J., McGinley, M., Liu, Y. et al. Pupil fluctuations track rapid changes in adrenergic and cholinergic activity in cortex. Nat Commun 7, 13289 (2016). https://doi.org/10.1038/ncomms13289

We have clarified this as suggested. However, we disagree slightly with the reviewer here. The key question is whether the cholinergic axons imaged originate in basal forebrain. While Reimer et al. 2016 did set out to do this, we believe a number of methodological considerations prevent this conclusion:

1) In their analysis, Reimer et al. 2016 combine data from mice with cholinergic axons labeled with either viral injection to basal forebrain or germline cross of ChAT-cre mice with reporter line. Unfortunately, it is unclear what the exact number of mice labeled with either strategy was. Based on the information in the paper, we can conclude that of the 6 mice used for experiments between 2 and 5 were germline cross. The problem with germline labeling of ChAT positive neurons is that when using a cross, VIP-ChAT+ neurons in cortex are also labeled. Based on the fact that Reimer et al. 2016 find an anticipatory increase in activity on locomotion onset, that is also seen by Larsen et al. 2018 (they use a germline cross strategy), an effect we do not see in our data, we speculate that a significant part of the signals reported in the Reimer et al. 2016 paper are from local VIP-ChAT+ neurons.

2) In their analysis, Reimer et al. 2016 also combine all imaging data obtained from both primary auditory cortex and primary visual cortex. Given the heterogeneity in the basal forebrain cholinergic neuronal population and their projection selectivity, to better understand these signals, it’s important to acquire the signals from cholinergic axons selectively in specific cortical regions, which we do in visual cortex. Based on the information provided in their paper, we were unfortunately not able to discern the injection location for their viral labeling strategy. Given the topographic selectivity in projection from basal forebrain, this could give hints as to the relative contribution of cholinergic projections to A1 vs V1 in their data. The injection coordinates given in the methods of the Reimer paper, of 4 mm lateral and 0.5 mm posterior to bregma to target basal forebrain, are likely wrong (they fall outside the head of the mouse).

Given the heterogeneity in the basal forebrain cholinergic neuronal population and their projection selectivity, to better understand these signals, it’s important to acquire the signals from cholinergic axons both selectively in a cortical region, as we do in visual cortex, and purely originating from basal forebrain. Collins et al. 2023 inject more laterally and thus characterize cholinergic input to S1 and A1, while Lohani et al. 2022 use GRAB sensors which complement our findings. Please note, we don’t think there is any substantial disagreement in the results of previous studies and ours, with very few exceptions, like the anticipatory increase in cholinergic activity that precedes locomotion onset in the Reimer et al. 2016 data, but not in ours. This is a rather critical point in the context of the literature of motor-related neuronal activity in mouse V1. Based on early work on the topic, it is frequently assumed that motor-related activity in V1 is driven by a cholinergic input. This is very likely incorrect given our results, hence we feel it is important to highlight this methodological caveat of earlier work.

3) Fig. 4H: The authors found that L5 neurons exhibit positive responses at the onset of locomotion in a closed-loop configuration. Moreover, these responses are further enhanced by photostimulation of BF axons.

In a previous study from the same authors' group (Heindorf and Keller, 2023), they reported 'negative' responses in L5a IT neurons during closed-loop locomotion. This raises a question about the potential influence of different L5 neuron types on the observed results between the two studies. Do the author think that the involvement of the other neuronal type in L5, the PT neurons, might explain the positive responses seen in the present study? Discussing this point in the paper would provide valuable insights into the underlying mechanisms.

Yes, we do think the positive response observed on locomotion onset in closed loop is due to non-Tlx3+ neurons. Given that Tlx3-cre only labels a subset of inter-telencephalic (IT) neurons (Gerfen et al., 2013; Heindorf and Keller, 2023), it’s not clear whether the positive response is explained by the pyramidal tract (PT) neurons, or the non-Tlx3+ IT neurons. Dissecting the response profiles of different subsets of layer 5 neurons is an active area of research in the lab and we hope to be able to answer these points more comprehensively in future publications. We have expanded on this in the discussion as suggested.

Furthermore, it would be valuable to investigate whether the effects of photostimulation of BF axons vary depending on neuronal responsiveness. This could help elucidate how neurons with positive responses, potentially putative PT neurons, differ from neurons with negative responses, putative IT neurons, in their response to BF axon photostimulation during locomotion.

We have attempted an analysis of the form suggested. In short, we found no relationship between a neuron’s response to optogenetic stimulation of ChAT axons and its response to locomotion onset, or its mean activity. Based on their response to locomotion onset in closed loop, we split layer 5 neurons into three groups, 30% most strongly decreasing (putative Tlx3+), 30% most strongly increasing, and the rest. We did not see a response to optogenetic stimulation of basal forebrain cholinergic axons in any of the three groups (Author response image 4A). We also found no obvious relationship between the mean activity of neurons and their response to optogenetic stimulation (Author response image 4B).

Author response image 4.

Neither putative layer 5 cell types nor neuronal responsiveness correlates with the response to optogenetic stimulation of cholinergic axons. (A) Average calcium response of layer 5 neurons split into putative Tlx3 (closed loop locomotion onset suppressed) and non-Tlx3 like (closed loop locomotion onset activated) to optogenetic stimulation of cholinergic axons. (B) Average calcium response of layer 5 neurons to optogenetic stimulation of cholinergic axons as a function of their mean response throughout the experimental session. Left: Each dot is a neuron. Right: Average correlation in the response of layer 5 to optogenetic stimulation and mean activity over all neurons per imaging site. Each dot is an imaging site.

(Minor comments)

1) It is unclear which BF subregion(s) were targeted in this study.

Thanks for pointing this out. We targeted the entire basal forebrain (medial septum, vertical and horizontal limbs of the diagonal band, and nucleus basalis) with our viral injections. All our axonal imaging data comes from visual cortex and given the sensory modality-selectivity of cholinergic projections to cortex, the labeled axons originate from medial septum and the diagonal bands (Kim et al., 2016). We have now added the labels for basal forebrain subregions targeted next to the injection coordinates in the manuscript.

2) Page 43, Line 818: The journal name of the cited paper Collins et al. is missing.

Fixed.

3) In the optogenetic experiments, how long is the inter-trial interval? Simulation of BF is known to have long-lasting effects on cortical activity and plasticity. It is, therefore, important to have a sufficient interval between trials.

The median inter-trial interval for different stimulation events are as follows:

• Optogenetic stimulation only : 15 s

• Optogenetic stimulation + grating : 12 s

• Optogenetic stimulation + mismatch: 35 s

• Optogenetic stimulation + locomotion onset: 45 s

We have added this information to the methods in the manuscript.

Assuming locomotion is the primary driver of acetylcholine release (as we argue in Figures 1 and 2), the frequency of stimulation roughly corresponds to the frequency of acetylcholine release experienced endogenously. It is of course possible that being awake and mobile puts the entire system in a longlasting acetylcholine driven state different from what would be observed during long-term quite wakefulness or during sleep. But the main focus of the optogenetic stimulation experiments we performed was to investigate the consequences of the rapid acetylcholine release driven by locomotion.

4) Page 11, Line 313: "..., we cannot exclude the possibility of a systemic contribution to the effects we observe through shared projections between different cortical and subcortical target." This possibility can be tested by examining the effect of optogenetic stimulation of cholinergic axons on locomotor activity, as they did for the chemogenetic experiments (Fig. S7). If the optogenetic manipulation changes locomotor activity, it is likely that this manipulation has some impact on subcortical activity and systemic contribution to the changes in cortical responses observed.

Based on the reviewer suggestion we tested this and found no change in the locomotor activity of the mice on optogenetic stimulation of cholinergic axons locally in visual cortex (we have added this as Figure S5 to the manuscript). Please note however, we can of course not exclude a systemic contribution based on this.

5) Fig. 4 and 5: In a closed-loop configuration, L2/3 neurons exhibit a transient increase in response at the onset of locomotion, while in an open-loop configuration, their response is more prolonged. On the other hand, L5 neurons show a sustained response in both configurations. Do the authors have any speculation on this difference?

This is correct. Locomotion onset responses in layer 2/3 are strongly modulated by whether the locomotion onset occurs in closed loop or open loop configurations (Widmer et al., 2022). This difference is absent in our layer 5 data here. We suspect this is a function of a differential within-layer cell type bias in the different recordings. In the layer 2/3 recordings we are likely biased strongly towards superficial L2/3 neurons that tend to be negative prediction error neurons (top-down excited and bottom-up inhibited), see e.g. (O’Toole et al., 2023). A reduction of locomotion onset responses in closed loop is what one would expect for negative prediction error neurons. While layer 5 neurons exhibit mismatch responses, they do not exhibit opposing top-down and bottom-up input that would result in such a suppression (Jordan and Keller, 2020).

We can illustrate this by splitting all layer 2/3 neurons based on their response to gratings and to visuomotor mismatch into a positive prediction error (PE) type (top 30% positive grating response), a negative prediction error type (top 30% positive visuomotor mismatch response), and the rest (remaining neurons and neurons responsive to both grating and visuomotor mismatch). Plotting the response of these neurons to locomotion onset in closed loop and open loop, we find that negative PE neurons have a transient response to locomotion onset in closed loop while positive PE neurons have a sustained increase in response in closed loop. In open loop the response of the two populations is indistinguishable. Splitting the layer 5 neurons using the same criteria, we don’t find a striking difference between closed and open loop between the two groups of neurons. We have added this as Figure S8.

Reviewer #2 (Recommendations For The Authors):

Major concerns:

1) As a ubiquitous promoter was used to drive GCaMP expression, please explain how excitatory neurons were identified.

2) As the data cover a very small range of running speeds, it is important to confirm that the binary locomotion signal model still applies when mice run at higher speeds - either by selecting recordings where mice have a wider range of running speeds or conducting additional experiments. In addition, please show the running speed tuning of individual axons.

3) Please provide a more detailed analysis of the effects of locomotion and cholinergic modulation on visual responses. How does cholinergic modulation affect orientation and direction tuning? Are the effects multiplicative or additive? How does this compare to the effects of locomotion on single neurons?

4) To ensure that the analyses in Figure 5 are not confounded by differences in the visual stimulus, please include average visual flow speed traces for each condition.

5) Please clarify why chemogenetic manipulations of cholinergic inputs had no effect on pairwise correlations in L2/3.

6) The latency effect is quite an extraordinary claim and requires careful analysis. Please provide examples of single neurons illustrating the latency effect - including responses across individual grating orientations/directions. One possible confound is that grating presentation could itself trigger locomotion or other movements. In the stationary / noOpto conditions, the grating response might not be apparent in the average trace until the animal begins to move. Thus the large latency in the stationary / noOpto conditions may reflect movement-related rather than visual responses.

Please see our responses to these points in the public review part above.

There are some minor points where text and figures could be improved:

1) When discussing the decorrelation of neuronal responses by cholinergic axon activation, it is important to make it clear that Figure 6D quantifies the responses of layer 5 apical dendrites rather than neurons.

We have added this information to the results section.

2) In Figure S7, please clarify why velocity is in arbitrary units.

This was an oversight and has been fixed.

3) Please clarify how locomotion and stational trials are selected in Figure 4.

We thank the reviewers for pointing this out. Trials were classified as occurring during locomotion or while mice were stationary as follows. We used a time-window of -0.5 s to +1 s around stimulus onset. If mice exhibited uninterrupted locomotion above a threshold of 0.25 cm/s in this time-window, we considered the stimulus as occurring during locomotion, otherwise it was defined as occurring while the mice were stationary. Note, the same criteria to define locomotion state was used to isolate visuomotor mismatch events, and also during control optogenetic stimulation experiments. We have added this information to the methods.

4) When testing whether cholinergic activation is sufficient to explain locomotion-induced decorrelation in Figure 6G-H, please show pre-CNO and post-CNO delta-correlation, not just their difference.

We can do that, but the results are harder to parse this way. We have added this as Figure S11 to the manuscript. The problem with parsing the figure is that the pre-CNO levels are different in different groups. This is likely a function of mouse-to-mouse variability and makes it harder to identify what the CNO induced changes are. Using the pre-post difference removes the batch influence. Hence, we have left this as the main analysis in Figure 6G and 6H.

Author Response

eLife assessment

The important work by Aballay et al. significantly advances our understanding of how G protein-coupled receptors (GPCRs) regulate immunity and pathogen avoidance. The authors provide convincing evidence for the GPCR NPR-15 to mediate immunity by altering the activity of several key transcription factors. This work will be of broad interest to immunologists.

The authors express their sincere appreciation to Timothy Behrens (Senior Editor), the Reviewing Editor, and the original reviewers for their considerate and favorable assessment of our manuscript.

Reviewer #1 (Public Review):

Summary:

Otarigho et al. presented a convincing study revealing that in C. elegans, the neuropeptide Y receptor GPCR/NPR-15 mediates both molecular and behavioral immune responses to pathogen attack. Previously, three npr genes were found to be involved in worm defense. In this study, the authors screened mutants in the remaining npr genes against P. aeruginosa-mediated killing and found that npr-15 loss-of-function improved worm survival. npr-15 mutants also exhibited enhanced resistance to other pathogenic bacteria but displayed significantly reduced avoidance to S. aureus, independent of aerotaxis, pathogen intake and defecation. The enhanced resistance in npr-15 mutant worms was attributed to upregulation of immune and neuropeptide genes, many of which were controlled by the transcription factors ELT-2 and HLH-30. The authors found that NPR-15 regulates avoidance behavior via the TRPM gene, GON-2, which has a known role in modulating avoidance behavior through the intestine. The authors further showed that both NPR-15-dependent immune and behavioral responses to pathogen attack were mediated by the NPR-15-expressing neurons ASJ. Overall, the authors discovered that the NPR-15/ASJ neural circuit may regulate distinct defense mechanisms against pathogens under different circumstances. This study provides novel and useful information to researchers in the fields of neuroimmunology and C. elegans research.

The authors are grateful for the thoughtful and insightful comments on our manuscript. Your feedback has been instrumental in refining our work, and we appreciate the time and expertise you have invested in evaluating our study.

Strengths:

1) This study uncovered specific molecules and neuronal cells that regulate both molecular immune defense and behavior defense against pathogen attack and indicate that the same neural circuit may regulate distinct defense mechanisms under different circumstances. This discovery is significant because it not only reveals regulatory mechanisms of different defense strategies but also suggests how C. elegans utilize its limited neural resources to accomplish complex regulatory tasks.

The authors express gratitude to the reviewer for recognizing that the present study revealed specific molecules and neuronal cells involved in regulating both molecular immune defense and behavioral defense against pathogen attacks. Additionally, the acknowledgment that the same neural circuit may oversee distinct defense mechanisms under different circumstances is appreciated.

2) The conclusions in this study are supported by solid evidence, which are often derived from multiple approaches and/or experiments. Multiple pathogenic bacteria were tested to examine the effect of NPR-15 loss-of-function on immunity; the impacts of pharyngeal pumping and defecation on bacterial accumulation were ruled out when evaluating defense; RNA-seq and qPCR were used to measure gene expression; gene inactivation was done in multiple strains to assess gene function.

The authors thank the reviewer for appreciating that this study is supported by solid evidence.

3) Gene differential expression, gene ontology, and pathway analyses were performed to demonstrate that NPR-15 controls immunity by regulating immune pathways.

The authors thank the reviewer for appreciating the Gene differential expression, gene ontology, and pathway analyses performed in the study.

4) Elegant approaches were employed to examine avoidance behavior (partial lawn, full lawn, and lawn occupancy) and the involvement of neurons in regulating immunity and avoidance (the use of a diverse array of mutant strains).

The author thanks the reviewer for appreciating the approaches used in this study.

5) Statistical analyses were appropriate and adequate.

The authors thank the reviewer for appreciating the Statistical analyses used in this study.

Reviewer #2 (Public Review):

Summary:

The authors are studying the behavioral response to pathogen exposure. They and others have previously describe the role that the G-protein coupled receptors in the nervous system plays in detecting pathogens, and initiating behavioral patterns (e.g. avoidance/learned avoidance) that minimize contact. The authors study this problem in C. elegans, which is amenable to genetic and cellular manipulations and allow the authors to define cellular and signaling mechanisms. This paper extends the original idea to now implicate signaling and transcriptional pathways within a particular neuron (ASJ) and the gut in mediating avoidance behaviour.

Strengths:

The work is rigorous and elegant and the data are convincing. The authors make superb use of mutant strains in C. elegans, as well tissue specific gene inactivation and expression and genetic methods of cell ablation. to demonstrate how a gene, NPR15 controls behavioral changes in pathogen infection. The results suggest that ASJ neurons and the gut mediate such effects. I expect the paper will constitute an important contribution to our understanding of how the nervous system coordinates immune and behavioral responses to infection.

The authors sincerely thank the reviewer for the thoughtful and positive review of our manuscript. We greatly appreciate the time and effort you dedicated to evaluating our work, and we are pleased that you find our study to be a rigorous and elegant contribution to the understanding of behavioral responses to pathogen exposure.

Reviewer #1 (Recommendations For The Authors):

The authors have adequately addressed my concerns and questions. I have no more comments or recommendations for the authors.

The authors thank the reviewer for the constructive comments on the manuscript

Reviewer #2 (Recommendations For The Authors):

The authors have adequately addressed my concerns.

The authors express their appreciation to the reviewer for the valuable and constructive comments provided on the manuscript.

Author Response

Reviewer #1 (Public Review):

Summary:

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

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

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

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

Strengths:

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

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

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

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

Weaknesses:

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

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

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

Contribution:

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

Reviewer #2 (Public Review):

Summary:

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

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

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

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

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

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

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

Hemodynamic response functions were studied for two reasons:

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

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

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

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

Details about the model were added.

Strengths:

Use of fMRI and EEG to study SWDs in rats.

Weaknesses:

Several aspects of the Methods and Results are unclear.

Reviewer #3 (Public Review):

Summary:

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

Strengths:

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

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

Weaknesses:

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

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

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

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

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

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

Reviewer #1 (Recommendations For The Authors):

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

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

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

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

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

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

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

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

Some minor issues:

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

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

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

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

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

Definitions for these abbreviations were added.

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

Subscripts were added.

Reviewer #2 (Recommendations For The Authors):

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

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

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

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

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

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

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

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

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

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

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

The following also is not precise:

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

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

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

The particular section was modified to the following:

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

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

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

Author response image 1.

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

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

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

What was the type of food?

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

What were the electrodes?

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

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

Reference added.

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Sentence was clarified:

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

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

Sentence was simplified:

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

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

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

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

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

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

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

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

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

Sentence was corrected as the following:

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

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

Sentence was corrected to the following:

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

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

Corrected as the following:

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

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

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

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

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

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

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

Clarified as:

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

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

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

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

Look comment above.

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

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

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

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

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

Modified as:

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

Results

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

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

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

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

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

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

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

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

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

Table 1 has no statistical comparisons.

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

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

Creation of statistical maps are explained in section 2.5.3.

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

Sentence was modified as the following:

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

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

Creation of statistical maps are explained in section 2.5.3.

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

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

Definition of ROI was clarified:

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

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

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

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

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

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

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

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

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

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

Some parts of the discussion and conclusion sections were modified.

Reviewer #3 (Recommendations For The Authors):

Minor comments:

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

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

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

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

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

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

Units were added.

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

Should state “each fMRI sequence” which was corrected.

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

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

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

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

Author Response

Reviewer #1 (Public Review):

The manuscript entitled 'Safb1 regulates cell fate determination in adult neural stem cells by enhancing Drosha cleavage of NFIB mRNA' by Iffländer et al, represents a solid piece of work addressing a non-canonical function of Drosha on NFIB mRNA processing via a newly identified Drosha partner, Safb1. The authors provide particularly systematic and convincing evidence on the biochemical interactions among the key players in this cascade. However, the significance of these interactions for NSC fate determination is not adequately supported by the data, hence, I have some remarks that would need to be addressed in order to clarify the impact of these events on NSC biology.

1) One of my main concerns is related to the nature of the DG NSCs used in all in vitro assays. The authors refer to their previous work on how these cells are isolated using a Hes5 mouse reporter line. However, both recent scRNAseq data (http://linnarssonlab.org/dentate/ from Hochgerner et al) and the authors' own immunostainings (Fig. 7A), clearly show that Hes5 does not label only adult NSCs in the DG, but also (if not primarily) astrocytes. Considering that the initial cultures could contain a high proportion of mature astrocytes, most of the major conclusions and hypotheses should be reformulated.

We thank the reviewer for their comment. We think that there is a misunderstanding about how the DG neural stem cells were isolated and cultured. In this manuscript we did not use the Hes5::GFP allele to isolate the stem cells. We isolated DG neural stem cells from C57Bl6 mice according to the protocol of Babu et al. (Babu et al. 2007 doi: 10.1371/journal.pone.0000388) and maintained and differentiated these according to our previous manuscripts (Ronaldo et al. 2016). This was not clear in the methods section of the original manuscript and, therefore, we have added the reference Babu et al. In order to address potential contamination with astrocytes, we have added images of the stem cells and their progeny immunostained with astrocytic markers (GFAP and S100b) in undifferentiated and differentiated states. These new data show that these neurogenic cells and their progeny do not express astrocytic markers until differentiation is induced.

2) Along these lines, Safb1 expression is quite widespread in the mouse DG (Fig. 7A) and does not display any specificity towards any type of progenitor cells compared to its expression in DGCs within the GCL. The authors should discuss this and integrate this expression information into their conclusions and interpretations, highlighting all pertinent limitations.

We appreciate and agree with the reviewer’s comment. SAFB1 is indeed broadly expressed by most if not all cells in the hippocampus. We quantified levels of SAFB1 expression across progenitors, astrocytes and neurons in the adult DG and in the SVZ, and show that SAFB1 levels differ across different neural stem cell populations and neural cells. We believe that our data show both in vitro and in vivo that the levels of SAFB1 are critical for determining the function of SAFB1 in regulating neural stem cell fate. We also showed that elevating SAFB1 levels in SVZ-derived neural stem cells suppresses their differentiation into oligodendrocytes, This we have made clearer in the text. However, how cells sense the levels of SAFB1 remains to be shown and it is difficult to speculate on the mechanism.

Author Response

Reviewer #1 (Public Review):

In this analysis derived from the BLADE study, a Phase IV investigation using the LHRH antagonist Degarelix, the authors revealed additional insights into the relationship between FSH and body composition.

The primary strength of the study lies in its prospective nature and the utilization of human subjects.

We thank the reviewer for the positive evaluation.

However, some weaknesses exist in the study.

First, the authors presented results from a simple correlation study without accounting for potential confounding factors in fat metabolism. Particularly, readers may be intrigued to understand how testosterone or estradiol interact with FSH in relation to fat mass.

As for the evaluation of circulating levels of testosterone and estradiol, unfortunately the protocol did not include the dosage for these hormones. The evaluation of testosterone, in particular, would have required mass photometry as the values of testosterone during therapy with degarelix are reduced below the sensitivity of the methods used in clinical practice. Therefore, the correlation/association analysis between testosterone and body composition would not have been reliable and would not have been useful for the study. All patients were considered to have hypogonadism due to the significant decrease in PSA values and the limited testosterone data available.

The inverse relationship between ALBI/FBM was previously documented in a paper by the same group (Palumbo et al, Prostate Cancer Prostatic Dis 2021). In that earlier publication, the authors reported no correlation between FSH and lean mass or ALBI, suggesting the significance of the correlation between FSH and ALBI/FBM arising from changes in fat body mass-a factor somehow not included in the prior paper, not necessarily from sarcopenia.

The referee is correct, as there is no correlation between lean mass and FSH, nor between lean mass variations and FSH variations. The correlation between ALMI/FBM and FSH is mostly due to the effect on fat mass. The text now includes a statement that emphasizes this concept (see Discussion page 8, lines 19-22).

Reviewer #2 (Public Review):

This manuscript reports the results of an ancillary study of a prospective trial assessing the effects of androgen deprivation therapy (ADT) with Dagarelix (a GnRH antagonist) on body composition in patients with prostate cancer. An interesting relationship between FSH levels, that were suppressed by Dagarelix treatment, and body composition parameters (particularly fat body mass) was described after 12 months of therapy. Therefore, the authors conclude that FSH could be a promising marker to monitor the risk of sarcopenic obesity and cardiovascular complications in prostate cancer patients undergoing ADT. As acknowledged by the Authors the main limitation of the study is the limited sample of patients. However, since testosterone levels were not assessed it is not possible to firmly establish whether the changes in fat mass observed with treatment are directly or indirectly associated with a reduction in FSH (and therefore in the latter case mediated by testosterone). Moreover, it is not clear whether the effect of the change in FSH levels during the study and the body composition parameters achieved at 12 months was evaluated (instead of assessing the relationship between FSH changes and changes in body composition parameters). Finally, tests on bone muscle mass and strength were not performed, so the hypothesis that variation of FSH levels in prostate cancer patients in ADT may affect sarcopenia remains speculative.

We appreciate the reviewer's positive assessment of our manuscript. We evaluated the correlation between FSH changes and body composition values after 12 months of Degarelix, as requested by the reviewer. No significant correlation was observed, see the attached table. Therefore we have decided not to insert this last statistical analysis in the revised paper.

Author Response

Reviewer #1 (Public Review):

Using a HFD mouse model, the authors examined the H3K4me3 mark in sperm and placental tissues followed by correlation to the transcriptomic changes in the placental tissues of the male and female offspring. The hypothesis that the authors tried to test was that sperm histone epimutations affect placental function, thereby leading to metabolic disorders in offspring. The strength of this work includes the interesting idea and the initial data generated. However, the entire study remains purely correlative without any validation experiment to support the correlation. The conclusion needs to be further supported by bigger sample size and more functional analyses demonstrating the causal relationship among the histone epimutations detected, the dysregulated mRNA expression in the placenta, and the phenotypes in offspring.

Functional data: We appreciate that we should have emphasized and written more clearly that we had indeed phenotyped the placentas and offspring metabolic health from the same model we derived the placenta tissue from as we reported in (Jazwiec et al., 2022)(PMID: 35377412). This was referenced in our submitted manuscript (Lines 105-107; 131-133; 135-139; 147-150; 232-235; 270-273; 297-300; 384-386; 433-435; 441-448; 507-514). We have made this more apparent in the manuscript by expanding our description of the offspring phenotypes in the introduction and clarified that it was from this model that the placenta’s used in this study were derived from (Jazwiec et al., 2022) (PMID: 35377412).

Regarding effect and sample size: It appears that on review the animal numbers used for the ChIP-seq were confused with the number of replicates by the reviewers. These details were in Supplementary file 1a. There were 3 replicates per experimental group and each replicate contained sperm from pooled samples that was equalized in cell number and comprised of sperm from n=7 control males, or n=16 HFD males. For the RNA-seq n=4 placentas were used from each experimental group from both males and females for a total N of 16. Although the sample size is moderate, we followed the Canadian Council of Animal Care guideline which calls for the use of the lowest animal number that elicits significant effects (CCAC guidelines p6 “Consideration must also be given to reduction, to determine the fewest number of animals appropriate to provide valid information and statistical power, while still minimizing the welfare impact for each animal”).

Validation: We used a high standard of computational validation and visualization strategies, to ensure confidence in genomic data. This also allowed for a comprehensive understanding of the biological and physiological impacts of paternal obesity on the sperm epigenome and placenta transcriptome. In our experimental design we also included biological and technical replicates. Together these methods provide robustness checks of the experimental data and support our conclusions. These are the validation strategies we used:

Technical and experimental validation

• We evaluated the quality of sequencing data using metrics of read quality, alignment and coverage. These are summarized in Supplementary file 1a.

• Visualized and performed statistical analysis of data to check for anomalies and discrepancies, Pearson correlation analysis shown on heatmap to look for variance and patterns in samples- all here highly correlated (Figure 2 – Figure supplement 1 B and Figure 4 – Figure supplement 1 A). We checked for batch effects and normalized the data (Figure 4 – Figure supplement 1 B) we used PCA plot analysis as a second check for sample behaving oddly (Figure 2 – Figure supplement 1 C and Figure 4 – Figure supplement 1 C).

• We used a deconvolution approach to improve the biological meaning of our bulk RNA-seq data (Figure 6, Figure 5 – Figure supplement 1 and 2).

• Performed functional enrichment analysis to gain insight into biological functions, pathways, and genome ontology and visualized individual regions identified to be altered as a confirmation (Figure 2 D and 2 E; Figure 4 E and F; Figure 6, Figure 2 – Figure supplement 1 E; Figure 3 – Figure supplement 1). Comparison to external data sets:

• We compared our data with external data sets using the same tissues and cell and to our prior studies: a) We compared ChIP-seq data from this obesity model with our former obesity ChIP-seq data (Figure 2 – Figure supplement 1); b) re-analyzed and compared placenta RNA-seq data from an in utero exposure hypoxia model that shared similar offspring and placenta phenotypes as we observed in the obesity model (Figure 6 and Figure 6 – Figure supplement 1).

• We used a deconvolution approach to improve the biological meaning of our bulk RNA-seq data (Figure 6, Figure 5 – Figure supplement 1 and 2). Statistical Significance and False Discovery Rate (FDR):

• We applied statistical tests and multiple testing corrections to reduce the likelihood of false positives (See also response 1 for additional testing added to the revised manuscript)

Causation versus correlation: We agree that the relationship between the sperm epigenome and placenta transcriptome is correlative, however this is the current state of the field for studies of paternal epigenetic transmission of environmental information. To take this study to the point where causation can be implied would require the generation of a sperm epigenome edited mouse model where we target genes implicated in placental function. Indeed, this targeting approach is well underway in our research program.

Reviewer #2 (Public Review):

This study follows up on previous work from this group, and others, relating paternal diet to changes in sperm epigenetics, and offspring phenotypes. The authors focus on paternal diet (high-fat diet versus a control chow), sperm chromatin, and molecular changes in the placenta associated with offspring development.

The text is well written and the figures are generally well presented and clear. The sperm epigenetic analyses and analysis of the placenta epigenetics and gene expression are generally well performed. The study provides new insight into how paternally mediated intergenerational epigenetic inheritance could involve placenta-embryo signaling.

A major weakness is that the high-fat diet used was from a different manufacturer than the control (lower fat) diet. Therefore, it is difficult to judge whether the effects are due to a change in fat levels, or the many other molecules that are likely to differ in chow between different manufacturers. Other weaknesses include lack of methodological detail in parts, low n values for some experiments, and the need for more mechanistic data.

Diets: It is worth reminding that we are studying the effects of obesity and not diet. Indeed, HFD induces metabolic dysfunction while the control does not. Although it is fair to point out that the composition of the control diet should be kept in mind, considering the desired outcomes within the scope of the study, the diets elicited the desired phenotypic effects serving as a model for obesity. We see this experimental design as a strength, as in this study we compared this model to our previous published obesity model (Pepin, Lafleur, Lambrot, Dumeaux, & Kimmins, 2022) (PMID: 35183795), and there was significant overlap in the regions of differential enrichment detected between both models even though they were conducted in different research settings, with different mouse substrain and different diet combinations. In our opinion this demonstrates that we are measuring robust effects of paternal obesity that can be replicated under different conditions. This comparative study design has been lacking in the field of epigenetic inheritance.

Animal numbers and replicates: It appears that on review the animal numbers used for the ChIP-seq were confused with the number of replicates by the reviewers. These details were in Supplementary file 1a. There were 3 replicates per experimental group and each replicate contained sperm from pooled samples that was equalized in cell number and comprised of sperm from n=7 control males, or n=16 HFD males. For the RNA-seq n=4 placentas were used from each experimental group from both males and females for a total N of 16. Although the sample size is moderate, we followed the Canadian Council of Animal Care guideline which calls for the use of the lowest animal number that elicits significant effects (CCAC guidelines p6 “Consideration must also be given to reduction, to determine the fewest number of animals appropriate to provide valid information and statistical power, while still minimizing the welfare impact for each animal”).

Whilst the authors may have achieved their aims, more data is needed to inform a potential mechanism.

It is difficult in studies on paternal epigenetic inheritance to attribute a mechanism and we agree that the relationship between the obesity altered sperm epigenome and the placenta abnormalities are correlative. However, the novelty in our study is that we postulate a new mechanism for paternal transmission of metabolic disease that implicates the placenta and demonstrate this via an altered placenta transcriptome and placenta developmental abnormalities described here and in our previous paper on this model ((Jazwiec et al., 2022); PMID: 35377412). The next steps for the field to address causation/mechanism requires generation of a sperm epigenome edited mouse model where we induce and track histone methylation changes at specific genes to the tissues in the next generation. Indeed, this targeting approach is underway in our research program.

Reviewer #3 (Public Review):

This study represents a useful addition to the authors' previous study examining the effects of paternal high-fat diet on offspring metabolism and gene expression in offspring (PMID: 35183795). It differs from the previous study in some of the details of the experimental model (age of sire when exposed to the diet manipulation, mouse substrain, and the nature of the control diet) and the results are largely in line with previous findings. The major finding is that many genes at which sperm H3K4me3 signal is altered also have altered expression in the placenta; some of these genes are paternally imprinted, providing a paternal-specific epigenetic signature. Strengths of the study include establishment of an important dataset correlating the sperm epigenome with gene expression in placental tissue, leading to an interesting and provocative conclusion. Weaknesses include a relatively superficial analysis of the dataset, revealing broad patterns but few specific conclusions, reliance on correlative analysis to draw conclusions, and absence of validation studies. Deconvolution analysis of bulk RNA-seq data helps to account for differences in cell composition between placental datasets, but does not add additional insight toward the central question of how sperm epigenetic state contributes to offspring gene expression. Overall the advance over previous work is relatively small.

Specific points:

1) The analysis as it stands is limited. To compare sperm H3K4me3 and placental expression, numbers of overlapping genes are provided, but no statistical analysis is done to indicate the significance of the overlap.

Fisher’s exact test to overlap paternal obesity-associated differentially enriched regions of H3K4me3 deH3K4me3) with female and male placenta differentially enriched genes (Figure 4 – Figure supplement 1 Di and ii).

2) There is little direct connection to biological systems or validation of differential enrichment/expression analysis. Gene ontology enrichments for genes differentially enriched for H3K4me3 in sperm or differentially expressed in placenta (broken up by sex) are performed, but the biological significance of these categories is not clear.

We used a high standard of computational validation and visualization strategies, to ensure confidence in genomic data. This also allowed for a comprehensive understanding of the biological and physiological impacts of paternal obesity on the sperm epigenome and placenta transcriptome. In our experimental design we also included biological and technical replicates. Together these methods provide robustness checks of the experimental data and support our conclusions. The validation strategies we used are detailed in response 17.

We revised the text to expand discussion on the observed enriched gene ontology terms, as well as the biological significance and functions of the genes we refer to in this section:

Lines 222-227: “The placenta is a rich source of hormone production, is highly vascularized, and secretes neurotransmitters (Hemberger, Hanna, & Dean, 2020; Rosenfeld, 2021). Disruption in these functions is suggested in the significantly enriched pathways that included genes involved in the transport of cholesterol, angiogenesis, and neurogenesis (Figure 4 C-D, Supplementary file 1e-f). Other significantly enriched processes included genes implicated in nutrient and vitamin transport (Figure 4 C-D).”

Lines 441-463:“Many of the DEGs in the paternal obese-sired placentas were involved in the regulation of the heart and brain. This is in line with paternal obesity associated to the developmental origins of neurological, cardiovascular, and metabolic disease in offspring (Andescavage & Limperopoulos, 2021; Binder, Beard, et al., 2015; Binder et al., 2012; Chambers et al., 2016; Cropley et al., 2016; de Castro Barbosa et al., 2016b; T. Fullston et al., 2012; Tod Fullston et al., 2013; Grandjean et al., 2015; Huypens et al., 2016; Jazwiec et al., 2022; Mitchell, Bakos, & Lane, 2011; Ng et al., 2010; Pepin et al., 2022; Perez-Garcia et al., 2018; Terashima et al., 2015; Thornburg et al., 2016; Thornburg & Marshall, 2015; Ueda et al., 2022; Wei et al., 2014). The brain-placenta and heart-placenta axes refer to their developmental linkage to the trophoblast which produces various hormones, neurotransmitters, and growth factors that are central to brain and heart development (Parrettini, Caroli, & Torlone, 2020; Rosenfeld, 2021). This is further illustrated in studies where placental pathology is linked to cardiovascular and heart abnormalities (Andescavage & Limperopoulos, 2021; Thornburg et al., 2016; Thornburg & Marshall, 2015). For example, in a study of the relationship between placental pathology and neurodevelopment of infants, possible hypoxic conditions were a significant predictor of lower Mullen Scales of Early Learning (Ueda et al., 2022). A connecting factor between the neural and cardiovascular phenotypes is the neural crest cells which make a critical contribution to the developing heart and brain (Hemberger et al., 2020; Perez-Garcia et al., 2018). Notably, neural crest cells are of ectodermal origin which arises from the TE (Prasad, Charney, & García-Castro, 2019), which is in turn governed by paternally-driven gene expression. It is worth considering the routes by which TE dysfunction may be implicated in the paternal origins of metabolic and cardiovascular disease. First, altered placenta gene expression beginning in the TE could influence the specification of neural crest cells which are a developmental adjacent cell lineage in the early embryo. TE signaling to neural crest cells could alter their downstream function. Second, altered trophoblast endocrine function will influence cardiac and neurodevelopment (Hemberger et al., 2020).”

3) The overall effect size is small. In most cases the magnitude of differences is minor, and it is not clear which of these changes are significant over noise. For example, the y-axis for the metagene plots in Figure 2B does not start at zero, so the total range of the difference in H3K4me3 is small. In Figure 6C, DEGs detected in hypoxic placenta after deconvolution analysis do not look very different compared to control.

Thank-you for pointing out that the scales were different in Figure 2 Bi and ii. They have been revised to show the same Y axis scale beginning at zero for comparison of regions that gained and lost H3K4me3 making the differences in H3K4me3 more readily visible. The heatmap shown in Figure 6 C visualizes the DEGs in hypoxic vs control placenta where 1477 DEGS were identified in our re-analysis using a convolution approach applied to the bulk-seq data set from Chu et al., 2019. We do not share the view that they are not well visualized in the heat map.

4) Deconvolution analysis was done on bulk RNA-seq data from placenta, and the numbers of DEGs identified with this analysis compared to the original analysis are shown, but is not clear how the deconvolution analysis changes the specific biological conclusions. In addition, the reference dataset for deconvolution is a published dataset generated in another lab, and it is unclear how comparable the reference sample is to the samples analyzed in this study, or how robust this analysis is when using a dataset generated under different conditions.

The deconvolution analysis allows to infer cellular composition within a tissue and suggests that there are changes in cell-type proportion that could change placenta function and improves the detection of differentially expressed genes (Aliee & Theis, 2021; Campbell et al., 2023; Kuhn, Thu, Waldvogel, Faull, & Luthi-Carter, 2011) (PMID: 34293324; 36914823; 21983921).

As per the published dataset used as a reference sample for the deconvolution analysis, it was ideal -we specifically chose this dataset for this analysis as the tissue of origin matched for the same mouse strain and developmental type points as our samples and those used in the Chu et al., 2019 analysis. We used the Chu et al., 2019 data set for comparative validation, and to further explore whether the biological effects of paternal obesity were like those of a hypoxic placenta. We have revised the text to more clearly show the biological relevance and interpretation of this analysis (see author response 12)

We revised the text to clarify the biological implications of this analysis:

Lines 282-290: “This reduction in the number of detected DEGs before versus after accounting for cellular composition suggests that changes in cell-type proportions at least partly drive tissue-level differential expression. This is consistent with the recent finding that preeclampsia-associated cellular heterogeneity in human placentas mediates previously detected bulk gene expression differences (Campbell et al., 2023). There were similarities between the bulk RNA-seq and deconvoluted analysis in that there was overlap of DEGs detected before and after adjusting for cell-type proportions (Figure 5 – Figure supplement 3 G and H, Fisher’s exact test P=1.8e-105 and P=0e+00, respectively). This differential gene expression analysis accounting for cellular composition provides insight into how paternal obesity may impact placental development and function and underscores the contribution of cellular heterogeneity in this process.”

Reviewer #4 (Public Review):

The members of the Kimmins lab perform a dietary study in mice to investigate the impact of obesity of fathers on the development of their offspring. To do so, they expose male mice to a high fat diet and determine the distribution and occupancy levels of the histone H3 lysine 4 trimethylation (H3K4me3) mark in spermatozoa and perform gene expression studies on placenta tissue obtained from mouse embryos during mid-gestation development. The authors report changes in H3K4me3 occupancy in sperm as well as in transcriptomes of placentas of male and female embryonic offspring. While the authors perform extensive computational analysis of the transcriptomic and chromatin immunoprecipitation data, the authors do not go much beyond making correlative statements at mainly the genome wide level between changes for H3K4me3 in sperm and transcriptional changes in placenta, the latter of which are in part related to changes in cellular composition (as deduced from transcriptional data). Given that both parental mice had the same genetic background, it was not possible to deduce parental specific contributions to transcriptional changes as observed in placentas of offspring. In all, the study falls short in increasing mechanistic insights into this important biological phenomenon.

It is difficult in studies on paternal epigenetic inheritance to attribute a mechanism and we agree that the relationship between the obesity altered sperm epigenome and the placenta abnormalities are correlative. However, the novelty in our study is that we postulate a new mechanism for paternal transmission of metabolic disease that implicates the placenta and demonstrate this via an altered placenta transcriptome and placenta developmental abnormalities described here and in our previous paper on this model ((Jazwiec et al., 2022); PMID: 35377412). The next steps for the field to address causation/mechanism requires generation of a sperm epigenome edited mouse model where we induce and track histone methylation changes at specific genes to the tissues in the next generation. Indeed, this targeting approach is underway in our research program.

Author Response

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

We appreciate the constructive comments made by the editor and the reviewers. We have corrected errors and provided additional experimental data and analysis to address the latest criticisms raised by the reviewers and provided point-by-point response to the reviewers as below.

Reviewer #1 (Recommendations For The Authors):

I do acknowledge the work the authors put into this manuscript and I can accept the fact that the authors decided on a minimum of additional experiments. However, I would recommend the authors to be more concise by adding more information in the method and result sections about how they performed their experiments such as which Nav and AMPAR DNA constructs they used, the age of the mice, how long time they exposed the patches to quinidine, information on how many times they repeated their pull downs etc.

Answer: We thank the reviewer’s comments. we have incorporated the suggested modifications into our revised manuscript. Specifically, we have included detailed information on the NaV and AMPAR constructs in the Methods section. The age of the homozygous NaV1.6 knockout mice and the wild-type littermate controls is postnatal (P0-P1) (see in Results and Methods section). Prior to the application of step pulses, cells were subjected to the bath solution containing quinidine for approximately one minute (see in Methods section). Additionally, the co-immunoprecipitation assays for Slack and NaV1.6 were repeated three times (see in Methods section).

Minor detail in line 263: "...KCNT1 (Slack) have been identified to related to seizure..." I guess this should have been "...KCNT1 (Slack) have been identified and related to seizure..."?

Answer: We thank the reviewer for raising this point. We have corrected it in the revised manuscript.

Also, and again minor detail, I had a comment about the color coding in Fig 4 and by mistake, I added 4B, but I meant the use of colors in the entire figure, and mainly the use of colors in 4C, G and I.

Answer: We apologize for the confusion. We have changed the color coding of Figure 4 in the revised manuscript.

Reviewer #2 (Recommendations For The Authors):

While the paper is improved, several concerns do not seem to have been addressed. Some may have been missed because there is no response at all, but others may have been unclear because the response does not address the concern, but a related issue. Details are below.

Answer: We thank the reviewer for the criticisms. We have made changes of our manuscript to address the concerns.

Original issue:

3) Remove the term in vivo.

Answer: We thank the reviewer for raising this point. In our experiments, although we did not conduct experiments directly in living organisms, our results demonstrated the coimmunoprecipitation of NaV1.6 with Slack in homogenates from mouse cortical and hippocampal tissues (Fig. 3C). This result may support that the interaction between Slack and NaV1.6 occurs in vivo.

New comment from reviewer:

The argument to use the term in vivo is not well supported by what the authors have said. Just because tissues are used from an animal does not mean experiments were conducted in vivo. As the authors say, they did not conduct experiments in living organisms. Therefore the term in vivo should be avoided. This is a minor point.

Answer: We thank the reviewer for pointing this out. We have removed the term “in vivo” in the revised manuscript.

Original:

4) Figure 1C Why does Nav1.2 have a small inward current before the large inward current in the inset?

Answer: We apologize for the confusion. We would like to clarify that the small inward current can be attributed to the current of membrane capacitance (slow capacitance or C-slow). The larger inward current is mediated by NaV1.2.

New comment:

This is not well argued. Please note why the authors know the current is due to capacitance. Also, how do they know the larger current is due to NaV1.2? Please add that to the paper so readers know too.

Answer: We thank the reviewer’s comment. To provide a clearer representation of NaV1.2mediated currents in Fig. 1C, we have replaced the original example trace with a new one in which only one inward current is observed.

Original:

The slope of the rising phase of the larger sodium current seems greater than Nav1.6 or Nav1.5. Was this examined?

Answer: Additionally, we did not compare the slope of the rising phase of NaV subtypes sodium currents but primarily focused on the current amplitudes.

New comment:

This is not a strong answer. There seems to be an effect that the authors do not mention and evidently did not quantify that argues against their conclusion, which weakens the presentation.

Answer: We thank the reviewer’s comment. To assess the slope of the rising phase of NaV subtype currents, we compared the activation time constants of NaV1.2, NaV1.5, and NaV1.6 peak currents in HEK293 cells co-expressing NaV channel subtypes with Slack. The results have shown no significant differences (Author response image 1). We have included this analysis (see Fig. S9A) and the corresponding fitting equation (see in Methods section) in the revised manuscript.

Author response image 1.

The activation time constants of peak sodium currents in HEK293 cells co-expressing NaV1.2 (n=6), NaV1.5 (n=5), and NaV1.6 (n=5) with Slack, respectively. ns, p > 0.05, one-way ANOVA followed by Bonferroni’s post hoc test.

Original:

2D-E For Nav1.5 the sodium current is very large compared to Nav1.6. Is it possible the greater effect of quinidine for Nav1.6 is due to the lesser sodium current of Nav1.6?

Answer: We thank the reviewer for raising this point. We would like to clarify that our results indicate that transient sodium currents contribute to the sensitization of Slack to quinidine blockade (Fig. 2C,E). Therefore, it is unlikely that the greater effect observed for NaV1.6 in sensitizing Slack is due to its lower sodium currents.

New comment:

I am not sure the question I was asking was clear. How can the authors discount the possibility that quinidine is more effective on NaV1.6 because the NaV1.6 current is relatively weak?

Answer: We thank the reviewer for raising this point. We have examined the sodium current amplitudes of NaV1.5, NaV1.5/1.6 chimeras, and NaV1.6 upon co-expression of NaV with Slack. Our analysis revealed that there are no significant differences between NaV1.5 and NaV1.5/6N, with both exhibiting much larger current amplitudes compared to NaV1.6 (Author response image 2), but only NaV1.5/6N replicates the effect of NaV1.6 in sensitizing Slack to quinidine blockade (Fig. 4H-I), suggesting the observed differences between NaV1.5 and NaV1.6 in sensitizing Slack are unlikely to be attributed to NaV1.6's lower sodium currents but may instead involve NaV1.6's Nterminus-induced physical interaction. We have included this analysis in the revised manuscript (see Fig. S9B).

Author response image 2.

Comparison of peak sodium current amplitudes of NaV1.5 (n=9), NaV1.5/6NC (n=13), NaV1.5/6N (n=10), and NaV1.6 (n=8) upon co-expressed with Slack in HEK293 cells. ns, p > 0.05, * p < 0.05, ** p < 0.01, *** p < 0.001, **** p < 0.0001; one-way ANOVA followed by Bonferroni’s post hoc test.

Original:

The differences between WT and KO in G -H are hard to appreciate. Could quantification be shown? The text uses words like "block" but this is not clear from the figure. It seems that the replacement of Na+ with Li+ did not block the outward current or effect of quinidine.

Answer: We apologize for the confusion. We would like to clarify the methods used in this experiment. The lithium ion (Li+) is a much weaker activator of sodium-activated potassium channel Slack than sodium ion (Na+)1,2.

1. Zhang Z, Rosenhouse-Dantsker A, Tang QY, Noskov S, Logothetis DE. The RCK2 domain uses a coordination site present in Kir channels to confer sodium sensitivity to Slo2.2 channels. J Neurosci. Jun 2 2010;30(22):7554-62. doi:10.1523/JNEUROSCI.0525-10.2010

2. Kaczmarek LK. Slack, Slick and Sodium-Activated Potassium Channels. ISRN Neurosci. Apr 18 2013;2013(2013)doi:10.1155/2013/354262 Therefore, we replaced Na+ with Li+ in the bath solution to measure the current amplitudes of sodium-activated potassium currents (IKNa)3.

3. Budelli G, Hage TA, Wei A, et al. Na+-activated K+ channels express a large delayed outward current in neurons during normal physiology. Nat Neurosci. Jun 2009;12(6):745-50. doi:10.1038/nn.2313

The following equation was used for quantification:

Furthermore, the remaining IKNa after application of 3 μM quinidine in the bath solution was measured as the following:

The quantification results were presented in Fig. 1K. The term "block" used in the text referred to the inhibitory effect of quinidine on IKNa.

New comment:

The fact remains that the term "block" is too strong for an effect that is incomplete. Also, the authors should add to the paper that Li+ is a weaker activator, so the reader knows some of the caveats to the approach.

Answer: We thank the reviewer for raising this point. We have added related citations and replaced the term “block” with “inhibit” in the revised manuscript.

Original:

1. In K, for the WT, why is the effect of quinidine only striking for the largest currents?

Answer: We thank the reviewer for raising this point. After conducting an analysis, we found no correlation between the inhibitory effect of quinidine and the amplitudes of baseline IKNa in WT neurons (p = 0.6294) (Author response image 3). Therefore, the effect of quinidine is not solely limited to targeting the larger currents.

Author response image 3.

The correlation between the inhibitory effect of quinidine and the amplitudes of baseline IKNa in WT neurons (data from manuscript Fig. 1K). r = 0.1555, p=0.6294, Pearson correlation analysis.

New comment:

Please add this to the paper and the figure as Supplemental.

Answer: We thank the reviewer for raising this point. We have added this figure as Fig.S3B in the revised manuscript.

Original:

5) Figure 2 A. The argument could be better made if the same concentration of quinidine were used for Slack and Slack + Nav1.6. It is recognized a greater sensitivity to quinidine is to be shown but as presented the figure is a bit confusing."

Answer: We apologize for the confusion. We would like to clarify that the presented concentrations of quinidine were chosen to be near the IC50 values for Slack and Slack+NaV1.6.

New comment:

Please add this to the paper.

Answer: We thank the reviewer for raising this point. We have added the clarification about the presented concentrations in the revised manuscript.

Original:

2C. Can the authors add the effect of quinidine to the condition where the prepulse potential was 90?"

Answer: We apologize for the confusion. We would like to clarify that the condition of prepulse potential at -90 mV is the same as the condition in Fig. 1. We only changed one experiment condition where the prepulse potential was changed to -40 mV from -90 mV.

New comment:

There was no confusion. The authors should consider adding the condition where the prepulse potential was -90.

Answer: We thank the reviewer for raising this point. We have added the clarification about the voltage condition in the revised manuscript (see in Fig. 2A caption).

Original:

2A. Clarify these 6 panels."

Answer: We thank the reviewer for raising this point. We have clarified the captions of Fig. 3A in the revised manuscript.

New comment: Clarification is needed. What is the blue? DAPI? What area of hippocamps? Please label cell layers. What area of cortex? Please label layers.

Answer: We thank the reviewer for raising this point. We have included the clarification in the Figure caption.

Original:

Figure 7. The images need more clarity. They are very hard to see. Text is also hard to see."

Answer: We apologize for the lack of clarity in the images and text. we would like to provide a concise summary of the key findings shown in this figure.

Figure 7 illustrates an innovative intervention for treating SlackG269S-induced seizures in mice by disrupting the Slack-NaV1.6 interaction. Our results showed that blocking NaV1.6-mediated sodium influx significantly reduced Slack current amplitudes (Fig. 2D,G), suggesting that the Slack-NaV1.6 interaction contributes to the current amplitudes of epilepsy-related Slack mutant variants, aggravating the gain-of-function phenotype. Additionally, Slack’s C-terminus is involved in the Slack-NaV1.6 interaction (Fig. 5D). We assumed that overexpressing Slack’s C-terminus can disrupt the Slack-NaV1.6 interaction (compete with Slack) and thereby encounter the current amplitudes of epilepsy-related Slack mutant variants.

In HEK293 cells, overexpression of Slack’s C-terminus indeed significantly reduced the current amplitudes of epilepsy-related SlackG288S and SlackR398Q upon co-expression with NaV1.5/6NC (Fig. 7A,B). Subsequently, we evaluated this intervention in an in vivo epilepsy model by introducing the Slack G269S variant into C57BL/6N mice using AAV injection, mimicking the human Slack mutation G288S that we previously identified (Fig. 7C-G).

New comment:

The images do not appear to have changed. Consider moving labels above the images so they can be distinguished better. Please label cell layers. Consider adding arrows to the point in the figure the authors want the reader to notice. The study design and timeline are unclear. What is (1) + (3), (2), etc.?

Answer: We thank the reviewer for pointing this out. We have modified Figure 7 in the revised manuscript and included the cell layer information in the Figure caption.

Original:

It is not clear how data were obtained because injection of kainic acid does not lead to a convulsive seizure every 10 min for several hours, which is what appears to be shown. Individual seizures are just at the beginning and then they merge at the start of status epilepticus. After the onset of status epilepticus the animals twitch, have varied movements, sometime rear and fall, but there is not a return to normal behavior. Therefore one can not call them individual seizures. In some strains of mice, however, individual convulsive seizures do occur (even if the EEG shows status epilepticus is occurring) but there are rarely more than 5 over several hours and the graph has many more. Please explain."

Answer: We apologize for the confusion. Regarding the data acquisition in relation to kainic acid injection, we initiated the timing following intraperitoneal injection of kainic acid and recorded the seizure scores of per mouse at ten-minute intervals, following the methodology described in previous studies4.

1. Huang Z, Walker MC, Shah MM. Loss of dendritic HCN1 subunits enhances cortical excitability and epileptogenesis. J Neurosci. Sep 2 2009;29(35):10979-88. doi:10.1523/JNEUROSCI.1531-09.2009

The seizure scores were determined using a modified Racine, Pinal, and Rovner scale5,6: (1) Facial movements; (2) head nodding; (3) forelimb clonus; (4) dorsal extension (rearing); (5) Loss of balance and falling; (6) Repeated rearing and failing; (7) Violent jumping and running; (8) Stage 7 with periods of tonus; (9) Dead.

1. Pinel JP, Rovner LI. Electrode placement and kindling-induced experimental epilepsy. Exp Neurol. Jan 15 1978;58(2):335-46. doi:10.1016/0014-4886(78)90145-0

2. Racine RJ. Modification of seizure activity by electrical stimulation. II. Motor seizure. Electroencephalogr Clin Neurophysiol. Mar 1972;32(3):281-94. doi:10.1016/00134694(72)90177-0

New comment:

This was clear. Perhaps my question was not clear. The question is how one can count individual seizures if animals have continuous seizures. It seems like the authors did not consider or observe status epilepticus but individual seizures. If that is true the data are hard to believe because too many seizures were counted. Animals do not have nearly this many seizures after kainic acid.

Answer: We appreciate the reviewer’s clarification. Our methodology involved assessing the maximum seizure scale during 10-minute intervals per mouse as previously described7, rather than counting individual seizures. For instance, a mouse exhibited the loss of balance and falling multiple times within 30-40 minute interval, we recorded the seizure scale as 5 for that time interval.

1. Kim EC, Zhang J, Tang AY, et al. Spontaneous seizure and memory loss in mice expressing an epileptic encephalopathy variant in the calmodulin-binding domain of Kv7.2. Proc Natl Acad Sci U S A. Dec 21 2021;118(51)doi:10.1073/pnas.2021265118

Reviewer #3 (Recommendations For The Authors):

While the authors have improved the manuscript, several outstanding issues still need to be addressed. Some may have been missed because there is no response at all, but others may have been unclear.

Answer: We thank the reviewer for the criticisms. We have added additional experimental data and analysis to address the concerns.

Original issue from Public Review:

1. Immunolabeling of the hippocampus CA1 suggests sodium channels as well as Slack colocalization with AnkG (Fig 3A). Proximity ligation assay for NaV1.6 and Slack or a super-resolution microscopy approach would be needed to increase confidence in the presented colocalization results. Furthermore, coimmunoprecipitation studies on the membrane fraction would bolster the functional relevance of NaV1.6-Slack interaction on the cell surface.

Answer: We thank the reviewer for good suggestions. We acknowledge that employing proximity ligation assay and high-resolution techniques would significantly enhance our understanding of the localization of the Slack-NaV1.6 coupling.

At present, the technical capabilities available in our laboratory and institution do not support highresolution testing. However, we are enthusiastic about exploring potential collaborations to address these questions in the future. Furthermore, we fully recognize the importance of conducting coimmunoprecipitation (Co-IP) assays from membrane fractions. While we have already completed Co-IP assays for total protein and quantified the FRET efficiency values between Slack and NaV1.6 in the membrane region, the Co-IP assays on membrane fractions will be conducted in our future investigations.

New comment from reviewer: so far, the authors have not demonstrated that Nav1.6 and Slack interact on the cell surface.

Answer: We thank the reviewer for pointing this out. We acknowledgement that our data did not directly demonstrate interaction between NaV1.6 and Slack on the cell surface and we have removed related terminology in the revised manuscript. Notably, our patch-clamp experiments in Fig. 2D,G and Fig. S10B showed a Na+-mediated membrane current coupling of Slack and NaV1.6. Additionally, the FRET efficiency values between Slack and NaV1.6 were quantified in the membrane region. These findings suggest that membrane-near Slack interacts with NaV1.6.

1. Although hippocampal slices from Scn8a+/- were used for studies in Fig. S8, it is not clear whether Scn8a-/- or Scn8a+/- tissue was used in other studies (Fig 1J & 1K). It will be important to clarify whether genetic manipulation of NaV1.6 expression (Fig. 1K) has an impact on sodiumactivated potassium current, level of surface Slack expression, or that of NaV1.6 near Slack.

Answer: We thank the reviewer for pointing this out. In Fig. 1G,J,K, primary cortical neurons from homozygous NaV1.6 knockout (Scn8a-/-) mice were used. We will clarify this information in the revised manuscript. In terms of the effects of genetic manipulation of NaV1.6 expression on IKNa and surface Slack expression, we compared the amplitudes of IKNa measured from homozygous NaV1.6 knockout (NaV1.6-KO) neurons and wild-type (WT) neurons. The results showed that homozygous knockout of NaV1.6 does not alter the amplitudes of IKNa (Author response image 4). The level of surface Slack expression will be tested further.

Author response image 4.

The amplitudes of IKNa in WT and NaV1.6-KO neurons (data from manuscript Fig. 1K). ns, p > 0.05, unpaired two-tailed Student’s t test.

New comment from reviewer: The current version of the manuscrip>t does not contain these pertinent details and needs to be updated to include the information pertaining homozygous NaV1.6 knockouts. What age were these homozygous NaV1.6 knockout mice? These details need to be clearly stated in the manuscript.

Answer: We thank the reviewer for pointing this out. We have included this analysis in the revised manuscript (see Fig. S3A). The age of homozygous NaV1.6 knockout mice are P0-P1 and we have added this detail in the revised manuscript.

1. Did the epilepsy-related Slack mutations have an impact on NaV1.6-mediated sodium current?

Answer: We thank the reviewer’s question. We examined the amplitudes of NaV1.6 sodium current upon expression alone or co-expression of NaV1.6 with epilepsy-related Slack mutations (K629N, R950Q, K985N). The results showed that the tested epilepsy-related Slack mutations do not alter the amplitudes of NaV1.6 sodium current (Author response image 5).

Author response image 5.

The amplitudes of NaV1.6 sodium currents upon co-expression of NaV1.6 with epilepsy-related Slack mutant variants (SlackK629N, SlackR950Q, and SlackK985N). ns, p>0.05, oneway ANOVA followed by Bonferroni’s post hoc test.

New comment from reviewer: Figure with the functional effect of co-expression of NaV1.6 with epilepsy-related Slack mutations should be included in the revised manuscript

Answer: We thank the reviewer for pointing this out. We have included this analysis in the revised manuscript (see Fig. S10A).

Original issue from Recommendations For The Authors:

1. A reference to homozygous knockout is made in the abstract; however, only heterozygous mice are mentioned in the methods section. The genotype of the mice needs to be made clear in the manuscript. Furthermore, at what age were these mice used in the study. Since homozygous knockout of NaV1.6 is lethal at a very young age (<4 wks), it would be important to clarify that point as well.

Answer: We thank the reviewer for pointing this out. In the revised manuscript, we have included information about the source of the primary cortical neurons used in our study. These neurons were obtained from postnatal homozygous NaV1.6 knockout C3HeB/FeJ mice and their wild-type littermate controls.

New comment from reviewer: The answer that postnatal homozygous NaV1.6 knockout C3HeB/FeJ mice were used is insufficient. What age were these mice? This needs to be clearly stated in the manuscript.

Answer: We thank the reviewer for pointing this out. The postnatal homozygous NaV1.6 knockout C3HeB/FeJ mice and their wild-type littermate controls are in P0-P1. We have included this information in the revised manuscript.

1. How long were the cells exposed to quinidine before the functional measurement were performed?

Answer: We thank the reviewer for pointing this out. The cells were exposed to the bath solution with quinidine for about one minute before applying step pulses.

New comment from reviewer: This needs to be clearly stated in the manuscript.

Answer: We thank the reviewer for pointing this out. We have included this information in the revised manuscript (see in Methods section).

1. In Fig. 6B-D, it is not clear to what extent co-expression of Slack mutants and NaV1.6 increases sodium-activated potassium current.

Answer: We thank the reviewer for pointing this out. We notice that the current amplitudes of Slack mutants exhibit a considerable degree of variation, ranging from less than 1 nA to over 20 nA (n =58). To accurately measure the effects of NaV1.6 on increasing current amplitudes of Slack mutants, we plan to apply tetrodotoxin in the bath solution to block NaV1.6 sodium currents upon coexpression of Slack mutants with NaV1.6.

New comment from reviewer: Were these experiments with TTX completed? If so, they should be added to the revised manuscript.

Answer: We thank the reviewer for pointing this out. We compared the current amplitudes of epilepsy-related Slack mutant (SlackR950Q) before and after bath-application of 100 nM TTX upon co-expression with NaV1.6 in HEK293 cells. The results showed that bath-application of TTX significantly reduced the current amplitudes of SlackR950Q at +100 mV by nearly 40% (Author response image 6), suggesting NaV1.6 contributes to the current amplitudes of SlackR950Q. We have included this data in the revised manuscript (see Fig. S10B).

Author response image 6.

The current amplitudes of SlackR950Q before and after bath-application of 100 nM TTX upon co-expression with NaV1.6 in HEK293 cells (n=5). ***p < 0.001, Two-way repeated measures ANOVA followed by Bonferroni’s post hoc test.

Additionally, we have corrected some errors in the methods and figure captions section:

1. Line 513, bath solution “5 glucose” should be “10 glucose.”

2. Figure 3A caption, the description “hippocampus CA1 (left) and neocortex (right)” was flipped and we have corrected it.

References

1. Zhang Z, Rosenhouse-Dantsker A, Tang QY, Noskov S, Logothetis DE. The RCK2 domain uses a coordination site present in Kir channels to confer sodium sensitivity to Slo2.2 channels. J Neurosci. Jun 2 2010;30(22):7554-62. doi:10.1523/JNEUROSCI.0525-10.2010

2. Kaczmarek LK. Slack, Slick and Sodium-Activated Potassium Channels. ISRN Neurosci. Apr 18 2013;2013(2013)doi:10.1155/2013/354262

3. Budelli G, Hage TA, Wei A, et al. Na+-activated K+ channels express a large delayed outward current in neurons during normal physiology. Nat Neurosci. Jun 2009;12(6):745-50. doi:10.1038/nn.2313

4. Huang Z, Walker MC, Shah MM. Loss of dendritic HCN1 subunits enhances cortical excitability and epileptogenesis. J Neurosci. Sep 2 2009;29(35):10979-88. doi:10.1523/JNEUROSCI.1531-09.2009

5. Pinel JP, Rovner LI. Electrode placement and kindling-induced experimental epilepsy. Exp Neurol. Jan 15 1978;58(2):335-46. doi:10.1016/0014-4886(78)90145-0

6. Racine RJ. Modification of seizure activity by electrical stimulation. II. Motor seizure. Electroencephalogr Clin Neurophysiol. Mar 1972;32(3):281-94. doi:10.1016/0013-4694(72)90177-0

7. Kim EC, Zhang J, Tang AY, et al. Spontaneous seizure and memory loss in mice expressing an epileptic encephalopathy variant in the calmodulin-binding domain of Kv7.2. Proc Natl Acad Sci U S A. Dec 21 2021;118(51)doi:10.1073/pnas.2021265118

Author Response

Reviewer #1 (Public Review):

Summary:

In this manuscript, Benner et al. identify OVO as a transcriptional factor instrumental in promoting the expression of hundreds of genes essential for female germline identity and early embryo development. Prior data had identified both ovo and otu as genes activated by OVO binding to the promoters. By combining ChIP-seq, RNA-seq, and analysis of prior datasets, the authors extend these data to hundreds of genes and therefore propose that OVO is a master transcriptional regulator of oocyte development. They further speculate that OVO may function to promote chromatin accessibility to facilitate germline gene expression. Overall, the data compellingly demonstrate a much broader role for OVO in the activation of genes in the female germline than previously recognized. By contrast, the relationship between OVO, chromatin accessibility, and the timing of gene expression is only correlative, and more work will be needed to determine the mechanisms by which OVO promotes transcription.

We fully agree with this summary.

Strengths:

Here Benner et al. convincingly show that OVO is a transcriptional activator that promotes expression of hundreds of genes in the female germline. The ChIP-seq and RNA-seq data included in the manuscript are robust and the analysis is compelling.

Importantly, the set of genes identified is essential for maternal processes, including egg production and patterning of the early embryo. Together, these data identify OVO as a major transcriptional activator of the numerous genes expressed in the female germline, deposited into the oocyte and required for early gene expression. This is an important finding as this is an essential process for development and prior to this study, the major drivers of this gene expression program were unknown.

We are delighted that this aspect of the work came across clearly. Understanding the regulation of maternal effect genes has been something of a black-box, despite the importance of this class of genes in the history of developmental genetics. The repertoire of essential oogenesis/embryonic development genes that are bound by and respond to OVO are well characterized in the literature, but nothing is known about how they are transcriptionally regulated. We feel the manuscript will be of great interest to readers working on these genes.

Weaknesses:

The novelty of the manuscript is somewhat limited as the authors show that, like two prior, well-studied OVO target genes, OVO binds to promoters of germline genes and activates transcription. The fact that OVO performs this function more broadly is not particularly surprising.

Clearly, transcription factors regulate more than one or two genes. Never-the-less we were surprised at how many of the aspects of oogenesis per se and maternal effect genes were OVO targets. It was our hypothesis that OVO would have a transcriptional effect genome-wide, however, it was less clear whether OVO would always bind at the core promoter, as is with the case of ovo and otu. Our results strongly support the idea that core promoter proximal binding is essential for OVO function; a conclusion of work done decades ago, which has not been revisited using modern techniques.

A major challenge to understanding the impact of this manuscript is the fact that the experimental system for the RNA-seq, the tagged constructs, and the expression analysis that provides the rationale for the proposed pioneering function of OVO are all included in a separate manuscript.

This is a case where we ended up with a very, very long manuscript which included a lot of revisiting of legacy data. It was a tough decision on how to break up all the work we had completed on ovo to date. In our opinion, it was too much to put everything into a single manuscript unless we wanted a manuscript length supplement (we were also worried that supplemental data is often overlooked and sometimes poorly reviewed). We therefore decided to split the work into a developmental localization/characterization paper and a functional genomics paper. As it stands both papers are long. Certainly, readers of this manuscript will benefit from reading our previous OVO paper, which we submitted before this one. The earlier manuscript is under revision at another journal and we hope that this improved manuscript will be published and accessible shortly.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Benner et al. interrogate the transcriptional regulator OVO to identify its targets in the Drosophila germline. The authors perform ChIP-seq in the adult ovary and identify established as well as novel OVO binding motifs in potential transcriptional targets of OVO. Through additional bioinformatic analysis of existing ATAC-seq, CAGE-seq, and histone methylation data, the authors confirm previous reports that OVO is enriched at transcription start sites and suggest that OVO does not act as part of the core RNA polymerase complex. Benner et al. then perform bulk RNA-seq in OVO mutant and "wildtype" (GAL4 mediated expression of OVO under the control of the ovo promoter in OVO mutants) ovaries to identify genes that are differentially expressed in the presence of OVO. This analysis supports previous reports that OVO likely acts at transcription start sites as a transcriptional activator. While the authors propose that OVO activates the expression of genes that are important for egg integrity, maturation, and for embryonic development (nanos, gcl, pgc, bicoid), this hypothesis is based on correlation and is not supported by in vivo analysis of the respective OVO binding sites in some of the key genes. A temporal resolution for OVO's role during germline development and egg chamber maturation in the ovary is also missing. Together, this manuscript contains relevant ChIP-seq and RNA-seq datasets of OVO targets in the Drosophila ovary alongside thorough bioinformatic analysis but lacks important in vivo experimental evidence that would validate the high-quality datasets.

We thank reviewer 2 for the appreciation of the genomics data and analysis. Some of the suggested in vivo experiments are clear next steps, which are well underway. These are beyond the scope of the current manuscript.

Temporal analysis of ovo function in egg chamber development is not easy, as only the weakest ovo alleles have any egg chambers to examine. However, we will also point out the long-known phenotypes of some of those weak alleles in the text (e.g. ventralized chambers in ovoD3/+). We will need better tools for precise rescue/degradation during egg chamber maturation.

Strengths:

The manuscript contains relevant ChIP-seq and RNA-seq datasets of OVO targets in the Drosophila ovary alongside thorough bioinformatic analysis

Thank you. We went to great lengths to do our highly replicated experiments in multiple ways (e.g. independent pull-down tags) and spent considerable time coming up with an optimized and robust informatic analysis.

Weaknesses:

1) The authors propose that OVO acts as a positive regulator of essential germline genes, such as those necessary for egg integrity/maturation and embryonic/germline development. Much of this hypothesis is based on GO term analysis (and supported by the authors' ChIP-seq data). However accurate interpretation of GO term enrichment is highly dependent on using the correct background gene set. What control gene set did the authors use to perform GO term analysis (the information was not in the materials and methods)? If a background gene set was not previously specified, it is essential to perform the analysis with the appropriate background gene set. For this analysis, the total set of genes that were identified in the authors' RNA-seq of OVO-positive ovaries would be an ideal control gene set for which to perform GO term analysis. Alternatively, the total set of genes identified in previous scRNA-seq analysis of ovaries (see Rust et al., 2020, Slaidina et al., 2021 among others) would also be an appropriate control gene set for which to perform GO term analysis. If indeed GO term analysis of the genes bound by OVO compared to all genes expressed in the ovary still produces an enrichment of genes essential for embryonic development and egg integrity, then this hypothesis can be considered.

We feel that this work on OVO as a positive regulator of genes like bcd, osk, nos, png, gnu, plu, etc., is closer to a demonstration than a proposition. These are textbook examples of genes required for egg and early embryonic development. Hopefully, this is not lost on the readers by an over-reliance on GO term analysis, which is required but not always useful in genome-wide studies.

We used GO term enrichment analysis as a tool to help focus the story on some major pathways that OVO is regulating. To the specific criticism of the reference gene-set, GO term enrichment analysis in this work is robust to gene background set. We will update the GO term enrichment analysis text to indicate this fact and add a table using expressed genes in our RNA-seq dataset to the manuscript and clarify gene set robustness in greater detail in the methods of the revision. We will also try to focus the reader’s attention on the actual target genes rather than the GO terms in the revised text.

2) The authors provide important bioinformatic analysis of new and existing datasets that suggest OVO binds to specific motifs in the promoter regions of certain germline genes. While the bioinformatic analysis of these data is thorough and appropriate, the authors do not perform any in vivo validation of these datasets to support their hypotheses. The authors should choose a few important potential OVO targets based on their analysis, such as gcl, nanos, or bicoid (as these genes have well-studied phenotypes in embryogenesis), and perform functional analysis of the OVO binding site in their promoter regions. This may include creating CRISPR lines that do not contain the OVO binding site in the target gene promoter, or reporter lines with and without the OVO binding site, to test if OVO binding is essential for the transcription/function of the candidate genes.

Exploring mechanism using in vivo phenotypic assays is awesome, so this is a very good suggestion. But, it is not essential for this work -- as has been pointed out in the reviews, in vivo validation of OVO binding sites has been comprehensively done for two target genes, ovo and otu. The “rules” appear similar for both genes. That said, we are already following up specific OVO target genes and the detailed mechanism of OVO function at the core promoter. We removed some of our preliminary in vivo figures from the already long current manuscript. We continue to work on OVO and expect to include this type of analysis in a new manuscript.

3) The authors perform de novo motif analysis to identify novel OVO binding motifs in their ChIP-seq dataset. Motif analysis can be significantly strengthened by comparing DNA sequences within peaks, to sequences that are just outside of peak regions, thereby generating motifs that are specific to peak regions compared to other regions of the promoter/genome. For example, taking the 200 nt sequence on either side of an OVO peak could be used as a negative control sequence set. What control sequence set did the authors use as for their de novo motif analysis? More detail on this is necessary in the materials and methods section. Re-analysis with an appropriate negative control sequence set is suggested if not previously performed.

We apologize for being unclear on negative sequence controls in the methods. We used shuffled OVO ChIP-seq peak sequences as the background for the de novo motif analysis, which we will better outline in the methods of the revision. This is a superior background set of sequences as it exactly balances GC content in the query and background sequences. We are not fond of the idea of using adjacent DNA that won’t be controlled for GC content and shadow motifs. Furthermore, the de novo OVO DNA binding motifs are clear, statistically significant variants of the characterized in vitro OVO DNA binding motifs previously identified (Lu et al., 1998; Lee and Garfinkel, 2000; Bielinska et al., 2005), which lends considerable confidence. We also show that the OVO ChIP-seq read density are highly enriched for all our identified motifs, as well as the in vitro motifs. We provide multiple lines of evidence, through multiple methods, that the core OVO DNA binding motif is 5’-TAACNGT-3’. We have high confidence in the motif data.

4) The authors mention that OVO binding (based on their ChIP-seq data) is highly associated with increased gene expression (lines 433-434). How many of the 3,094 peaks (conservative OVO binding sites), and what percentage of those peaks, are associated with a significant increase in gene expression from the RNA-seq data? How many are associated with a decrease in gene expression? This information should be added to the results section.

Not including the numbers of the overlapping ChIP peaks and expression changes in the text was an oversight on our part. The numbers that relate to this (666 peaks overlapping genes that significantly increased in expression, significant enrichment according to Fishers exact test, 564 peaks overlapping genes that significantly decreased in expression, significant depletion according to Fishers exact test) are found in figure 4C and will be added to the text.

5) The authors mention that a change in endogenous OVO expression cannot be determined from the RNA-seq data due to the expression of the OVO-B cDNA rescue construct. Can the authors see a change in endogenous OVO expression based on the presence/absence of OVO introns in their RNA-seq dataset? While intronic sequences are relatively rare in RNA-seq, even a 0.1% capture rate of intronic sequence is likely to be enough to determine the change in endogenous OVO expression in the rescue construct compared to the OVO null.

This is a good point. The GAL4 transcript is downstream of ovo expression in the hypomorphic ovoovo-GAL4 allele. We state in the text that there is a nonsignificant increase in GAL4 expression with ectopic rescue OVO, although the trend is positive. We calculated the RPKM of RNA-seq reads mapping to the intron spanning exon 3 and exon 4 in ovo-RA and found that there is also a nonsignificant increase in intronic RPKM with ectopic rescue OVO (we will add to the results in the revision). We would expect OVO to be autoregulatory and potentially increase the expression of GAL4 and/or intronic reads, but the ovoovo-GAL4>UASp-OVOB is not directly autoregulatory like the endogenous locus. It is not clear to us how the intervening GAL4 activity would affect OVOB activity in the artificial circuit. Dampening? Feed-forward? Is there an effect on OVOA activity? Regardless, this result does not change our interpretation of the other OVO target genes.

6) The authors conclude with a model of how OVO may participate in the activation of transcription in embryonic pole cells. However, the authors did not carry out any experiments with pole cells that would support/test such a model. It may be more useful to end with a model that describes OVO's role in oogenesis, which is the experimental focus of the manuscript.

We did not complete any experiments in embryonic pole cells in this manuscript and base our discussion on the potential dynamics of OVO transcriptional control and our previous work showing maternal and zygotic OVO protein localization in the developing embryonic germline. Obviously, we are highly interested in this question and continue to work on the role of maternal OVO. We agree that we are extended too far and will remove the embryonic germ cell model in the figure. We will instead focus on the possible mechanisms of OVO gene regulation in light of the evidence we have shown in the adult ovary, as suggested.

Author Response

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

Reviewer #1:

Drawing on insights from preceding studies, the researchers pinpointed mutations within the spag7 gene that correlate with metabolic aberrations in mice. The precise function of spag7 has not been fully described yet, thereby the primary objective of this investigation is to unravel its pivotal role in the development of obesity and metabolic disease in mice. First, they generated a mice model lacking spag7 and observed that KO mice exhibited diminished birth size, which subsequently progressed to manifest obesity and impaired glucose tolerance upon reaching adulthood. This behaviour was primarily attributed to a reduction in energy expenditure. In fact, KO animals demonstrated compromised exercise endurance and muscle functionality, stemming from a deterioration in mitochondrial activity. Intriguingly, none of these effects was observed when using a tamoxifen-induced KO mouse model, implying that Spag7's influence is predominantly confined to the embryonic developmental phase. Explorations within placental tissue unveiled that mice afflicted by Spag7 deficiency experienced placental insufficiency, likely due to aberrant development of the placental junctional zone, a phenomenon that could impede optimal nutrient conveyance to the developing fetus. Overall, the authors assert that Spag7 emerges as a crucial determinant orchestrating accurate embryogenesis and subsequent energy balance in the later stages of life.

The study boasts several noteworthy strengths. Notably, it employs a combination of animal models and a thorough analysis of metabolic and exercise parameters, underscoring a meticulous approach. Furthermore, the investigation encompasses a comprehensive evaluation of fetal loss across distinct pregnancy stages, alongside a transcriptomic analysis of skeletal muscle, thereby imparting substantial value. However, a pivotal weakness of the study centres on its translational applicability. While the authors claim that "SPAG7 is well-conserved with 97% of the amino acid sequence being identical in humans and mice", the precise role of spag7 in the human context remains enigmatic. This limitation hampers a direct extrapolation of findings to human scenarios. Additionally, the study's elucidation of the molecular underpinnings behind the spag7-mediated anomalous development of the placental junction zone remains incomplete. Finally, the hypothesis positing a reduction in nutrient availability to the fetus, though intriguing, requires further substantiation, leaving an aspect of the mechanism unexplored.

Hence, in order to fortify the solidity of their conclusions, these concerns necessitate meticulous attention and resolution in the forthcoming version of the manuscript. Upon the comprehensive addressing of these aspects, the study is poised to exert a substantial influence on the field, its significance reverberating significantly. The methodologies and data presented undoubtedly hold the potential to facilitate the community's deeper understanding of the ramifications stemming from disruptions during pregnancy, shedding light on their enduring impact on the metabolic well-being of subsequent generations.

Thanks to this reviewer for their thoughtful analysis and commentary. Human mutations in SPAG7 are exceedingly rare (SPAG7 | pLoF (genebass.org)), potentially because of the deleterious effects of SPAG7-deficiency on prenatal development. This makes investigation into the causative effects of SPAG7 in humans challenging. There exist mutations in the SPAG7 region of the genome that are associated with BMI, but no direct coding variants within the spag7 gene itself have been studied.

We agree with the reviewer that the precise role of spag7 in the placenta remains unknown. However, given its robust expression and high protein levels in the placenta, including in key cells, such as the syncytiotrophoblast (https://www.proteinatlas.org/ENSG00000091640-SPAG7/tissue/Placenta), it is highly likely that spag7 is critical for normal placenta development and function. Multiple studies (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC9716072/) have recently shown that sperm associated RNAs play a critical role in embryonic and early placenta development. Our findings will provide the basis for future studies that can elucidate the role of spag7 in human placenta.