Author Response

Public Reviews:

Reviewer #1 (Public Review):

The authors observed a decline in autophagy and proteasome activity in the context of Milton knockdown. Through proteomic analysis, they identified an increase in the protein levels of eIF2β, subsequently pinpointing a novel interaction within eIF subunits where eIF2β contributes to the reduction of eIF2α phosphorylation levels. Furthermore, they demonstrated that overexpression of eIF2β suppresses autophagy and leads to diminished motor function. It was also shown that in a heterozygous mutant background of eIF2β, Milton knockdown could be rescued. This work represents a novel and significant contribution to the field, revealing for the first time that the loss of mitochondria from axons can lead to impaired autophagy function via eIF2β, potentially influencing the acceleration of aging. To further support the authors' claims, several improvements are necessary, particularly in the methods of quantification and the points that should be demonstrated quantitatively. It is crucial to investigate the correlation between aging and the proteins eIF2β and eIF2α.

Thank you so much for your comments. We will further investigate the correlation between aging and the proteins eIF2β and eIF2α and include the results in the revised version.

Reviewer #2 (Public Review):

In the manuscript, the authors aimed to elucidate the molecular mechanism that explains neurodegeneration caused by the depletion of axonal mitochondria. In Drosophila, starting with siRNA depletion of Milton and Miro, the authors attempted to demonstrate that the depletion of axonal mitochondria induces the defect in autophagy. From proteome analyses, the authors hypothesized that autophagy is impacted by the abundance of eIF2β and the phosphorylation of eIF2α. The authors followed up the proteome analyses by testing the effects of eIF2β overexpression and depletion on autophagy. With the results from those experiments, the authors proposed a novel role of eIF2β in proteostasis that underlies neurodegeneration derived from the depletion of axonal mitochondria.

The manuscript has several weaknesses. The reader should take extra care while reading this manuscript and when acknowledging the findings and the model in this manuscript.

The defect in autophagy by the depletion of axonal mitochondria is one of the main claims in the paper. The authors should work more on describing their results of LC3-II/LC3-I ratio, as there are multiple ways to interpret the LC3 blotting for the autophagy assessment. Lysosomal defects result in the accumulation of LC3-II thus the LC3-II/LC3-I ratio gets higher. On the other hand, the defect in the early steps of autophagosome formation could result in a lower LC3-II/LC3-I ratio. From the results of the actual blotting, the LC3-I abundance is the source of the major difference for all conditions (Milton RNAi and eIF2β overexpression and depletion). In the text, the authors simply state the observation of their LC3 blotting. The manuscript lacks an explanation of how to evaluate the LC3-II/LC3-I ratio. Also, the manuscript lacks an elaboration on what the results of the LC3 blotting indicate about the state of autophagy by the depletion of axonal mitochondria.

We agree with the reviewer that multiple ways exist to interpret the LC3 blotting for the autophagy assessment. Thus, we analyzed the levels of p62, an autophagy substrate, and found that milton knockdown caused elevated levels of p62 (Figure 2B). Together, these results suggest that autophagic degradation is lowered.

Another main point of the paper is the up-regulation of eIF2β by depleting the axonal mitochondria leads to the proteostasis crisis. This claim is formed by the findings from the proteome analyses. The authors should have presented their proteomic data with much thorough presentation and explanation. As in the experiment scheme shown in Figure 4A, the author did two proteome analyses: one from the 7-day-old sample and the other from the 21-day-old sample. The manuscript only shows a plot of the result from the 7-day-old sample, but that of the result from the 21-day-old sample. For the 21-day-old sample, the authors only provided data in the supplemental table, in which the abundance ratio of eIF2β from the 21-day-old sample is 0.753, meaning eIF2β is depleted in the 21-day-old sample. The authors should have explained the impact of the eIF2β depletion in the 21-day-old sample, so the reader could fully understand the authors' interpretation of the role of eIF2β on proteostasis.

Thank you for your comments. We will include more analyses of the proteomic data in the next version of our manuscript. In this study, we aimed to elucidate the mechanisms by which depletion of axonal mitochondria induces proteostasis disruption prematurely. Thus, we did not investigate the roles of differentially expressed proteins in proteostasis at 21-day-old in milton knockdown. Aging disrupts proteostasis via multiple pathways: eIF2β levels may be lowered by feedback of earlier changes or via interaction with other age-related changes at 21-day-old. We will include more discussion in the next version of our manuscript.

The manuscript consists of several weaknesses in its data and explanation regarding translation.

(1) The authors are likely misunderstanding the effect of phosphorylation of eIF2α on translation. The P-eIF2α is inhibitory for translation initiation. However, the authors seem to be mistaken that the down-regulation of P-eIF2α inhibits translation. Thank you for your comment. We understand that the phosphorylation of eIF2α is inhibitory for translation initiation, as we described in page 9, Line 312-314. We propose a model in which autophagic defects caused by milton knockdown is mediate by upregulation of eIF2β, however, we are not arguing that the translational suppression in milton knockdown is caused by a reduction in p-eIF2α. We found that milton knockdown causes an increase in eIF2β, and overexpression of eIF2β copied phenotypes of milton knockdown such as autophagic defects (Figure 5 and 6). We also found that the increase in eIF2β reduces the level of p-eIF2α (Supplemental Figure 2), thus, eIF2α phosphorylation in milton knockdown may be caused by an increase in eIF2β. However, the effects of upregulation of eIF2β on the function of eIF2 complex is not fully understood. The translational suppression in milton knockdown may be caused by disruption of eIF2 complex, while it is also possible that it is mediated by a function of eIF2β that is yet-to-be-determined, or mediated by the pathways other than eIF2. We will include more details in the revised version.

(2) The result of polysome profiling in Figure 4H is implausible. By 10%-25% sucrose density gradient, polysomes are not expected to be observed. The authors should have used a gradient with much denser sucrose, such as 10-50%. Thank you for pointing it out. We are sorry, it was a mistake. The gradient was actually 10-50%, and we described it wrong. We will correct it in the revised version.

(3) Also on the polysome profiling, as in the method section, the authors seemed to fractionate ultra-centrifuged samples from top to bottom and then measured A260 by a plate reader. In that case, the authors should have provided a line plot with individual data points, not the smoothly connected ones in the manuscript. Thank you for pointing it out. We will replace the graph.

(4) For both the results from polysome profiling and puromycin incorporation (Figure 4H and I), the difference between control siRNA and Milton siRNA are subtle, if not nonexistent. This might arise from the lack of spatial resolution in their experiment as the authors used head lysate for these data but the ratio of Phospho-eIF2α/eIF2α only changes in the axons, based on their results in Figure 4E-G. The authors could have attempted to capture the spatial resolution for the axonal translation to see the difference between control siRNA and Milton siRNA.

Thank you for your comment. A new set of experiments with technical challenges will be required to capture the spatial resolution for the axonal translation. We will work on it and hope to achieve it in the future.

Author Response

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

Reviewer #2 (Recommendations For The Authors):

I would like to thank the authors for their comments. However, my request for additional experiments to consolidate this manuscript and text changes have not been addressed (point 1 and point 2), which I believe are essential for completion of this manuscript.

The reviewer raised the question about the relevant substrates of PARG in S-phase cells (point 1). As we explained in our previous response, the most important substrate of PARG is PARP1, since we observed increased chromatin-associated PARP1 and PARylated PARP1 in cells with PARG depletion. Moreover, PARP1 or PARP1/2 depletion rescued cell lethality caused by PARG depletion. These data strongly suggest that PARP1 is the major substrate of PARG in S phase cells. Of course, PARG may have additional substrates. In the future, we will perform proteomics experiments as suggested by this reviewer to identify additional PARG substrates, which may reveal new roles of PARG in S phase progression.

The reviewer also suggested us to re-organize our manuscript (point 2). However, we prefer to keep the manuscript as it is, since this is how the project evolved. The other reason we would like to share with the readers is the challenge to validate KO cells. This is an important lesson we learned from this study. We hope that this will raise the awareness of hypomorphic mutant cells we often use to draw conclusions about gene functions and/or genetic interactions. We understand that the current flow of our manuscript may bring some confusion. To avoid it, we included additional explanations at the beginning of this manuscript to draw attention to the readers that our initial KO cells may not be complete PARG KO cells, i.e. they may have residual PARG activity. We also included additional discussion of this important point in the Discussion section.

Moreover, WB analysis of PARG KO clones is inconclusive, as the additional prominent band at 50 kDa could be a degradation product. The authors should check PARG levels are localization by IF, which allows detection of intact proteins and their cellular localizations, since the shorter isoform should be localized in the cytosol. WB with PARG isoforms is missing important information regarding Mw of the PARG constructs and Mw labels of western blots, which makes is difficult to evaluate this data and compare to KO. Ideally, KO and PARG isoform samples should be all on one gel for proper comparison with different antibodies.

We appreciate the concerns raised by this reviewer. We agree that the additional prominent band at 50kDa could be a degradation product. As we explained in our previous response, despite using several PARG antibodies, we could not draw a clear conclusion which functional isoforms or truncated forms were expressed in our PARG KO cells.

Immunostaining experiments may not be more conclusive, since IF experiments rely on the same antibodies for recognizing endogenous PARG. Additionally, even a protein mainly localizes in the cytosol, we cannot exclude the possibility that a small fraction of this protein may localize in nuclei and have nuclear functions.

Instead, as we presented in our manuscript, we used a biochemical assay to measure PARG activity in cell lysate and showed that our initial PARG KO cells still have residual PARG activity. However, we could not detect any PARG activity in our complete/conditional PARG KO cells (cKO cells; these cells can only survive in the presence of PARP inhibitor). These data strongly suggest that PARG is essential for cell survival.

Author Response

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

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) The author should evaluate the possibility of naturally occurring arrhythmia due to the geometry of the tissues, by using voltage or calcium dye.

Answer: We thank the reviewer for this suggestion. We have performed new experiments using a voltage-sensitive fluorescent dye (i.e. FluoVolt) with data reported in the new Figure 4 + new results section “arrhythmia analysis”. Briefly, we found that our ring-shaped tissues are compatible with live fluorescence imaging. We were then able to show that our cardiac tissues beat regularly, without naturally occurring arrhythmias or extra beats. We could not detect any re-entrant waves in our tissues in the conditions offered by the speed of our camera. A specific paragraph has also been added to the discussion.

(2) There is only 50% survival after 20 days of culture in the optimized seeding group. Is there any way to improve it? The tissues had two compartments, cardiac and fibroblast-rich regions, where fibroblasts are responsible for maintaining the attachment to the glass slides. Do the cardiac rings detach from the glass slides and roll up? The SD of the force measurement is a quarter of the value, which is not ideal with such a high replicate number.

Answer: This paper report seminal data that will serve as a foundation for further use of the platform. We are currently expanding to other cell lines with improvement in survival (see https://insight.jci.org/articles/view/161356). We confirm that the rings do not detach. The pillar was specifically designed to avoid this (See figure 1B).

As the platform utilizes imaging analysis to derive contractile dynamics, calibration should be done based on the angle and the distance of the camera lens to the individual tissues to reduce the error. On the other hand, how reproducible of the pillars? It is highly recommended to mechanically evaluate the consistency of the hydrogel-based pillars across different wells and within the wells to understand the variance.

Answer: We propose a system and a measurement method that do not need calibration. Contraction amplitude is expressed as a ratio between the contracted / relaxed areas (See figure 3 A). There is thus no influence of the distance of the camera lens.

In order to evaluate the consistency of the mechanical properties of the hydrogel, we reproduced the experiment pictured in Figure1-Supplement 1, and measured the Young’s Modulus of three different gel solutions on different days. In the three experiments performed, we found values of 10.0-12.2 kPa, resulting in a final average value of 11.2 (+/- 0.6) kPa, coherent with the value reported in the article. We are therefore confident that the mechanical properties are consistent across and within wells. More extensive mechanical characterization of the molded gels would require the access to an Atomic Force Microscope (AFM), and is considered in the future.

The author should address the longevity and reproducibility issues, by working on the calibration of camera lens position/distance to tissues and further optimizing the seeding conditions with hydrogels such as collagen or fibrin, and/or making sure the PEG gels have high reproducibility and consistency.

Answer: This paper report seminal data that will serve as a foundation for further use of the platform. This platform (including the design, approach and choice of polymers) allows a fast and reproducible formation of an important number of cardiac tissues (up to 21 per well in a 96-well format, meaning a potential total of about 2,000 tissues) with a limited number of cells.

(3) The evaluation of the arrhythmia should be more extensively explained and demonstrated.

Answer : See answer to comment 1

(4) The results of isoproterenol should be checked as non-paced tissues should have increased beating frequency with increasing dosages. Dofetilide does not typically have a negative inotropic effect on the tissues. Please check on the cell viability before and after dosing

Answer : We agree with this reviewer on the principle. However, we have repeated the experiments and we confirm our results, i.e. increasing concentrations of isoproterenol induced a trend towards increase in the contraction force and significantly increased contraction and relaxation speeds without change in the beat rate (Figure 5C). We do not have a definitive explanation for this observation. Our hypothesis is that this increase in contraction and relaxation speeds induced by isoproterenol is translated, on average in our study, into an increase in contractile force rather than in an increase in contraction frequency. This may depend on the cell line used, and is very well illustrated in a recent paper from Mannhardt and colleagues (Stem cell reports. 2020; 15(4):983–998). Of the 10 different cell lines tested in engineered heart tissues, all show an increase in contraction and relaxation speeds after isoproterenol administration, but this is translated either into an increase in contractile force (4 cell lines) or into a shortening of the beat (3 cell lines), and only 2 cell lines show an increase in both parameters. Indeed, since iPSC-CMs are immature cardiac cells, it is rare to obtain a positive force-frequency relationship without any maturation medium or mechanical or electrical training. We agree that above a concentration of 10nM, dofetilide shows cardiotoxicity in our tissues as tissues completely stop beating.

Reviewer #2 (Recommendations For The Authors):

In addition to the general comments in the public review, I have the following specific suggestions to the authors, that would help improve the manuscript.

(1) Please describe the protocol for preparation of cardiac rings (shown in Figure 1C) in more detail. In particular, please describe how the tissues were transferred from the mold into the 96-well plate and how are they positioned and characterized during the study.

Answer: There is no transfer of the tissues as they directly form in the well, that is pre-equipped with the molded PEG gel (See Figure 1B and methods section). The in situ analysis is a strong asset of this platform.

(2) Please clarify the timepoints in this study. The overall schematic in Figure 1 C shows that the rings were formed on day 22 and then studied for 14 days, while Figure 2B shows data over 20 days following seeding, and Figure 3 shows data 14 days after seeding. It appears that these were separate studies (optimization of myocyte/fibroblast ratio followed by the main study.

Answer: Figure 1C is showing the timeline including the cardiomyocytes differentiation. hiPSC-CMs are indeed seeded in the wells 22 days after starting the differentiation, which represent the Day0 for tissue formation. We apologize for the confusion.

(3) Please explain if the number of rings per well (Figure 2) was used as the only criterion for selecting the myocyte/fibroblast ratio, and if so, why. Were these rings also characterized for their structural and contractile properties?

Answer: Figure 2 supplement 1 report the contractility data according to the different tested ratios, and show no differences. The number for generated ring-shaped tissues was indeed the only criterion retained.

(4) Please provide rationale for using the dermal rather than cardiac fibroblasts.

Answer: We had previous experience generating EHTs using dermal fibroblasts which are easier to obtain commercially. Our approach could in theory also work using cardiac fibroblasts, which we have not tested in the present study.

(5) Figure 2 panels C-E show an interesting segregation of cardiomyocytes into a thin cylindrical layer that does not appear to contain fibroblasts and a shorter and thicker cylinder containing fibroblasts mixed with occasional myocytes. Please specify at which time point this structure forms, and how does it change over time in culture? At which time point were the images taken? It would be helpful to include serial images taken over 1-14 days of study.

Answer: We thank the reviewer for this interesting comment. We have performed additional immunostainings (reported in Figure 2 supplement 3) on tissues at Day 1 and day 7 after seeding. The segregation appears in the 7 first days. It appears that 1 day after seeding the fibroblasts are not yet attached, although the cardiac fiber has already started to be formed. Seven days after seeding, fibroblasts are fully spread and attached, and the contractile ring is formed and well-aligned. Brightfield images are reported in Figure 1E.

(6) In the cardiomyocyte region (Figure 2D) the cells staining for troponin seem to be only at the surfaces. The thickness of the layer is only about 30-40 µµ, so one would assume that cell viability was not an issue. Please specify and discuss the composition of this region.

Answer: We agree but we think this is a technical issue as at the center of the tissue, tissue thickness will limit laser penetration, although at the surface (inner our outer), the laser infiltrates easily between the tissue and the PEG. Moreover, we see on the zoomed view of the tissue in Figure 2 Supplement 2 that we have a staining inside the cardiac fiber, which just appears less strong due to tissue thickness.

(7) Please also discuss segregation in terms of possible causes and the implications of apparently very limited contact between the two cell types, i.e., how representative is this two-region morphology of native heart tissue. Also, it would be interesting to know how the segregation has changed with the change in myocyte/fibroblast ratio.

Answer: We are not sure there is a very limited contact as the use of fibroblasts is critical to ensure the formation of tissues (i.e. no tissues can be formed if we avoid the use of fibroblasts). We agree that these ring-shaped cardiac tissues are not especially representative of a native heart tissue in terms of interactions between several cell types. They were developed as a surrogate for physiopathological and pharmacological experiments (see a recent application in https://insight.jci.org/articles/view/161356)

(8) There is interest and demonstrated ability to culture engineered cardiac tissues over longer periods of time. Please comment what was the rationale for selecting 14-day culture and if the system allows longer culture durations.

Answer: In line with this comment, we have studied the contractile parameters of our rings 28 days after seeding and compared to their contractile parameters at D14. We found a slight increase for all the parameters, which is significant for the maximum contraction speed. Nevertheless, the data is much more variable and the number of tissues is lower (29 for D14 against 17 for D28). Therefore, we demonstrated that long-term culture of our tissues is possible, however not yet optimized. Hence, the following physiological and pharmacological tests have been done at D14.

(9) Figure 3 documents the development of contractile parameters over 14 days of culture. Would it be possible to replace the arbitrary units with the actual values? Also, would it be possible to include the corresponding images of the rings taken at the same time points, to show the associated changes in ring morphologies.

Answer: Contraction amplitude is expressed as a ratio between the contracted / relaxed areas (See figure 3 A): it is a ratio, thus without unit. Corresponding images can be seen in Figure 1 E.

(10) The measured contraction stress, strain, and the speeds of contraction and relaxation improve from day 1 to day 7 and then plateau (Figure 3, Supplemental Figure 3. Please discuss this result.

Answer: The new immunostainings performed on tissues at Day 1 and Day 7 show the progressive alignment of the cardiomyocytes and the muscular fibers, with an almost complete organization at Day 7.

(11) The beating frequency does not appear to markedly change over time, while Figure 3B shows strong statistical significance (***) throughout the 14-day period. Please check/confirm.

Answer: We confirm this result.

(12) Please comment on the lack of effect of isoproterenol on beating frequency.

Answer: We agree with this reviewer on the principle. However, we have repeated the experiments and we confirm our results, i.e. increasing concentrations of isoproterenol induced a trend towards increase in the contraction force and significantly increased contraction and relaxation speeds without change in the beat rate (Figure 5C). We do not have a definitive explanation for this observation. Our hypothesis is that this increase in contraction and relaxation speeds induced by isoproterenol is translated, on average in our study, into an increase in contractile force rather than in an increase in contraction frequency. This may depend on the cell line used, and is very well illustrated in a recent paper from Mannhardt and colleagues (Stem cell reports. 2020; 15(4):983–998). Of the 10 different cell lines tested in engineered heart tissues, all show an increase in contraction and relaxation speeds after isoproterenol administration, but this is translated either into an increase in contractile force (4 cell lines) or into a shortening of the beat (3 cell lines), and only 2 cell lines show an increase in both parameters. Indeed, since iPSC-CMs are immature cardiac cells, it is rare to obtain a positive force-frequency relationship without any maturation medium or mechanical or electrical training.

(13) Please compare the contractile function of cardiac tissues measured in this study with data reported for other iPSC-derived tissue models.

Answer : A specific paragraph tackles this aspect in the discussion

Author Response

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

Public Reviews

We thank the reviewers for their insightful comments and helpful suggestions that allowed us to improve the manuscript.

Reviewer #1:

Thermogenic adipocyte activity associate with cardiometabolic health in humans but decline with age. Identifying the underlying mechanisms of this decline is therefore highly important.

To address this task, Holman and co-authors investigated the effects of two major determinants of thermogenic activity: cold, which induce thermogenic de novo differentiation as well as conversion of dormant thermogenic inguinal adipocytes: and aging, which strongly reduce thermogenic activity. The authors study young and middle-aged mice at thermoneutrality and following cold exposure.

Using linage tracing, the authors conclude that the older group produce less thermogenic adipocytes from progenitor differentiation. However, they found no differences between thermogenic differentiation capacity between the age groups when progenitors are isolated and differentiated in vitro. This finding is consistent with previous findings in humans, demonstrating that progenitor cells derived from dormant perirenal brown fat of humans differentiate into thermogenic adipocytes in vitro. Taken together, this underscores that age-related changes in the microenvironment rather than autonomous alterations in the ASPCs explain the age-related decline in thermogenic capacity. This is an important finding in terms of identifying new approaches to switch dormant adipocytes into an active thermogenic phenotype.

To gain insight into the age-related changes, the authors use single cell and single nuclei RNA sequencing mapping of their two age groups, comparing thermoneutral and cold conditions between the two groups. Interestingly, where the literature previously demonstrated that de novo lipogenesis (DNL) occurs in relation to thermogenic activation, the authors show that DNL in fact is activated in a white adipocyte cell type, whereas the beige thermogenic adipocytes form a separate cluster.

Considering recent findings, that adipose tissue contains several subtypes of ASPCs and adipocytes, mapping the changes at single cell resolution following cold intervention provides an important contribution to the field, in particular as an older group with limited thermogenic adaptation is analyzed in parallel with a younger, more responsive group. This model also allowed for detection of microenvironment as a determining factor of thermogenic response.

The use of only two time points (young and middle-aged) along the aging continuum limits the conclusions that can be made on aging as the only driver of the observed differences between the groups. It should for example be noted that the older mice had higher weights and larger fat depots, thus the phenotype is complex and this should be taken into consideration when interpreting the data.

In conclusion, this study provides an important resource for further studies on how to reactivate dormant thermogenic fat and potentially improve metabolic health.

(1) The authors claim "Aging impairs cold-induced beige adipogenesis and adipocyte metabolic reprogramming". It is previously established in humans that aging strongly associate with a decline in thermogenic capacity. With this in mind, it is easy to accept that the reduced browning observed in the older group is due to age. However, the older group also have larger adipose depots, which also can be a confounding factor. I, therefore, recommend bringing this into the discussion and putting more focus on the complexity of the phenotype. For example, it could be discussed whether the de novo lipogenesis less due to that the adipocytes of older mice is already filled with more lipids. Additional time points along the aging continuum would be needed to make a strong conclusion about age as the determinant, but even so, aging is complex and further definitions and discussion would be needed.

We agree with the reviewer regarding the confounding effect of body weight changes. We have added a paragraph to the discussion (pasted below) to comment on the complexity of the phenotype and the contributing role of linked changes in body weight/composition.

“Aging is a complex process, and unsurprisingly, many pathways have been linked to the aging-related decline in beiging capacity. For example, increased adipose cell senescence, impaired mitochondrial function, elevated PDGF signaling and dysregulated immune cell activity during aging diminish beige fat formation (Benvie et al., 2023; Berry et al., 2017; Goldberg et al., 2021; Nguyen et al., 2021). Of note, older mice exhibit higher body and fat mass, which is associated with metabolic dysfunction and reduced beige fat development. While the effects of aging and altered body composition are difficult to separate, previous studies suggest that the beiging deficit in aged mice is not solely attributable to changes in body weight (Rogers et al., 2012). Further studies, including additional time points across the aging continuum may help clarify the role of aging and ascertain when beiging capacity decreases.”

(2) The study would gain from more comparisons to existing human studies and discussion on the translation potential of the findings. For example, how does the adipocyte subtypes identified in the current study translate to subtypes identified in human adipose tissue (e.g. Emont et al).

We analyzed the human adipose tissue atlas from Emont et al. 2022 (PMID: 35296864). We did not find any obvious homologous human adipocyte subtypes. However, this and other available human single cell studies have not investigated the effects of cold exposure on white adipose tissue depots, which may be necessary to reveal DNL-high and especially beige adipocytes.

(3) The group has contributed multiple studies demonstrating that Prdm16 is a major inducer of a thermogenic phenotype, and the literature shows that Prdm16 promote a thermogenic phenotype in favour of a fibrogenic aging phenotype. It would therefore be interesting to see how Prdm16 is regulated in the current data set, across adipocytes subtypes, age groups and temperature conditions.

We thank the reviewer for this comment. Previous studies showed that PRDM16 protein and not mRNA levels are downregulated during aging (Wang et al., 2019, Cell Metab, PMID: 31155495; Wang et al., 2022, Nature, PMID: 35978186). Consistent with this, we did not observe an agingassociated reduction in Prdm16 mRNA levels in adipocytes in our dataset. We did observe enrichment of Prdm16 mRNA levels in beige adipocytes relative to other adipocyte clusters. We included these data in Fig. 5F.

(4) In Figure 1, it is difficult to understand why the 6 weeks cold exposure is not shown in relation to the thermoneutrality, 3 days and 2-week cold exposure? It would be useful to have this in the same graph relating the levels and showing all four marker genes for all time points.

These experiments were done at different times using separate groups of mice. We have now clarified this in the figure legend.

(5) The older mice had larger inguinal fat depots, suggesting more lipids stored. The morphology of adipose tissue has previously been shown to be modulated by cold acclimation and is also the main similarity between brown adipose tissue in adult humans and young mice beige adipose tissue. Fig S2b suggests smaller adipocytes in the young group. It would also be useful, for comparison to published data, if authors show tissue sections with H&E of their model.

Good point. We added panels showing H&E staining of serial iWAT sections, showing changes in tissue morphology across age and temperature conditions (Figure S1F).

(6) The authors use t-tests to compare the differences induced by e.g. cold or min vs max cell culture media etc, within each age group. However, in my opinion, a two-way Anova with post-tests would be more informative as this would allow for testing the effects of the two age categories on any quantitative variable and allow for addressing whether there is an interaction between the categories.

Following the reviewer’s recommendation, we applied two-way ANOVA with a Tukey correction for multiple comparisons for categorical comparisons with different age groups and conditions. P values from all significant multiple comparison tests are now included within the methods section.

(7) In Figure 5F, please include Adipoq expression between clusters and please add a reference to why Nnat is considered a canonical white adipocyte marker.

We added Adipoq to the violin plot in Figure 5F, showing differential expression across adipocyte clusters. We included a line in the results section to highlight this observation:

“Interestingly, Adiponectin (Adipoq) was differentially expressed across adipocyte clusters, with higher levels in Npr3-high and DNL-high cells.”

We removed “canonical” and added references for Nnat and Lep as white marker genes.

(8) After 14 days of cold exposure, it looks like the DNL high population divides into two populations, did the authors explore if there was any differences between these clusters?

We also noticed this apparent division and explored this question. However, upon increasing the resolution for clustering and splitting the DNL high population, there were no obvious differentially expressed genes that defined the two subclusters. Thus, we opted to keep them together.

(9) As cold treatment transform a subset of cells, can authors perform a data-driven analysis to visualize the directions in their single nuclei data sets by using monocle pseudotime and/or velocity analyses?

This is a good question. We spent a long time trying to address this question using several trajectory and pseudotime analysis methods, including Velocity (scVelo), Slingshot and Dynoverse. Unfortunately, we were unable to obtain concordant results using at least two different methods and felt that the analyses were unreliable.

Reviewer #2:

This manuscript focused on why aging leads to decreased beiging of white adipose tissue. The authors used an inducible lineage tracing system and provided in vivo evidence that de novo beige adipogenesis from Pdgfra+ adipocyte progenitor cells is blocked during early aging in subcutaneous fat. Single-cell RNA sequencing of adipocyte progenitor cells and in vitro assays showed that these cells have similar beige adipogenic capacities in vitro. Single-cell nucleus RNA sequencing of mature adipocytes indicated that aged mice have more Npr3 high-expressing adipocytes in the subcutaneous fat from aged mice.

Meanwhile, adipocytes from aged mice have significantly lower expression of genes involved in de novo lipogenesis, which may contribute to the declined beige adipogenesis.

The mechanism that leads to age-related impairment of white adipose tissue beiging is not very clear. The finding that Pdgfra+ adipocyte progenitor cells contribute to beige adipogenesis is novel and interesting. It is more intriguing that the aging process represses Pdgfra+ adipocyte progenitor cells from differentiating into beige adipocytes during cold stimulation. Mature adipocytes that have high de novo lipogenesis activity may support beige adipogenesis is also novel and worth further pursuing. The study was carried out with a nice experimental design, and the authors provided sufficient data to support the major conclusions. I only have a few comments that could potentially improve the manuscript.

(1) It is interesting that after three days of cold exposure, aged mice also have much fewer beige adipocytes. Is de novo adipogenesis involved at this early stage? Or does the previous beige adipocyte that acquired white morphology have a better "reactivation" in young mice? It would be nice if the author could discuss the possibilities.

This is a good question. We did not evaluate beige adipogenesis at the 3d timepoint. However, a previous study demonstrates that 3d of cold exposure is sufficient to promote de novo beige adipogenesis (Wang et al., Nat Med. 2013, PMID: 23995282). We observed that beige adipogenesis from Pdgfra+ cells are a relatively minor contributor to beige adipocyte development, even after long term cold exposure in young mice. Based on these data, we presume that beige adipocyte activation (or re-activation) is the dominant mechanism for beige adipocyte development.

To clarify this point, we have included the following lines in the manuscript:

“Previous studies in mice using an adipocyte fate tracking system show that a high proportion of beige adipocytes arise via the de novo differentiation of ASPCs as early as 3 days of cold (Wang et al., 2013).”

“Based on these findings, we presume that mature (dormant beige) adipocytes serve as the major source of beige adipocytes in our cold-exposure paradigm. However, long-term cold exposure also recruits smooth muscle cells to differentiate into beige adipocytes; a process that we did not investigate here (Berry et al., 2016; Long et al., 2014; McDonald et al., 2015; Shamsi et al., 2021).”

(2) Is the absolute number of Pdgfra+ cells decreased in aged mice? It would be nice to include quantifications of the percentage of tomato+ beige adipocytes in total tomato+ cells to reflect the adipogenic rate.

We presented FACS quantification of tdTomato+/Pdgfra+ cells in Fig. 2B. We added a graph showing the percentage of Pdgfra+ cells of total live, lin- cells in adipose tissue; this showed no difference between young and aged mice. We did not perform FACS quantification of tdTomato+ beige adipocytes due to the technical challenges with sorting adipocytes. Quantification of total tdTomato+ cells was also unreliable and inconsistent due to the widespread labeling of fibroblasts, blood vessels, along with traced adipocytes. Thus, we did not include this analysis.

(3) Line 112, the sentence seems to be not finished.

This has been corrected.

Author Response

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

Response to Reviewers’ Public Comments

We are grateful for the reviewers’ comments. We have modified the manuscript accordingly and detail our responses to their major comments below.

(1) Reviewer 2 was concerned that transformation of continuous functional data into categorical form could reduce precision in estimating the genetic architecture.

We agree that transforming continuous data into categories may reduce resolution, but it also improves accuracy when the continuous data are affected by measurement noise. In our dataset, many genotypes are at the lower bound of measurement, and the variation in measured fluorescence among these genotypes is largely or entirely caused by measurement noise. By transforming to categorical data, we dramatically reduced the effect of this noise on the estimation of genetic effects. We modified the results and discussion sections to address this point.

(2) Reviewer 2 asked about generalizability of our findings.

Because our paper is the first use of reference-free analysis of a 20-state combinatorial dataset, generalizability is at this point unknown. However, a recent manuscript from our group confirms the generality of the simplicity of genetic architecture: using reference-free methods to analyze 20 published combinatorial deep mutational scans, several of which involve 20-state libraries, we found that main and pairwise effects account for virtually all of the genetic variance across a wide variety of protein families and types of biochemical functions (Park Y, Metzger BPH, Thornton JW. 2023. The simplicity of protein sequence-function relationships. BioRxiv, 2023.09.02.556057). Concerning the facilitating effect of epistasis on the evolution of new functions, we speculate that this result is likely to be general: we have no reason to think that the underlying cause of this observation – epistasis brings genotypes with different functions closer in sequence space to each other and expands the total number of functional sequences – arises from some peculiarity of the mechanisms of steroid receptor DBD folding or DNA binding. However, we acknowledge that our data involve sequence variation at those sites in the protein that directly mediate specific protein-DNA contact; it is plausible that sites far from the “active site” may have weaker epistatic interactions and therefore have weaker effects on navigability of the landscape. We have addressed these issues in the discussion.

(3) Reviewer 3 asked “in which situation would the authors expect that pairwise epistasis does not play a crucial role for mutational steps, trajectories, or space connectedness, if it is dominant in the genotype-phenotype landscape?”

The question addressed in our paper is not whether epistasis shapes steps, trajectories or connectedness in sequence space but how it does so and what its particular effects are on the evolution of new functions. The dominant view in the field has been that the primary role of epistasis is to block evolutionary paths. We show, however, that in multi-state sequence space, epistasis facilitates rather than impedes the evolution of new functions. It does this by increasing the number of functional genotypes and bringing genotypes with different functions closer together in sequence space. This finding was possible because of the difference in approach between our paper and prior work: most prior work considered only direct paths in a binary sequence space between two particular starting points – and typically only considering optimization of a single function – whereas we studied the evolution of new functions in a multi-state amino acid space, under empirically relevant epistasis informed by complete combinatorial experiments. The result is a clear demonstration that the net effect of real-world levels of epistasis on navigability of the multidimensional sequence landscape is to make the evolution of new functions easier, not harder.

(4) Reviewer 3 asked for “an explanation of how much new biological results this paper delivers as compared with the paper in which the data were originally published.”

Starr 2017 did not use their data to characterize the underlying genetic architecture of function by estimating main and epistatic effects of amino acid states and combinations; it also did not evaluate the importance of epistasis in generating functional variants, determining the transcription factor’s specificity, or shaping evolutionary navigability on the landscape.

(5) Reviewer 3 requested an explanation of how the results would have been (potentially) different if a reference-based approach were used, and how reference-based analysis compares with other reference-free approaches to estimating epistasis.

This topic has been covered in detail in a recent manuscript from our group (Park et al. Biorxiv 2023.09.02.556057). Briefly, reference-free approaches provide the most efficient explanation of an entire genotype-phenotype map, explaining the maximum amount of genetic variance and reducing sensitivity to experimental noise and missing genotypes compared to reference-based approaches. Reference-based approaches tend to infer much more epistasis, especially higher-order epistasis, because measurement error and local idiosyncrasy near the wild-type sequence propagate into spurious high-order terms. Reference-based analyses are appropriate for characterizing only the immediate sequence neighborhood of a particular “wild-type” protein of interest. Reference-free approaches are therefore best suited to understanding genotype-phenotype landscapes as a whole. We have clarified these issues in the revised discussion.

(6) Reviewer 3 suggested that the comparison between the full and main-effects-only model should involve a re-estimation of main effects in the latter case.

This is indeed what we did in our analysis. We have clarified the description in the results and methods sections to make this clear.

(7) Reviewer 3 asked about the applicability of the approach to data beyond those analyzed in the present study and requirements to use it.

Our approach could be used for any combinatorial DMS dataset in which the phenotypic data are categorical (or can be converted to categorical form). Complete sampling is not required: a virtue of reference-free analysis is that by averaging the estimated effects of states and combinations over all variants that contain them, reference-free analysis is highly robust to missing data (except at the highest possible order of epistasis, where only a single variant represents a high-order effect) as long as variant sampling is unbiased with respect to phenotype. All the required code are publicly available at the github link provided in this manuscript. We have also described a general form of reference-free analysis for continuous data and applied it to 20 protein datasets in a recent publication (Park et al. Biorxiv 2023.09.02.556057).

(8)Reviewer 3 suggested that the text could be shortened and made less dense.

We agree and have done a careful edit to streamline the narrative.

Response to Reviewers’ Non-Public Recommendations

(1) Reviewer 1 noted that specific epistatic effects might in some cases produce global nonlinearities in the genotype-phenotype relationship. They then asked how our results might change if we did not impose a nonlinear transformation as part of the genotype-phenotype model. The reviewer’s underlying concern was that the non-specific transformation might capture high-order specific epistatic effects and thus reducing their importance.

Because our data are categorical, we required a model that characterizes the effect of particular amino acid states and combinations on the probability that a variant is in a null, weak, or strong activation class. A logistic model is the classic approach to this kind of analysis. The model structure assumes that amino acid states and combinations have additive effects on the log-odds of being in one functional class versus the lower functional class(es); the only nonlinear transformation is that which arises mathematically when log-odds are transformed into probability through the logistic link function. Thinking through the reviewer’s comment, we have concluded that our model does not make any explicit transformation to account for nonlinearity in the relationship between the effects of specific sequence states/combinations and the measured phenotype (activation class). If additional global nonlinearities are present in the genotype-phenotype relationship – such as could be imposed by limited dynamic range in the production of the fluorescence phenotype or the assay used to measure it – it is possible that the sigmoid shape of the logistic link function may also accommodate these nonlinearities. We have noted this part in the revised manuscript.

(2) Reviewer 1 observed that our model seems to prefer sets of several pairwise interactions among states across sites rather than fewer high-order interactions among those same states.

This finding arises because the pattern of phenotypic variation across genotypes in our dataset is consistent with that which would be produced by pairwise interactions rather than by high-order interactions. In a reference-free framework, these patterns are distinct from each other: a group of second-order terms cannot fit the patterns produced by high-order epistasis, and high-order terms cannot fit the pattern produced by pairwise interactions. Similarly, main-effect terms cannot fit the pattern of phenotypes produced by a pairwise interaction, and a pairwise epistatic term cannot fit the pattern produced by main effects of states at two sites. For example, third-order terms are required when the genotypes possessing a particular triplet of states deviate from that expected given all the main and second-order effects of those states; this deviation cannot be explained by any combination of first- and second-order effects.

We explain this point in detail in our recent manuscript (Park Y, Metzger BPH, Thornton JW. 2023. The simplicity of protein sequence-function relationships. BioRxiv, 2023.09.02.556057) and we summarize it here. Consider the simple example of two sites with two possible states (genotypes 00, 01, 10, and 11). If there are no main effects and no pairwise effects, this architecture will generate the same phenotype for all four variants – the global average (or zero-order effect). If there are pairwise effects but no main effects, this architecture will generate a set of phenotypes on which the average phenotype of genotypes with a 0 at the first site (00 and 01) equals the global average – as does the average of those with 0 at the second site (00 and 10). The epistatic effect causes the individual genotypes to deviate from the global average. This pattern can be fit only by a pairwise epistatic term, not by first-order terms. Conversely, if there are main effects but no pairwise effects, then the average phenotype of genotypes 00 and 01 will deviate from the global average (by an amount equal to the first-order effect), as will the average of (00 and 10): the phenotype of each genotype will be equal to the sum of the relevant first-order effects for the state it contains. This pattern cannot be fit by second-order model terms. The same logic extends to higher orders: a cluster of second-order terms cannot explain variation generated by third-order epistasis, because third-order variation is by definition is the deviation from the best second-order model.

(3) Reviewer 1 suggested several places in the text where citations to prior work would be appropriate.

We appreciate these suggestions and have modified the manuscript to refer to most of these works.

(4) Reviewer 1 pointed to the paper of Gong et al eLife 2013 and asked whether it is known how robust the proteins in our study are to changes in conformation/stability compared to other proteins, and whether this might impact the likelihood of observing higher-order epistasis in this system.

The DBDs that we study here are very stable, and previous work shows that mutations affect DNA specificity primarily by modifying the DBD’s affinity rather than its stability (McKeown et al., Cell 2014). Additionally, Gong et al.’s findings pertain to a globally nonlinear relationship between stability and function, which arises from the Boltzmann relationship between the energy of folding and occupancy of the folded state. Because our data are categorical – based on rank-order of measured phenotype rather than fluorescence as a continuous phenotype – the kind of global nonlinearity observed in Gong’s study are not expected to produce spurious estimates of epistasis in our work. We have modified the discussion to discuss the point.

(5) Reviewer 1 asked a) why the epistatic models produce landscapes on which variants have fewer neighbors on average than main-effects only models and b) why the average distance from all ERE-specific nodes to all SRE-specific nodes is greater with epistasis (but the average distance from ERE to nearest SRE is lower with epistasis).

In the main effects-only landscape, the functional genotypes are relatively similar to each other, because each must contain several of the states that contribute the most to a positive genetic score. Moreover, ERE-specific nodes are similar to each other, and SRE-specific nodes are similar to each other, because each must contain one or more of a relatively small number of specificity-determining states. When epistasis is added to the genetic architecture, two things happen: 1) more genotypes become functional because there are more combinations that can exceed the threshold score to produce a functional activator and 2) these additional functional variants are more different from each other – in general, and within the classes of ERE- or SRE-specific variants – because there are now more diverse combinations of states that can yield either phenotype. As a result, a broader span of sequence space is occupied, but ERE- and SRE-specific variants are more interspersed with each other. This means that the average distance between all pairs of nodes is greater, and this applies to all ERE-SRE pairs, as well. However, the interspersing means that the closest single SRE to any particular ERE is closer than it was without epistasis. We have added this explanation to the main text.

(6) Reviewer 2 asked us to explain why average path length increases with pairwise epistasis as the strength of selection for specificity increases.

This behavior occurs because of the existence of a local peak in the pairwise model. Genotypes on this peak contained few connections to other genotypes, all of which were less SRE specific. Thus, with strong selection, i.e. high population size, the simulations became stuck on the local peak, cycling among the genotypes many times before leaving, resulting in a large increase in the mean step number. As shown in the rest of the figure, when the longest set of paths are removed, there are still differences in the average number of steps with and without epistasis. This issue is described in the methods section.

(7) Reviewers made several suggestions for clarity in the text and figures.

We have modified the paper to address all of these comments.

(8) Reviewer 3 stated that the code should be available.

The code is available at https://github.com/JoeThorntonLab/DBD.GeneticArchitecture.

Author Response

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

Reviewer #1 (Public Review):

Summary:

The authors were trying to understand the relationship between the development of large trunks and longirrostrine mandibles in bunodont proboscideans of Miocene, and how it reflects the variation in diet patterns.

Strengths:

The study is very well supported, written, and illustrated, with plenty of supplementary material. The findings are highly significant for the understanding of the diversification of bunodont proboscideans in Asia during Miocene, as well as explaining the cranial/jaw disparity of fossil lineages. This work elucidates the diversification of paleobiological aspects of fossil proboscideans and their evolutionary response to open environments in the Neogene using several methods. The authors included all Asian bunodont proboscideans with long mandibles and I suggest that they should use the expression "bunodont proboscideans" instead of gomphotheres.

Weaknesses:

I believe that the only weakness is the lack of discussion comparing their results with the development of gigantism and long limbs in proboscideans from the same epoch.

Thank you for your comprehensive review and positive feedback on our study regarding the co-evolution of feeding organs in bunodont proboscideans during the Miocene. We appreciate your suggestion, and have decided to use the term "bunodont elephantiforms" (for more explicit clarification, we use elephantiforms to exclude some early proboscideans, like Moeritherium, ect.) instead of "gomphotheres," and we will make this change in our revised manuscript. We also appreciate the potential weakness you mentioned regarding the lack of discussion comparing our results with the development of gigantism and long limbs in proboscideans from the same epoch. We agree with the reviewer’s suggestion, and we are aware that gigantism and long limbs are potential factors for trunk development. Gigantism resulted in the loss of flexibility in elephantiforms, and long limbs made it more challenging for them to reach the ground. A long trunk serves as compensation for these limitations. limb bones were rare to find in our material, especially those preserved in association with the skull.

Reviewer #2 (Public Review):

This study focuses on the eco-morphology, the feeding behaviors, and the co-evolution of feeding organs of longirostrine gomphotheres (Amebelodontidae, Choerolophodontidae, and Gomphotheriidae) which are characterised by their distinctive mandible and mandible tusk morphologies. They also have different evolutionary stages of food acquisition organs which may have co-evolve with extremely elongated mandibular symphysis and tusks. Although these three longirostrine gomphothere families were widely distributed in Northern China in the Early-Middle Miocene, the relative abundances and the distribution of these groups were different through time as a result of the climatic changes and ecosysytems.

These three groups have different feeding behaviors indicated by different mandibular symphysis and tusk morphologies. Additionally, they have different evolutionary stages of trunks which are reflected by the narial region morphology. To be able to construct the feeding behavior and the relation between the mandible and the trunk of early elephantiformes, the authors examined the crania and mandibles of these three groups from the Early and Middle Miocene of northern China from three different museums and also made different analyses.

The analyses made in the study are:

(1) Finite Element (FE) analysis: They conducted two kinds of tests: the distal forces test, and the twig-cutting test. With the distal forces test, advantageous and disadvantageous mechanical performances under distal vertical and horizontal external forces of each group are established. With the twig-cutting test, a cylindrical twig model of orthotropic elastoplasity was posed in three directions to the distal end of the mandibular task to calculate the sum of the equivalent plastic strain (SEPS). It is indicated that all three groups have different mandible specializations for cutting plants.

(2) Phylogenetic reconstruction: These groups have different narial region morphology, and in connection with this, have different stages of trunk evolution. The phylogenetic tree shows the degree of specialization of the narial morphology. And narial region evolutionary level is correlated with that of character-combine in relation to horizontal cutting. In the trilophodont longirostrine gomphotheres, co-evolution between the narial region and horizontal cutting behaviour is strongly suggested.

(3) Enamel isotopes analysis: The results of stable isotope analysis indicate an open environment with a diverse range of habitats and that the niches of these groups overlapped without obvious differentiation.

The analysis shows that different eco-adaptations have led to the diverse mandibular morphology and open-land grazing has driven the development of trunk-specific functions and loss of the long mandible. This conclusion has been achieved with evidence on palaecological reconstruction, the reconstruction of feeding behaviors, and the examination of mandibular and narial region morphology from the detailed analysis during the study.

All of the analyses are explained in detail in the supplementary files. The 3D models and movies in the supplementary files are detailed and understandable and explain the conclusion. The conclusions of the study are well supported by data.

We appreciate your detailed and insightful review of our study. Your summary accurately captures the essence of our research, and we are pleased to note that multiple research methods were used to demonstrate our conclusions. Your recognition of the evidence-based conclusions from paleoecological, feeding behavior reconstruction, and morphological analyses reinforces the validity of our findings. Once again, we appreciate your time and thoughtful reviews.

Reviewer #1 (Recommendations For The Authors):

Thank you very much for the invitation to review this amazing manuscript. It is very well written and supported, and I have only minor suggestions to improve the text:

(1) Some references are not in chronological sequence in the text, and this should be reviewed.

We greatly appreciate the positive comments of the reviewer. We revised the reference of the manuscript as the reviewer’s suggestion.

(2) I suggest the use of the expression "bunodont proboscideans" instead of Gomphotheres because there is no agreement if Amebelodontidae and Choerolophodontidae are within Gomphotheriidae, as well as some brevirrostrine bunodont proboscideans from South America. So I think it is ok to use "Gomphotheriidae", but not gomphotheres to refer to all bunodont proboscideans included in the study.

The reviewer is correct. Using “gomphotheres” to refer to these three groups is inappropriate. We have replaced “gomphotheres” with "bunodont elephantiforms" throughout the entire manuscript. Here, we use “elephantiforms”, not “proboscideans”, to avoid confusion with some early proboscidean members like Moeritherium, ect.

(3) I was expecting some discussion on the development of large trunks related to the gigantism in these bunodont proboscideans, regarding the huge skulls and the columnar limbs.

We appreciate this suggestion, and we are aware that gigantism is a potential factor for trunk development. It is difficult to compare the three groups (Amebelodontidae, Choerolophodontidae, and Gomphotheriidae) in terms of their weight and limb bone length, because in our material, limb bones were rarely found, especially those associated with cranial material. Nevertheless, at this stage, all elephantiforms had significantly enlarged cranial sizes and limb bone lengths compared to early members like Phiomia. Gigantism caused the loss of flexibility in elephantiforms, and even the long limbs made it more difficult for an elephantiform to reach the ground. A long trunk compensates for this evolutionary change. Exploring these aspects further is a part of our future work.

(4) The reference to Alejandro et al should be replaced by Kramarz et al (and the correct surname of the authors). The name and surname of this reference need to be corrected. The correct names are Kramarz, A., Garrido, A., Bond, M. 2019. Please correct this in the text too.

We thank the reviewer for catching this error. This reference has been corrected.

Reviewer #2 (Recommendations For The Authors):

I believe your paper will lead to other studies on other Proboscidean groups on the evolution of the mandible and trunk. There are some corrections in the text:

• In line 199 in the text in pdf, "Tassy, 1994" should be "Tassy, 1996".

• In line 241, "studied" should be "studies"

• In line 313, "," after the word "tool" should be "."

We appreciate the reviewer for pointing these errors out and have revised these based on the suggestions.

• In the References, you write "et al." in some references. You should write the names of all of the authors.

• In the References: "Lister AM. 2013" and "Shoshani&Tassy" are not referenced in the text.

• In the References: "Tassy P. Gaps, parsimony, and early Miocene elephantoids (Mammalia), with a re-evaluation of Gomphotherium annectens (Matsumoto, 1925). Zool. J. Linn." should be "Tassy P. 1994. Gaps, parsimony, and early Miocene elephantoids (Mammalia), with a re-evaluation of Gomphotherium annectens (Matsumoto, 1925). Zool. J. Linn. 112, 1-2, 101-117" and replaced before "Tassy P. 1996".

We appreciate the reviewer’s suggestions and have revised these references.

Author Response

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

Reviewer #1

The authors provided experimental data in response to my comments/suggestions in the revision. Overall, most points were appropriate and satisfactory, but some issues remain.

(1) It is not fully addressed how atypical survivors are generated independently of Rad52-mediated homologous recombination.

The newly provided data indicate that the formation of atypical telomeres is independent of the Rad52 homologous recombination pathway.

"The atypical telomeres clones exhibit non-uniform telomere pattern", but the TG-hybridized signals after XhoI digestion are clear and uniform.

"Atypical telomere" clones may carry circular chromosomes embedded with short TG repeats, rather than linear chromosomes. In other words, atypical telomeres may differ from telomeres, the ends of chromosomes. Is atypical telomere formation dependent on NHEJ? Given that "two chromosomes underwent intra-chromosomal fusions" (Line 248), are atypical telomere clones detected frequently in SY13 cells containing two chromosomes?

We thank the reviewer’s questions. Frankly, we have not been able to determine the chromosome structures in these so-called "atypical survivors". As we mentioned in the manuscript, there could be mixed telomere structures, e.g. TG tract amplification, intro-chromosome telomere fusion and inter-chromosome telomere fusion. Worse still, these 'atypical survivors' may not have maintained a stable genome, and their karyotype may have undergone stochastic changes during passages. To avoid misunderstanding, we change the term "atypical" to "uncharacterized" in the revised manuscript.

We have previously shown that deletion of YKU70 does not affect MMEJ-mediated intra-chromosome fusion in single-chromosome SY14 cdc13Δ cells (Wu et al., 2020). In SY12 cells, double knockout of TLC1 and YKU resulted in synthetic lethality, and we were unable to continue our investigation. The result of synthetic lethality of TLC1 and YKU70 double deletion was shown in the Figure 7B in the reviewed preprint version 1, and the result was not included in the reviewed preprint version 2 in accordance with the reviewer's instructions.

"Atypical” survivors could be detected in SY13 cells (Figure 1D), but the frequency of their formation in the SY13 strain appeared to be lower than in SY12. As one can imagine, SY13 contains two chromosomes and its survivors should have a higher frequency of intra-chromosome fusions.

(2) From their data, it is possible that X and Y elements influence homologous recombination, type 1 and type 2 (type X), at telomeres. In particular, the presence of X and Y elements appears to be important for promoting type 1 recombination. In other words, although not essential, subtelomeres have some function in maintaining telomeres. I suggest that the authors include author response image 4 in the text. They could revise their conclusion and the paper title accordingly.

According to this suggestion, we have included author response image 4 in the revised manuscript as Figure 2E, Figure 5D, Figure 6C and Figure 6E. Accordingly, we have changed the title as “Elimination of subtelomeric repeat sequences exerts little effect on telomere essential functions in Saccharomyces cerevisiae”.

(3) Minor points: The newly added data indicate that X survivors are generated in a type 2-dependent manner. The authors could discuss how Y elements were eroded while retaining X elements (line 225, Figure 2A).

Thank this reviewer’s suggestion. We have discussed it in the revised manuscript (p.13 line 244-245). When telomere was deprotected, chromosome end resection took place. Since SY12 only has one Y’-element, it is hard to search homology sequences to repair the Y’-element in XVI-L. When the X-element in XVI-L was exposed by further resection, it is easier to find homology sequences to repair. So, in Type X survivor the Y’-element was eroded while retaining X-element.

Reviewer #2

I would like to congratulate the authors for their work and the efforts they put in improving the manuscript. The major criticism I had previously, ie testing the genetic requirements for the survivor subtypes, has been met. Below are a few minor comments that don't necessarily require a response.

(1) I think the Author response image 6 could have been included in the manuscript. I understand that the authors don't want to overinterpret survivor subtype frequencies, but this figure would have suggested some implication of Rad51 in the emergence of survivors even in the absence of Y' elements. At this stage, however, it is up to the authors, and leaving this figure out is also fine in my opinion.

According to the suggestion, the author response image 6 has been presented as Figure 6—figure supplement 7.

(2) Chromosome circularization seems to rely on microhomologies. Previously, the authors proposed that SY14 circularization depended on SSA (Wu et al. 2020), but here, since circularization appears to be Rad52-independent, it is likely to be based on MMEJ rather than SSA (although there are contradictory results on Rad52's role in MMEJ in the literature).

Yes, we mentioned it in the revised manuscript.

(3) p. 28 lines 511-513: "The erosion sites and fusion sequences differed from those observed in SY12 tlc1Δ-C1 cells (Figure 2D), suggesting the stochastic nature of chromosomal circularization": I don't think they are necessarily stochastic, because the sequences beyond the telomeres are now modified, the available microhomologies have changed as well.

We agreed with your opinion. In different chromosomes, there tend to be some hotspots for chromosome fusion. For example, in Figure 6C and 6F the resection site in Chr1 and Chr2 was the same in SY12XYΔ+Y tlc1Δ-C1 and SY12XYΔ tlc1Δ-C1. So, we speculate that there are some hotspots for chromosome fusion, but which site the cell will choose in one round chromosome fusion event is stochastic.

(4) Typos and other errors:

• p. 3 line 52: "subtelomerice" and "varies" are mispelled.

• p. 5 line 78: "processes" should be "process".

• Supp files are mislabelled (the numbers do not correspond to file name).

• Supp file 2: how come SY12 has only one Y' element and SY13 has two?

• p. 10 line 175: "emerging" should be "emergence".

• p.15 line 276: "counter-selected" should be "being counter-selected" or "counterselection".

• p. 29 line 523: "the formation of them" should be "their formation".

• p. 37 line 653: "could have been an ideal tool": the sentence is grammatically incorrect. Writing "AND could have been an ideal tool" is enough to make it structurally correct.

Thanks for pointing these errors out. We have corrected them in the revised manuscript. For the question “how come SY12 has only one Y' element and SY13 has two?” we were not sure at this moment. We speculated that one of the Y’ might be lost during genetic engineering of the chromosomes by CRISPR–Cas9 system.

Reviewer #3

The authors included statistical analyses of the qPCR data (Fig 4B) as requested, but did not comment on the striking difference in expression of MPH3 and HSP32 in the SY12 strain compared to BY4742. An improvement of the manuscript is the inclusion of rad52 tlc1 strains in their analyses, demonstrating that the "atypical and circular survivors" arose independently of homologous recombination. In addition, by analyzing rad51 and rad50 mutant strain they could demonstrate that the "type X" survivors had similar molecular requirements to type II survivors. Overall, the revised submission improves the article.

We thank the reviewer’s comments and suggestions. The SY12 strain (with three chromosomes) exhibited lower expression levels of both MPH3 and HSP32 compared to the parental strain BY4742 (with 16 chromosomes). We speculated that with the reduced chromosome numbers, the silencing proteins appeared to no longer be titrated by other telomeres that have been deleted. We have added these comments in the revised manuscript.

Wu, Z.J., Liu, J.C., Man, X., Gu, X., Li, T.Y., Cai, C., He, M.H., Shao, Y., Lu, N., Xue, X., et al. (2020). Cdc13 is predominant over Stn1 and Ten1 in preventing chromosome end fusions. Elife 9.

Author Response

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

eLife assessment:

This valuable study describes a new role of epithelial intercellular adhesion molecule 1 (ICAM-1) protein in controlling bile duct size. The effect is mediated via EBP-50 and subapical actomyosin to regulate size of bile canaliculi. These solid findings have theoretical and practical implications in hepatology and human disorders of bile ducts.

Public Reviews:

In this study, Cacho-Navas et al. describe the role of ICAM-1 expressed on the apical membrane of bile canaliculi and its function to control the bile canaliculi (BCs) homeostasis. This is a previously unrecognized function of this protein in hepatocytes. The same authors have previously shown that basolateral ICAM-1 plays a role in controlling lymphocyte adhesion to hepatocytes during inflammation and that this interaction is responsible for the loss of polarity of hepatocytes during disease states.

This new study shows that ICAM-1 is mainly localized in the apical domain of the BC and in association with EBP-50, communicates with the subapical acto-myosin ring to regulate the size and morphology of the BC. They used the well-known immortal cell line of liver cells (HepG2) in which they deleted ICAM-1 gene by CRISPR-Cas9 editing and hepatic organoids derived from WT and ICAM-1-KO mice. alternating KO as well as rescue experiments. They show that in the absence of apical ICAM-1, the BC become dilated.

The data sufficiently support the conclusions of the study.

Recommendations for the authors:

We would like to thank the editor and reviewer for recognizing the manuscript's value and the solid nature of the data. We are also thankful to them for acknowledging that the manuscript supports the conclusions. Below, we have addressed their commentaries and questions in a point-by-point rebuttal document:

We have a few suggestions to improve the manuscript:

(1) HepG2 cells form canaliculi-like structures but are not the ideal system to study the apical basal polarity. On the other hand, hepatic organoids can assume a hepatocyte-like phenotype, when cultured under specific conditions but are not functionally comparable to hepatocytes organized in a 3D structure with a hollow lumen that does not recapitulate the BC physiological structure. Therefore, primary hepatocyte in collagen sandwich would be the best model to study the polarization of BCs and could be isolated from WT and ICAM-1-KO mice, that are available. Some of the major findings should be confirmed in this system.

We adopted the culture of hepatic organoids as an experimental strategy motivated by the difficulties to culture primary hepatocytes experienced in previous analyses (RegleroReal, Cell Rep, 2014). The generation of organoids or mature hepatocytes from various sources of stem cells is a commonly employed strategy in hepatocyte cell biology (Meyer et al. EMBO Rep, 2023), due to the difficulties in maintaining mature hepatic epithelial cell cultures for longer than a few hours.

The hepatic organoids we have used in the manuscript are being accepted as advanced cellular strategies for a broad range of fields (Belenguer, Nat Commun, 2022; de Crignis, eLife, 2021; Huch, Cell, 2015). Despite they have some morphological differences with real hepatocytes, we conducted a thorough characterization of their organization identifying canalicular-like structures with functional (CFDA) and molecular (HA-4) markers, which we believe adds value to the manuscript. In addition, the organoid technology has allowed us to import the bipotent precursors to get an permanent source of hepatic cells without the need to import and use the ICAM-1_KO mice, in line with the current guides to reduce animal experimentation.

Taking this into account and to further validate data obtained with our cellular systems, we carried out a quantification of the canalicular diameter in livers from WT and ICAM1_KO cells (New Figure 8B), which validates our data on human cell lines and organoids. We acknowledge that the data obtained from hepatic tissues cannot rule out the contribution of immune cell adhesion to changes in the hepatocyte architecture. However, these experiments, together with the aforementioned organoids and human cell lines, strongly suggest a role for hepatic ICAM-1 in regulating canalicular size.

(2) Overexpression of proteins was used in the study. While this approach is an easier means to visualize, without the use of specific antibodies, it is known to alter the distribution of the protein compared to the endogenous one.

Most of our characterization has been done with antibodies or other fluorescent tools against endogenous proteins localized at BCs: CD59, F-actin, EBP50, MHC, MLC…. In addition, we have included MDR1-GFP and GFP-Rab11, the latter to analyze the subapical compartment (SAC) surrounding BCs. As requested by the reviewer, we now include in a new Supplementary Figure 1C the confocal analyses of endogenous canalicular markers, radixin and MRP2, as well as a new Supplementary Figure 1D containing the staining of an endogenous marker of the SAC, plasmolipin/PLLP (Fraticelli et al, Nat Cell Biol, 2015; Cacho-Navas, Cell Mol Life Sci, 2022), which is consistent with the previous analyses performed with GFP-Rab11.

(3) In the absence of ICAM-1, BCs change shape and dimension but still show the presence of microvilli. What happens to the distribution of polarized transporters like Mrp2, or the transport of bile acids (CFDA clearance) in vivo in the KO animal?

Thank you for this comment. We have analyzed this transporter in murine livers and human hepatic cells. MRP2 distribution does not significantly change and is concentrated in BCs also in ICAM-1_KO livers (New Figure 8C). Likewise, ICAM-1 gene edition does not affect MRP2 localization in the polarized human hepatic epithelial cell line in vitro (Supplementary Figure 1C). We cannot rule out changes for this transporter in other murine liver cell types in vivo, such as sinusoidal endothelial cells, which we believe should be further addressed in a different piece of work.

(4) Does the lack of ICAM-1 affect the cell viability, proliferation or cell size?

ICAM-1_KO cells proliferate slightly more slowly than their WT counterparts, with no detected changes in cell size and death. We present these data in Supplementary Figure 1, A and B.

(5) Are the findings recapitulated in the livers of ICAM-1 KO animals?

ICAM-1 KO animals present enlarged BCs, which is consistent with the main findings of the manuscript (Figure 8B).

The text needs to be more concise. Some of the concepts, in particular those already published, should be condensed. There is a large amount of experiments that are difficult to connect logically. Possibly, cartoons summarizing the approach of the figure could help the reader.

The text of Results and Discussion sections has been shortened by almost 100 words, despite the additional panels and experiments are now described and discussed. New cartoons have been added in Figure 5G and Figure 8F, in addition to those previously included in Figure 1 and Supplementary Figure 6, the latter containing a graphical descriptions of the main conclusions.

Also, more detailed information about statistical analysis (what post-test was used?), concentration of cytokines, and description of the mouse model should be included in the methods.

Cytokine concentrations have been included in the legend of Figure 3 and in the Cell and Culture section of Methods. A brief description of the ICAM-1_KO mouse and the corresponding reference for further information is also provided in the Organoid Culture section of Methods. A statistical analysis section describing the post-test used is also included at the end of Methods. The references of anti-plasmolipin, anti-radixin and antiMRP2 antibodies, as well as the new fixation methods used for immunofluorescence are also included in the corresponding Antibody List and in the Confocal Microscopy section of Methods, respectively . .

Figure 3D. Sample names should be added as in the rest of the figures.

The arrangement of sample names in Figure 3D has been revised and is now similar to that of Figure 3A.

Author Response

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

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 astroglial 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, more than 50% of the cells in the astroglial lineage clusters are NSCs, which is extremely high and inconsistent with classic histology studies.

While the authors have made efforts to address previous critics, major concerns have not been adequately addressed, including a very limited sample size and with poor patient information. In addition, some analytical approaches are still questionable and the authors acknowledged that some they cannot address. Therefore, while the topic is interesting, some results are preliminary and some conclusions are not fully supported by the data presented.

We thank the reviewer for reevaluating our revised manuscript. We respect the reviewer’s comments and discuss the technical and conceptual limitations of this work. Here we provide the response to Reviewer #1 (Public Review) on these below.

Firstly, we appreciate the concerns raised by Reviewer 1 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 Figure 2-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.

Secondly, we cannot adequately address the major concern regarding sample size raised by the reviewer due to the scarcity of stroke and neonatal human brain samples. We have collected additional details about the donors. Please refer to Figure 1-source data 1 for the updated information. Other information regarding the lifestyle parameters of these donors has not been sufficiently recorded by the hospital. Therefore, we cannot improve the patient information further.

Thirdly, regarding the questionable subpopulations of granule cells (GCs) that derive from neuroblasts in Figure 4A-4D, which are inconsistent with previous single-cell transcriptomic studies, we tried various strategies to confirm the identity of the two subpopulations of granule cells (GCs) derived from neuroblasts but didn’t get 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.

In the end, we have discussed the technical and conceptual limitations of this work and added a brief discussion about these limitations in the last paragraph of the main text. We hope the readers can interprate our data critically and objectively.

Reviewer #2 (Public Review):

In this manuscript, Yao et al. present a series of experiments aiming at generating a cellular atlas of the human hippocampus across aging, and how it may be affected by injury, in particular, stroke. Although the aim of the study is interesting and relevant for a larger audience, due to the ongoing controversy around the existence of adult hippocampal neurogenesis in humans, a number or technical weaknesses result in a poor support for many of the conclusions made from the results of these experiments.

In particular, a recent meta analysis of five previous studies applying similar techniques to human samples has identified different aspects of sample size as main determinants of the statistical power needed to make significant conclusions. Some of this aspects are the number of nuclei sequenced and subject stratification. These two aspects are of concern in Yao's study. First, the number of sequenced nuclei is lower than the calculated numbers of nuclei required for detecting rare cell types. 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. Secondly, the number of donors included in some of the groups is extremely low (n=1) and the miscellaneous information provided about the donors is practically inexistent. As individual factors such as chronic conditions, medication, lifestyle parameters, etc... are considered determinant for the variability of adult hippocampal neurogenesis levels across individuals, this represents a series limitation of the current study. Overall, several technical weaknesses severely limit the relevance of this study and the ability of the authors to achieve their experimental aims.

After a first review round, the manuscript is still lacking a clear discussion of its several technical limitations, which will help the audience to grasp the relevance of the findings. In particular, detailed information about individual patients health status and relevant lifestyle parameters that may have affected it is lacking. The authors make the point themselves that the discrepancies among studies might be caused by health state differences across hippocampi, which subsequently lead to different degrees of hippocampal neurogenesis.". So, even in the authors own interpretation this is a serious limitation to the manuscript, that however out of the authors control, impacts on the quality of their findings.

Reviewer #2 (Recommendations For The Authors):

Please see public review. I do understand the authors point about incomplete patient data collection and low patient numbers and how the former is out of their control. Nevertheless, these are crucial parameters that impact negatively on the quality and relevance of several of their bold claims in the manuscript, especially given the low number of patients included. The current version still lacks a clear and honest discussion of the several technical and conceptual limitations of the authors work, as in some cases they are presented to the reviewers in the rebuttal letter, for the readership, so that they could critically evaluate the relevance of the authors' finding in a bigger perspective.

We thank the reviewer for reevaluating our revised manuscript. We respect the reviewer’s comm¬ents and discuss the technical and conceptual limitations of this work. Here we provide the response to Reviewer #2 (Public Review) on these below.

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 possible that we are able to detect NBs. Importantly, 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%. 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,B andF, 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, 5D and 6B), cell type-specific gene expression (Figure1 C and D), overall transcriptomic characteristics (Figure 1-supplement 1E), and developmental potential (Figure4 A-D, Figure 6E and F). We hope these evidences together could explain why we can identify the rare neurogenic populations.

Regarding the limited sample size and poor patient information, we cannot adequately address these two major concerns. Due to the scarcity of stroke or neonatal human samples, it was not feasible to collect a larger sample size within the expected timeframe. We have collected additional details about the donors. Please refer to Figure 1-source data 1 for the updated information. Other information regarding the lifestyle parameters of these donors has not been sufficiently recorded by the hospital. Therefore, we cannot improve the patient information further.

As per the reviewer’s recommendation, in the latest version, we have discussed the technical and conceptual limitations of this work and added a brief discussion about these limitations in the last paragraph of the main text. We hope the readers can interprate our data critically and objectively.

Author Response

We thank both reviewers for the positive evaluation of our work and suggestions on how to improve it.

We agree with Reviewer #1 that reporting uncertainties will both clarify and strengthen our arguments. Where applicable, uncertainties will be added in a revised version.

To Reviewer #2’s suggestion of including free energy calculations to estimate the free energies of hydrogen bond and hydrophobic interactions, the current free energy methods are capable of given accurate estimates of the relative binding free energies of similar ligands; however, accurate calculations of the absolute free energies of hydrogen bond and hydrophobic interactions are not feasible yet.

Again, we thank the reviewers for their assessment and suggestions. We will update the manuscript as we have outlined above.

Author Response

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

Public Review

[...] A particular strength of the present study is the structural characterization of human PURA, which is a challenging target for structural biology approaches. The molecular dynamics simulations are state-of-the-art, allowing a statistically meaningful assessment of the differences between wild-type and mutant proteins. The functional consequences of PURA mutations at the cellular level are fascinating, particularly the differential compartmentalization of wild-type and mutant PURA variants into certain subcellular condensates.

Weaknesses that warrant rectification relate to (i) The interpretation of statistically non-significant effects seen in the molecular dynamic simulations.

We removed from the manuscript the sentence which indicated that we analyzed statistically non-significant effects. Therefore, the above statement has been resolved.

(ii) The statistical analysis of the differential compartmentalization of PURA variants into processing bodies vs. stress granules, and

We re-analyzed all cell-biological data and adjusted the statistical analysis of P-bodies and Stress-granule intensity analysis. The new, and improved statistics have replaced the original analyses in the corresponding figures (Figs. 1C and 2B).

(iii) Insufficient documentation of protein expression levels and knock-down efficiencies.

Quantification of protein expression levels by Western blotting is shown in Appendix Figure S1. Quantification of knock-down efficiencies by Western blot experiments (Appendix Figure S3).

Recommendations for the authors: Reviewer #1

Concerns and Suggested Changes

(a) I have only one concern about the computational part and that is about statements such as "There are also large differences in the residue surrounding the mutation spot (residues 90 to 100), where the K97E mutant also shows much greater fluctuation. However, these differences are not significant due to the large standard deviations." If the differences are not statistically significant, then I would suggest either removing such a statement or increasing the statistics.

We agree with the Reviewer’s comment. We removed this sentence from the text.

Recommendations for the authors: Reviewer #2

General Comments

This is a challenging structural target and the authors have made considerable efforts to determine the effect of several mutations on the structure and function. Many of the constructs, however, could not be expressed and/or purified in bacteria. However, it is not clear to what extent other expression systems (e.g. Drosophila or human) were considered and if this would have been beneficial.

We did not use other expression systems because the wild-type protein is well-behaved when expressed in E. coli. In case a mutant variant cannot be expressed or does not behave well in E. coli, this constitutes a clear indication that the respective mutation impairs the protein’s integrity. Thus, by using E. coli as a reference system for all the variants of PURA protein, we could assess the influence of the mutations on the structural integrity and solubility. Only for the variants that did not show impairment in E. coli expression, we continued to assess in more detail why they are nevertheless functionally impaired and cause PURA Syndrome.

Concerns and Suggested Changes

(a) The schematic in Figure 3A would have been helpful for interpreting the mutations discussed in Figures 1 and 2. I would suggest moving it earlier in the text.

We changed the figure according to the Reviewer’s suggestion.

(b) I believe the RNA used for binding studies in Figures 3C and D was (CGG)8. Are the two "free" RNA bands a monomer and a dimer (duplex?)?

Although we do not know for certain, it is indeed likely that the two free RNA bands represent either different secondary structures of the free RNA or a duplex of two molecules. Of note, PURA binds to both “free” RNA bands, indicating that it either does not discriminate between them or melts double-stranded RNA in these EMSAs.

There also seems to be considerable cooperativity in the binding, so I wonder if a shorter RNA oligonucleotide might facilitate the measurement of Kds.

The length of the used RNA was selected based on the estimated elongated size of the full-length PURA and the presence of 3 PUR repeats. Assuming that one PUR repeat interacts with about 6-7 bases (data from the co-structure of Drosophila PURA with DNA; PDB-ID: 5FGP) and that full-length PURA forms a dimer consisting of three PUR repeats, the full-length protein in its extended form should cover a nucleic-acid stretch of about 24 bases.

Also, it is not clear how the affinities were measured particularly for hsPURA III since free band is never fully bound at the highest protein concentration.

It was not our goal to measure Kds for the interaction of PURA variants with RNA. The EMSA experiments were conducted to detect relative differences in the interaction between PURA variants and RNA. To estimate the differences, we measured total intensity of the bound (shifted) and unbound RNA. The intensities of the bands observed on the scanned EMSA gels were quantified with FUJI ImageJ software. We calculated the percentage of the shifted RNA and normalized it. hsPURA III fragment shows much lower affinity therefore it does not fully shift RNA with the highest protein concentration when compared to the full-length PURA and to PURA I-II.

(c) Do the human PURA I+II and dmPURA I+ II crystallize in the same space group and have similar packing? Can the observed structural flexibility be due to crystal contacts?

hsPURA I+II and dmPURA I+II crystallize in different space groups with different crystal packing. In both cases, the asymmetric unit contains 4 independent molecules with the flexible part of the structure composed of the β4 and β8 (β ridge) exposed to solvent. In the case of the Drosophila structure, we do not observe any flexibility of both β-strands. In contrast, for the human PURA structure the β ridge exhibits lots of flexibility and it adopts different conformations in all 4 molecules of the asymmetric unit. We observe similar flexibility of the β4 and β8 (β ridge) in the structure of K97E mutant which contains 2 molecules in the asymmetric unit. We would like to add that we expect crystal contacts to rather stabilize than destabilize domains.

Similarly, can the conformations observed for the K97E mutant be partially explained by packing?

Regarding the sequence shift observed for the β5 and β6 strands in hsPURA I+II K97E variant: although the β5 strand with shifted amino acid sequence is involved in the contact with the symmetry-related molecule with another β5 strand we don’t consider this interaction as a source of the shift. To be sure that the shift is not forced by the crystallization, we had performed NMR measurement which confirmed that in solution there is a strong change in the β-stands comparing WT and K97E mutant. This is an unambiguous indication that the structural changes observed in the crystal structure are also happening in solution. In addition, the MD simulations provide additional confirmation of our interpretation that K97E destabilizes the corresponding PUR domain. Taken together, we provide proof from three different angles that the observed differences indeed affect the integrity and hence function of the protein.

(d) Perhaps, it is my misunderstanding, but I find the NMR data on the Arg sidechains for the K97E confusing. If they are visible for K97E and not WT, doesn't this indicate that there is an exchange between two conformations or more dynamics in the WT structure? This does not seem to be the opposite of the expectation if K97E is thought to have more conformational flexibility.

Due to a technical issue (peak contour level), arginine side chain resonances were not clearly visible in the WT spectrum. The figure 5F has been updated. Now, they do correspond to those seen in the mutant spectrum. However, to prevent any confusion or mis/overinterpretation, we removed the sentence regarding arginine side chain: "Intriguingly, arginine side chain resonances Nε-Hε were only visible in the K97E variant, while they were broadened out in the wild-type spectrum."

(e) The most speculative part of the paper is the interpretation of SG and PB localization of PURA in Fig 1 and 2. There is an important issue with the statistics that must be clarified because it would appear that statistical significance was determined using each SG or PB as an independent measurement. This is incorrect and significance should be measured by only using the means of three biological replicates. This is well described here. It is not clear at this time if the reported P values will be confirmed upon reanalysis, and this may require reinterpretation of the data.

We are grateful for this clarifying comment and agree that the statistical analysis of P-body and stress granule was misleading. Of note, while the figures depicted all the values independent of the biological repeats, the statistical analyses were done on the mean value of each replicate of each cell line and not all raw data points.

We prepared new Plots, only showing the mean value of each replicate, and also re-calculated P-values. The values have changed only slightly in this new analysis because we now also included the previously labeled outliers (red points) to better demonstrate that significance still exists even when considering them.

In the new analysis of stress-granule association, only the value of the K97E mutant lost its significance, indicating that its association to stress granules is not lost. Therefore, we adjusted the following sentences in the manuscript.

Results:

Original: "While quantification showed a reduced association of hsPURA K97E mutant with G3BP1-positive granules (Fig 1B), the two other mutants, I206F and F233del, showed the same co-localization to stress granules as the wild type control."

Corrected: "In all the patient-related mutations, no significant reduction in stress granule association was seen when compared to the wild type control (Fig 1C)."

Original: "The observation that only one of the patient-related mutations of hsPURA, K97E, showed reduced stress granule association indicates that this feature may not constitute a major hallmark of the PURA syndrome. It should be noted however that this interpretation must be considered with some caution as the experiments were performed in a PURA wild-type background."

Corrected: "As we did not observe significant changes in the association of patient-related mutations of hsPURA to stress granules, it is suggested that that this feature may not constitute a major hallmark of the PURA syndrome. It should be noted however that this interpretation must be considered with some caution as the experiments were performed in a PURA wild-type background."

(f) A western blot showing the level of overexpression of the PURA proteins should be shown in Figure 1 as well as the KD of endogenous PURA for Figure S2?

As requested, a Western blot showing the level of overexpression of the different PURA proteins has been added as Appendix Figure S1.

A Western blot of the siRNA-mediated knock-down experiments of PURA and their corresponding control has been added to Appendix Figure S3. Quantification of three biological repeats showed a significant reduction of PURA protein levels upon knock down.

(g) While I appreciate that rewriting is time-consuming, I would recommend considering restructuring the manuscript because I think that it would aid the overall clarity. I think the foundation of the work is the structural characterization and would suggest beginning the paper with this data and the biochemical characterization. The co-localization with SGs and PBs and how this may be relevant to disease is much more speculative and is therefore better to present later. While I appreciate that the structural interpretation of why some mutants localize to PBs differently is not entirely clear, I do think that this would provide some context for the discussion.

In the initial version of the manuscript we first presented the structural characterization of PURA and afterwards the co-localization with SGs and PBs. As this reviewer stated him-/herself in (e), we also noticed that the SG and PB interpretation is the most speculative part of this manuscript. We felt that having this at the end of the results section would weaken the manuscript. On the other hand, we consider that the structural interpretation of mutations is much stronger and has a greater impact for future research. After long discussion we decided to swap the order to leave the most important results for the end of the manuscript.

Recommendations for the authors: Reviewer #3

Concerns and Suggested Changes:

(a) For the characterization of G3BP1-positive stress granules in HeLa cells upon depletion of PURA, it remains unclear what is the efficiency of siRNA? The authors should provide a western blot to indicate how much the endogenous levels were reduced.

We completely agree with the stated concern and addressed it accordingly. We had performed this experiment prior to submission but for some unknown reason it was not included in the manuscript.

The Western blot of siRNA-mediated knock-down experiments of PURA and their corresponding control is now shown in Appendix Figure S3. Quantification of three biological repeats, showed a significant reduction of PURA protein levels upon knock down.

(b) How does knocking down PURA affect DCP1A-positive structures in HeLa cells? Would P bodies be formed even in the absence (or reduction) of total PURA?

Indeed, the stated question is very interesting. In fact, we have already shown in our recent publication (Molitor et al., 2023) that a knock down of PURA in HeLa and NHDF cells leads to a significant reduction of P-bodies. We actually referred to this finding on page 6:

"Since hsPURA was recently shown to be required for P-body formation in HeLa cells and fibroblasts (Molitor et al. 2023), PURA-dependent liquid phase separation could potentially also directly contribute to the formation of these granules."

On the same page, we also refer to the underlying molecular mechanism:

"However, when putting this observation in perspective with previous reports, it seems unlikely that P-body formation directly depends on phase separation by hsPURA, but rather on its recently reported function as gene regulator of the essential P-body core factors LSM14a and DDX6 (Molitor et al., 2023)."

Author Response

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

• Is the coronal slice in Figure 2 the corresponding mid-coronal plane to compute Dice scores? If so, the authors could mention it so that readers have an idea where the selected slice is.

This is indeed a good point. The coronal slice in Figure 2 is not part of the set of slices that we used to compute Dice scores. Showing such a slice is important, so we have added a small figure to the appendix with one of these slices, along with the corresponding automated segmentations.

• SIFT descriptors were adopted to detect fiducials only. Maybe it could also be applied to align stacked photographs of brain slices.

While SIFT is robust against changes in pose (e.g., object rotation), perspective, and lightning, it is not robust against changes in the object itself – such as changes between one slice to the next, as is the case in our work. We have added a sentence to the methods section clarifying this issue.

Author Response

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

Reviewer #1

Weaknesses:

Start site fidelity in purified recons5tuted systems can be drama5cally altered in different buffer condi5ons. Interpreta5on of the observed changes to start site selec5on in mRNAs in the absence or presence of Ded1 using only the one buffer condi5on used is therefore limited.

This is an excellent point and is something we could explore in future studies using the Rec-Seq system. We have added this caveat to the Discussion on lines 797-809. We have previously studied the fidelity of start codon recogni>on in the recons>tuted system (Kolitz et al., [2009] RNA, 15:138-152) and found that under our standard buffer condi>ons the codon specificity generally reflects what we observed in vivo using a dual-luciferase reporter assay, with the most stable 48S complexes forming on AUG codons, followed by first posi>on mismatches (GUG, UUG, CUG), with second and third posi>on mismatches leading to significantly less stable complexes. However, as the reviewer notes, there are some devia>ons: ACG and AUA are poor codons in the in vitro system under the buffer condi>ons used but allowed rela>vely strong expression in our in vivo reporter assay. It should also be noted that the hierarchy of nearcognate start codon usage in vivo in yeast differs according to the study and the reporter used, making it difficult to establish a “ground truth” for start codon fidelity.

I have some specific comments to strengthen the manuscript and address some minor issues.

It is not clear to me whether the authors refold the purified mRNA aEer phenol/chloroform extrac5on? Have the authors observed different results if the mRNA is refolded or not? This is appropriate since the authors compare their Rec-Seq data to PARS scores that were generated from refolded mRNAs. One assumes that the total mRNA used is refolded in the same way as the PARS score study, but this is not clearly stated. The authors should make this point clear in the text and methods.

This is an excellent point. We did not use the final refolding protocol that Kertesz et al. used when they developed their PARS scores and now clarify this in the Methods sec>on (lines 962967). It is possible that we would have seen stronger correla>ons in the analyses using PARS scores had we followed the renatura>on protocol, although the fact that we observed significant correla>ons (e.g., Fig. 3E-H) suggests the structures in the Kertesz et al. mRNAs were similar to those in our mRNAs.

It is not clear how the authors determine the concentra5on of total mRNA that is used in the assay - reported as 60 nM? Are the authors assuming a molecular weight of an average mRNA to determine the concentra5on? The authors should provide more detail for how they quan5fy their mRNA concentra5on and its stoichiometry compared to 43S PICs.

We thank the reviewer for poin>ng out this oversight and have now included this informa>on on lines 849-855 of the Methods sec>on.

Comments regarding start site fidelity in the recons5tuted system:

The authors use in vitro transcribed tRNAi-Met. Since tRNA modifica5ons may play a role in start site fidelity, the authors should perhaps men5on that this will need to be inves5gated in a future study in the discussion.

This is a good point and we now note it as a caveat in the Discussion on lines 806-809.

The authors state that Ded1 promotes leaky scanning regardless of the mAUG start site context (page 24; lines 533-534). The authors then state on page 25 that the level of iAUG ini5a5on rela5ve to mAUG ini5a5on does depend on the mAUG context (lines 545-546). This seems contradictory unless I am not understanding this correctly? It would certainly be surprising that mAUG context didn't regulate leaky scanning in the recons5tuted system given the fact that ini5a5on codon context regulates selec5on in cells (when Ded1 is present).

These statements are correct as wrihen. As shown in Figure 5O, the frequency of leaky scanning (as measured by rela>ve ribosome occupancy of the internal region of the ORF, not including the main start codon, to the whole ORF, including the main start codon; RRO) decreases as the context score around the start codon gets stronger (green and purple lines). The RRO is increased to the same extent when 500 nM Ded1 is added, regardless of the strength of the start codon context, indica>ng that Ded1 enhances leaky scanning equally (compare slopes of the green line without Ded1 to the purple line with Ded1). Because of this, the effect of Ded1 on RRO (DRR0) is constant across context score bins (orange line). There is no discrepancy between our two conclusions that leaky scanning of the mAUG increases as context score decreases and that Ded1 increases leaky scanning equally for good and bad mAUG contexts, indica>ng that Ded1 does not inspect the mAUG context and simply decreases the dwell >me equally at all contexts.

Further to the start site context ques5on. It is possible that the fidelity of the recons5tuted system (i.e. buffer condi5ons) is not fully reflec5ng in vivo-like start site selec5on. A rigorous characteriza5on of commercially available re5culocyte lysate systems iden5fied buffer condi5ons that provided similar start site fidelity to that observed in live cells (Kozak. Nucleic Acids Res. 1990 May 11;18(9):2828). While I feel that it is beyond the context of the current work to undertake a similar rigorous buffer characteriza5on, one must be careful about interpre5ng the results about leaky scanning and upstream ini5a5on sites in the current work. Perhaps one would observe similar results to Guenther et al. if the fidelity (buffer condi5ons) of the recons5tuted system were different? I appreciate that the authors state that their results only apply to their recons5tuted system and do not necessarily suggest that previous data are incorrect, but with only one buffer condi5on being tested in the current study it may be appropriate to further soEen the interpreta5on of the current results when compared to published data in live cells.

This point is well-taken. As noted above, we have added a caveat about possible effects of buffer condi>ons on start codon fidelity to the Discussion (lines 797-809). In terms of the possibility that upstream ini>a>on is more frequent in vivo than we observe in the in vitro RecSeq system, we previously studied 5’UTR transla>on in vivo using ribosome profiling (Kulkarni et al. [2019] BMC Biol., 17:101). The ra>o of RPFs in 5’UTRs to coding sequences in this study was 0.0027, very similar to the value measured in the in vitro Rec-Seq system in the presence of Ded1 (0.0016-0.0017). Thus, it does not seem that the frequency of upstream ini>a>on is drama>cally higher in vivo than in our in vitro system. We have now made note of this point in the Results (lines 594-598). Guenther et al. employed a ribosome profiling protocol in which they added cycloheximide to their cells prior to lysis, which has been shown to create significant ar>facts, par>cularly in 5’UTR transla>on (e.g., Gerashchenko and Gladyshev [2014] Nucleic Acids Res., 42:e134). Nevertheless, as suggested by the reviewer, we have modified the text in the Results and Discussion to somen the interpreta>on somewhat (lines 582-583; 616-618; 761763).

Reviewer #2

Weaknesses:

Several findings in this report are quite surprising and may require addi5onal work to fully interpret. Primary among these is the finding that Ded1p s5mulates accumula5on of PICs at internal site in mRNA coding sequences at an incidence of up to ~50%. The physiological relevance of this is unclear.

We agree with the reviewer that understanding the physiological significance, if any, of the apparent leaky scanning of main AUG start codons induced by Ded1 is an unanswered ques>on that will require addi>onal studies. It is possible that rapid 60S subunit joining and forma>on of the 80S ini>a>on complex amer start codon recogni>on on most mRNAs reduces the leaky scanning effect in vivo. We now bring up this possibility in the Discussion sec>on (lines 804809). However, as noted in lines 568-580, mRNAs that display significantly decreased mRPFs at 500 nM Ded1 in the Rec-Seq system also tend to have TEs that are increased in the ded1-cs- mutant rela>ve to WT yeast in in vivo ribosome profiling experiments, sugges>ng that Ded1 ac>vity also diminishes ini>a>on on mAUG codons in these mRNAs in vivo.

A limita5on of the methodology is that, as an endpoint assay, Rec-Seq does not readily decouple effects of Ded1p on PIC-mRNA loading from those on the subsequent scanning step where the PIC locates the start codon. Considering that Ded1p ac5vity may influence each of these ini5a5on steps through dis5nct mechanisms - i.e., binding to the mRNA cap-recogni5on factor eIF4F, or direct mRNA interac5on outside eIF4F - addi5onal studies may be needed to gain deeper mechanis5c insights.

We agree that this is a limita>on of the Rec-Seq assay and now men>on this point in the Discussion sec>on (lines 810-817). It is possible that future work using cross-linking agents to stabilize 43S complexes bound near the cap and scanning the 5’UTR, similar to the methodology used in 40S ribosome profiling, could enable us or others to disentangle these steps from one another.

As the authors note, the achievable Ded1p concentra5ons in Rec-Seq may mask poten5al effects of Ded1p-based granule forma5on on transla5on ini5a5on. Addi5onal factors present in the cell could poten5ally also promote this mechanism. Consequently, the results do not fully rule out granule forma5on as a poten5al parallel Ded1p-mediated transla5on-inhibitory mechanism in cells.

We agree. As stated in the Discussion sec>on (lines 735-741): “It is possible that at higher concentra>ons of Ded1 than were achievable in these in vitro experiments or in the presence of addi>onal factors that modify Ded1’s ATPase or RNA binding ac>vi>es the factor could directly inhibit a subset of mRNAs, by ac>ng as an mRNA clamp that impedes scanning by the PIC, or by sequestering the mRNAs in insoluble condensates. It might be interes>ng in the future to test candidate factors in Rec-Seq to determine if they switch Ded1 from being a s>mulatory helicase to an inhibitory mRNA clamp that removes transcripts from the soluble phase.”

It is certainly clear why the 15-minute 5mepoint was chosen for these assays. However, I wondered whether data from an earlier 5mepoint would provide useful informa5on. The descrip5on on line 210 of the compiled PDF suggests data from different 5mepoints may be available; if it is, in my view it could be a useful addi5on. More generally, including language about the single-turnover nature of these reac5ons may be helpful for the benefit of a broad audience.

In preliminary experiments, we have used the Rec-Seq system to measure the kine>cs of 48S PIC forma>on transcriptome-wide. As you probably can imagine, this is a challenging experiment and requires addi>onal work before we would feel comfortable publishing it. We very much agree with the reviewer that resolving the kine>cs of these events will provide important addi>onal informa>on. As suggested, we have added caveats about the endpoint and single-turnover nature of the assay to the Discussion (lines 821-828).

I wondered whether it might be useful to present addi5onal informa5on on the mRNAs not found in the assay. For example, are these the least abundant mRNAs, which may not have had 5me to recruit the 43S PIC?

75% of mRNAs (2719 of 3640) not observed in the Rec-Seq analysis had densi>es below the median (2.3 reads per nucleo>de). We now men>on this in the Methods sec>on (lines 855856).

The Rec-Seq recruitment reac5ons were carried out at 22C˚ . Considering that remodeling of RNA structure by helicase enzymes is a focal point of the study, linking the results to the recruitment landscape at a closer-to-physiological temperature may bolster the conclusions.

In the future, it would be interes>ng to test the effects of temperature on 48S PIC forma>on using the Rec-Seq system. As the reviewer suggests, the interplay between temperature and mRNA structure could reveal interes>ng phenomenon. It is worth no>ng, however, that there is no clear “physiological” temperature for S. cerevisiae. For consistency and convenience, lab yeast is usually grown at 30 ˚C, but in the wild yeast live at a wide range of temperatures, which generally change throughout the day. From this standpoint, 22 ˚C seems reasonably physiological.

Results from Rec-seq experiments conducted at 15° C might be more directly comparable to in vivo Ribo-seq data with the ded1-cs mutant. However, already ~90% of the Ded1hyperdependent mRNAs iden>fied by Ribo-seq analysis of that mutant were iden>fied here as Ded1-s>mulated mRNAs in Rec-Seq experiments at 22°C. The Ribo-seq experiments conducted by Guenther et al. were conducted on the ded1-ts mutant at 37°C; thus, any structures that confer Ded1-dependent leaky-scanning through uORFs detected in that study should have been stable in our Rec-Seq experiments.

The introduc5on provides an important, detailed exposi5on of the state of the field with respect to Ded1p ac5vity. Nevertheless, in my view, it is quite lengthy and could be streamlined for clarity. As just one example, the proposed func5on of Ded1p in the nucleus seems like a detail that could be dispensed with for the present work.

We have ahempted to shorten the Introduc>on, as suggested. However, we did not remove the short sec>on describing Ded1’s possible roles in the nucleus and ribosome biogenesis because we felt it was important to emphasize that one of the strengths of the Rec-Seq system is that it allows us to isolate the early steps of transla>on ini>a>on from later steps and from other cellular processes. In addi>on, at the sugges>on of Reviewer #3, we added a brief explana>on of Ded1’s possible role in the subunit joining step of transla>on.

Reviewer #3

Weaknesses:

The slow nature of the biochemical experiments could bias results.

We agree that the 15-minute >me point used could mask effects that are manifested at a purely kine>c level. It should be noted that we have measured the observed rate constants for 48S forma>on on a variety of mRNAs in the in vitro recons>tuted system in the presence of satura>ng Ded1 (Gupta et al. [2018] eLife, hhps://elifesciences.org/ar>cles/38892 ) and found that they are generally in the range of es>mates of rate constants for transla>on ini>a>on in vivo in yeast (~1-10 min-1; e.g., Siwiak and Zielenkiewicz [2010], PLOS Comput. Biol., 6: e100865). In preliminary experiments, we have used the Rec-Seq system to measure the kine>cs of 48S PIC forma>on transcriptome-wide in the absence of Ded1 and find that the mean rate constant observed (~2 min-1) is also within the range of es>mates of the rate of transla>on ini>a>on in vivo in yeast. We hope to publish this analysis in a future manuscript.

It has been suggested that Ded1 and its human homolog DDX3X could play a role in subunit joining postscanning (Wang et al. 2022, Cell and Geissler et al. 2012 Nucleic Acids Res). Could the authors poten5ally inves5gate this by adding GTP, eIF5B and 60S subunits into the reac5on mixture and isola5ng 80S complexes?

This is a very interes>ng sugges>on. One of our plans with the Rec-Seq system is to see if we can also observe 80S forma>on with it and dis>nguish 80S from 48S complexes. Although we haven’t yet tried this and there might be technical obstacles to doing it, if it works we would like to examine the poten>al effects of Ded1, as suggested. We now men>on this possibility in the Discussion sec>on (lines 709-716 and 810-817).

An incuba5on 5me of 15 minutes is quite long on the 5mescale of transla5on ini5a5on. Presumably, the compe55on for 40S among mRNAs is par5ally kine5cally controlled so it would be interes5ng if the authors could do a 5me series on the incuba5on 5me. Does Ded1 increase ini5a5on on more structured UTRs even at shorter incuba5ons or are those only observed with longer incuba5ons?

We agree. See the response to the ques5on about kine5cs above.

Does GDPNP lead to off-pathway events? What happens when GTP is used in the TC? Presumably in the absence of eIF5B the 48S PIC should remain stalled at the start codon.

In previous experiments in the recons>tuted system, we showed that using GTP instead of GDPNP resulted in 48S complexes that were less stable than those stalled prior to GTP hydrolysis (e.g., Algire et al. [2002] RNA 8:382-397). This is presumably because eIF2•GDP and eIF5 release from the complex and the Met-tRNAi can dissociate in the absence of subunit joining. Although we haven’t tried it in the Rec-Seq system, we suspect that the resul>ng PICs would fall apart during sucrose gradient sedimenta>on.

The authors use assembly of a 48S PIC at the start codon as evidence of scanning but could use more evidence to back this claim up. Does removing the cap structure on the two luciferase mRNA controls disrupt ini5a5on using this approach? That would be direct evidence of 5' end 40S loading and scanning to the start codon.

In previous work using the recons>tuted system, we studied the effect of the 5’-cap on 48S PIC forma>on (Mitchell et al. [2010] Mol. Cell 39:950-962; Yourik et al. [2017] eLife hhps://elifesciences.org/ar>cles/31476 ). We found that stable 48S PIC forma>on is strongly dependent on the presence of the 5’-cap. In addi>on, the cap prevents off-pathway events and enforces a requirement for the full set of ini>a>on factors to achieve efficient 48S PIC forma>on. As the reviewer indicates, the cap-dependence of the system supports the conclusion that 5’end loading and scanning take place. We have now added this informa>on and the relevant cita>ons to the Introduc>on (lines 147-153). We thank the reviewer for poin>ng out this oversight. It should also be noted that the cases of mRNAs in which 5’UTR transla>on is increased by addi>on of Ded1 support the conclusion that the factor promotes ahachment of the PIC to the 5’ ends of mRNAs and subsequent 5’ to 3’ scanning, as noted in lines 608-618.

The authors state that "The correla5on between CDS length and RE could be indirect because CDS length also correlates with 5'UTR length". Could the authors bin the transcripts into different 5' UTR length ranges and then probe for CDS length differences on RE for each 5' UTR length bin? This could be useful to truly parse the mechanism by which CDS length is influencing RE.

This was an excellent sugges>on. We now include this analysis in a new supplementary figure, Figure 3S-2. Corresponding text was added in lines 380-387:

“Importantly, correlations between Ded1 stimulation and 5’ UTR lengths are evident for all three groups of mRNAs containing distinct ranges of CDS lengths (Fig. 3-S2A-C). In contrast, a marked correlation between Ded1 stimulation and CDS length was detected only for the group of mRNAs with longest 5’UTRs (Fig. 3-S2D-F), and only the latter group showed a clear correlation between 5’UTR length and CDS length (Fig. 3-S2G-I). Thus, the correlation between Ded1 stimulation and CDS length appears to be indirect, driven by the tendency for the mRNAs with the longest 5’UTRs to also have correspondingly longer CDSs.”

We thank the reviewer for this very useful idea.

In Figure 3I, why does RE dip for the middle bins of CDS length in both 100 nM and 500 nM condi5ons, and then rise back up for the later bins? In other words, why do the shortest and longest CDS have the best RE in the presence of ded1?

We do not know the reason for this dip and now say this in the Results on lines 377-378.

The discussion sec5on would be well served to discuss proposed roles of Ded1 post-scanning and how those fit, if at all, with the data presented throughout the manuscript.

We have now added this to the Discussion (lines 709-716 and 810-817). We thank the reviewer for poin>ng out this oversight.

Minor comments:

• Define bins on figures rather than using bin number for axis labels. For example, Figure 3A-D x-axis labels indicate the length range of each bin.

Thank you for the sugges>on. We have made this change.

• Figure 3I: the data seem to indicate that shortest CDSs have a ded1 dependency similar to the longest CDSs. This result seems inconsistent with the given rela5onship between UTR length, structure, CDS length. Please clarify.

See answer to this ques>on above.

• Replace qualita5ve statements, such as "substan5ally smaller reduc5ons" with percent change, numbers, etc.

We have tried to replace qualita>ve statements with quan>ta>ve ones, where possible.

Author Response

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

eLife assessment

This fundamental study advances our understanding of the cell specific treatment of cone photoreceptor degeneration by Txnip. The evidence supporting the conclusions is convincing with rigorous genetic manipulation of Txnip mutations, however, there are a few areas in which the article may be improved through further analysis and application of the data. The work will be of broad interest to vision researchers, cell biologists and biochemists.

Reviewer #1 (Public Review):

Summary:

This is a follow-up study to the authors' previous eLife report about the roles of an alpha-arrestin called protein thioredoxin interacting protein (Txnip) in cone photoreceptors and in the retinal pigment epithelium. The findings are important because they provide new information about the mechanism of glucose and lactate transport to cone photoreceptors and because they may become the basis for therapies for retinal degenerative diseases.

Strengths:

Overall, the study is carefully done and, although the analysis is fairly comprehensive with many different versions of the protein analyzed, it is clearly enough described to follow. Figure 4 greatly facilitated my ability to follow, understand and interpret the study.

Weaknesses:

I have just one concern that I would like the authors to address. It is about the text that begins at line 133: "We assayed their ability to clear GLUT1 from the RPE surface (Figure 2A)". Please provide more details about this. From the figure it appears that n = 1 for this experiment, but given how careful the authors are with these types of studies that seems unlikely. How did the authors quantify the ability to clear GLUT1 from the surface? Was it cleared from both the apical and basal surface? (It is hard to resolve the apical and basal surfaces in the images provided). The experiments shown in Fig. 1H and Fig. 1I of PMID 31365873 shows how GLUT1 disappears only from the apical surface (under the conditions of that experiment and through the mechanism described in their text). It would be helpful for the authors to discuss their current results in the context of that experiment.

We repeated all eight AAV-Best1-Txnip alleles for RPE GLUT1 staining with more than three eyes of each condition. We also quantified the GLUT1 intensity on the RPE basal surface. A new Figure 2-figure supplement 1 with these data has been added to this submission. The results and conclusions are similar to those in our initial submission.

As mentioned in our provisional responses: GLUT1 on the basal surface of the RPE is more easily scored than that on the apical surface. The photoreceptor inner segments and Müller glia microvilli also have GLUT1, and their processes are juxtaposed and/or intertwined with the apical processes of the RPE, making the apical process GLUT1 staining of the RPE much more difficult to score. In some sections where the RPE and the retina separate, we can score the apical process GLUT1 staining of the RPE, but we do not always have this situation in our sections. The current quantification in the new Figure 2-figure supplement 1 thus concerns only the basal staining.

As a separate issue, Reviewer #1 mentioned the work of another group (Wang et al., 2019, PMID: 31365873), which claimed that, on the apical surface of the RPE, GLUT1 is down-regulated in a RP mouse strain, RhoP23H. We have not consistently observed such a down-regulation of GLUT1 in other RP mouse strains such as rd1, rd10 or Rho-/- (unpublished data; see review Xue and Cepko, 2023, PMID: 37460158). However, as we pointed out above, it is difficult to score GLUT1 staining on the RPE apical surface. It is even more difficult in the degenerating retina where RPE and photoreceptor processes degenerate. For reference, one can see images of degenerating RPE apical processes in Wu et al. 2021 (PMID: 33491671).

Reviewer #2 (Public Review):

The hard work of the authors is much appreciated. With overexpression of a-arrestin Txnip in RPE, cones and the combined respectively, the authors show a potential gene agnostic treatment that can be applied to retinitis pigmentosa. Furthermore, since Txnip is related to multiple intracellular signaling pathway, this study is of value for research in the mechanism of secondary cone dystrophy as well.

There are a few areas in which the article may be improved through further analysis and application of the data, as well as some adjustments that should be made in to clarify specific points in the article.

Reviewer #3 (Public Review):

Summary:

Xue et al. extended their groundbreaking discovery demonstrating the protective effect of Txnip on cone photoreceptor survival. This was achieved by investigating the protection of cone degeneration through the overexpression of five distinct mutated variants of Txnip within the retinal pigment epithelium (RPE). Moreover, the study explored the roles of two proteins, HSP90AB1 and Arrdc4, which share similarities or associations with Txnip. They found the protection of Txnip in RPE cells and its mechanism is different from its protection in cone cells. These discoveries have significant implications for advancing our understanding of the mechanisms underlying Txnip's protection on cone cells.

Strengths: (1) Identify the roles of different Txnip mutations in RPE and their effects on the expression of glucose transporter

(2) Dissect the mechanism of Txnip in RPE vs Cone photoreceptors in retinal degeneration models.

(3) Explore the functions of ARrdc4, a protein similar to Txnip and HSP90AB1 in cone degeneration.

Weaknesses:

(1) Arrdc4 has deleterious effect on cone survival but no discussion on its mechanism.

(2) Inhibition of HSP90 is known to cause retinal generation. It is unclear why inhibition enhances the protection of Txnip.

As mentioned in our provisional responses, little was known about the function of Arrdc4 or HSP90AB1 in cones. We summarize some of the recent discoveries regarding these two proteins in the new Discussion:

“Arrdc4, the most similar α-arrestin protein to Txnip that also has Arrestin N- and C- domains, accelerated RP cone death when transduced via AAV (Figure 1). This observation suggests that Txnip has unique functions that protect RP cones. Recently, Arrdc4 has been proposed to be critical for liver glucagon signaling, which could be negated by insulin (Dagdeviren et al. 2023). The implication of this potential role in RP cone survival is unclear, but interestingly, the activation of the insulin/mTORC1 pathway is beneficial to RP cone survival (Punzo et al. 2009; Venkatesh et al. 2015).”

“Little is known about the function of HSP90AB1. Knocking down Hsp90ab1 improved mitochondrial metabolism of skeletal muscle in a diabetic mouse model (Jing et al. 2018). Knocking out HSP90AA1, a paralog of HSP90AB1 which has 14% different amino acids, led to rod death and correlated with PDE6 dysregulation (Munezero et al. 2023). Inhibiting HSP90AA1 with small molecules transiently delayed cone death in human retinal organoids under low glucose conditions (Spirig et al. 2023). However, the exact role of HSP90AA1 in photoreceptors needs to be clarified, and the implications for HSP90AB1 in RP cones are still unclear. ”

In addition, we used AlphaFold Multimer, an AI algorithm based on AlphaFold-2, to explore the possible interaction between TXNIP, PARP1 and HSP90AB1 in the revision. One of the predicted models is shown as the new Figure 5-figure supplement 2. The C-terminus of Txnip is predicted to link HSP90AB1 and PARP1 together in this model.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I have just one concern that I would like the authors to address. It is about the text that begins at line 133: "We assayed their ability to clear GLUT1 from the RPE surface (Figure 2A)". Please provide more details about this. From the figure it appears that n = 1 for this experiment, but given how careful the authors are with these types of studies that seems unlikely. How did the authors quantify the ability to clear GLUT1 from the surface? Was it cleared from both the apical and basal surface? (It is hard to resolve the apical and basal surfaces in the images provided). The experiments shown in Fig. 1H and Fig. 1I of PMID 31365873 shows how GLUT1 disappears only from the apical surface (under the conditions of that experiment and through the mechanism described in their text). It would be helpful for the authors to discuss their current results in the context of that experiment.

See our responses to Review #1’s public review section above.

Also, is the clearance from the RPE plasma membrane homogenous throughout the RPE monolayer?

In the area of AAV infection, the effects are very homogenous. In the uninfected area, the clearance does not occur, and we consider the uninfected area of the same eye to be an excellent internal control.

A statistical analysis (as was provided for other experiments in the manuscript) would help to make the surprising conclusion about C.Txhniip.C247S more convincing.

In this revision, we used the Mann-Whitney U test with the Bonferroni correction for GLUT1 intensity quantification. For the cone survival statistics, we used the t-test or ANOVA with Dunnett multiple comparison test. The information has been added to each figure legend.

Another improvement I suggest for this figure is to include normal full length Txnip as a positive control to show how completely it removes GLUT1 from the surface.

Added. See the new Figure 2-figure supplement 1.

Another point that should be discussed is - when Txnip prevents GLUT1 from reaching the surface does all the GLUT1 get fully degraded within the cell. A brief description of how Txnip influences GLUT1 stability and localization would be helpful.

We are unable to track the fate of the GLUT1 after it is removed, i.e. we do not see definitive intracellular staining. We do not know if this is due to degradation or a hidden epitope.

Minor point

(1) Confusing citation on lines 99-100: "We previously showed that overexpressing the Txnip wt allele in the RPE using an RPE specific promoter, derived from the Best1 gene (Esumi et al. 2009),.." makes it sound like Esumi et al. is the citation for their previous study, which is not correct.

We have amended this to: "We previously showed (Xue et al. 2021) that overexpressing the Txnip wt allele in the RPE using an RPE-specific promoter, derived from the Best1 gene (Esumi et al., 2009), did not improve RP cone survival."

Reviewer #2 (Recommendations For The Authors):

Regarding the manuscript, here are some suggestions that authors can take into consideration for the completeness of the study:

(1) The text references the relationship between α-arrestin and glucose metabolism in cone cells, but fails to provide an explanation for its specific involvement in glucose metabolism. Consequently, readers may struggle to discern the targeted metabolic pathway.

We understand this point from Reviewer, and would love to know more about its mechanism, which is one reason why we undertook the current study. The mechanism(s) by which Txnip affects metabolism remains to be elucidated. To summarize our findings from our previous study, we showed that LDHB, which converts lactate to pyruvate, was required for Txnip-mediated rescue. Addition of the LDHB gene, however, did not boost rescue. We also showed that mitochondrial size and membrane potential were improved, and the Na/K pump function was improved, in Txnip-treated cones. Improved mitochondria were not sufficient, however, as revealed by a PARP-1 KO mouse with improved mitochondria that did not extend cone survival. In addition, using a Txnip mutant that does not remove the glucose transporter, we still saw cone rescue, so this function cannot be required for Txnip-mediated rescue. How does Txnip lead to improved mitochondria and to a reliance on lactate? We do not know.

(2) Although the author conducted an experiment on arrdc14 due to its similarity to Txnip, the lack of clarification on why arrdc4, with a 60% amino acid similarity, did not yield the same effects as Txnip remains unaddressed. Highlighting structural disparities or differences in intracellular signaling pathways could potentially shed light on this incongruity. Subsequently, an additional experiment may be warranted to test the hypothesis regarding the effective component of α-arrestin for cone rescue.

Additional experiments are needed to learn of the relevant differences between Arrdc4 and Txnip, but are beyond the scope of our work at the present. However, we have added a paragraph on newly published data on the function of Arrdc4 in the new Discussion:

“Arrdc4, the most similar α-arrestin protein to Txnip that also has Arrestin N- and C- domains, accelerated RP cone death when transduced by AAV (Figure 1). This observation suggests that Txnip has unique functions that protect RP cones. Recently, Arrdc4 has been proposed to be critical for liver glucagon signaling, which could be negated by insulin (Dagdeviren et al. 2023). The implication of this potential role regarding RP cone survival is unclear, but interestingly, the activation of the insulin/mTORC1 pathway is beneficial to RP cone survival (Punzo et al. 2009; Venkatesh et al. 2015).”

(3) The utilization of distinct mutant Txnip variants to impact RPE, cones, and their combined influence is noted. A comparative table elucidating the impact of cone rescue on these three targets would greatly enhance clarity.

We presented these data in Figure 4 in a table format.

Additionally, the text does not definitively establish whether Txnip.C247S.LL351 and 352AA, as well as Txnip.C247S, indeed manifest discrepancies when exclusively affecting RPE.

We edited a sentence in Results to: “Similar to Best1-wt Txnip (Xue et al., 2021), Best1-Txnip.C247S did not show significant improvement of cone survival, ruling out the C247S mutation alone as promoting the cone survival by Best1-Txnip.C247S.LL351 and 352AA.”

(4) While the text mentions that Txnip stimulates lactate utilization within cones, it remains unclear whether this effect extends to RPE. If applicable, this trait could potentially contribute to its role in cone rescue.

We agree with the Reviewer, and hope to address this question in our next study.

(5) The discussion introduces the notion that one potential mechanism for cone rescue by Txnip.C247S involves facilitating unhindered movement of Thioredoxin for redox processes. To validate this hypothesis and elucidate the mechanics of Txnip's involvement in cone rescue, it may be prudent to conduct further experiments concentrating on the interaction between Txnip and thioredoxin. Alternatively, an experiment aimed at upregulating Thioredoxin expression would be a valuable addition.

We hope to address this question in the future. However, the effect may be more complicated than our simple hypothesis regarding release of Thioredoxin. More than a dozen proteins were found to differentially interact with Txnip vs. Txnip.C247S (Forred et al. 2016).

Reviewer #3 (Recommendations For The Authors):

(1) Glucose transporter 1 is identified as an important mechanism in the protection of cone degeneration. It is unclear why GLut1 is upregulated in retinal cells although the expression of Txnip mutants are specifically in the RPE in Figure 2.

This retinal GLUT1 upregulation was not consistently observed in the treated eyes, so we did not comment on it in the text.

(2) Mutant N. Txnip was mentioned in the discussion that it causes obvious retinal degeneration. The quantification of retinal thickness from Figure 2 will be more rigorous.

Unlike the robust effects of Best1-N.Txnip on RPE GLUT1 level, this negative effect of Best1-N.Txnip on ONL thickness was not consistent. This result does not undermine the other major conclusions. Therefore, we deleted the related sentence of the original text: “This hypothesis is supported by the observation that N.Txnip led to an obvious thinning of the outer nuclear layer of the wt retina, reflecting a loss of photoreceptors”. We did leave in the related finding as follows:

“The N-terminal half of Txnip (1-228aa) might exert harmful effects in the RPE, that negate the beneficial effects from the C-terminal half, suggested by the observation that its removal, in the C-terminal 149-397 allele, led to better cone survival when expressed in the RPE (Figure 2). In cones, the C-terminal half, including the C-terminal IDR tail, may cooperate with the N-terminal half, or negate its negative effects, to benefit RP cone survival. However, the C-terminal half is not sufficient for cone rescue when expressed in cones, as the 149-397 allele did not rescue.”

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this manuscript, Sang et al. proposed a pair of IR60b-expressing pharyngeal neurons in Drosophila use IR25a, IR76b, and IR60b channels to detect high Na+ and limit its consumption. Some of the key findings that support this thesis are: 1) animals that lacked any one of these channels - or with their IR60b-expressing neurons selectively silenced - showed much reduced rejection of high Na+, but restored rejection when these channels were reintroduced back in the IR60b neurons; 2) animals with TRPV artificially expressed in their IR60b neurons rejected capsaicin-laced food whereas WT did not; 3) IR60b-expressing neurons exhibited increased Ca2+ influx in response to high Na+ and such response went away when animals lacked any of the three channels.

Strengths:

The experiments were thorough and well designed. The results are compelling and support the main claim. The development and the use of the DrosoX two-choice assay put forward for a more quantitative and automatic/unbiased assessment for ingestion volume and preference.

Weaknesses:

There are a few inconsistencies with respect the the exact role by which IR60b neurons limit high salt consumption and the contribution of external (labellar) high-salt sensors in regulating high salt consumption. These weaknesses do not significantly impact the main conclusion, however.

Reviewer #2 (Public Review):

Summary:

In this paper, Sang et al. set out to identify gustatory receptors involved in salt taste sensation in Drosophila melanogaster. In a two-choice assay screen of 30 Ir mutants, they identified that Ir60b is required for avoidance of high salt. In addition, they demonstrate that activation of Ir60b neurons is sufficient for gustatory avoidance using either optogenetics or TRPV1 to specifically activate Ir60b neurons. Then, using tip recordings of labellar gustatory sensory neurons and proboscis extension response behavioral assays in Ir60b mutants, the authors demonstrate that Ir60b is dispensable for labellar taste neuron responses to high salt and the suppression of proboscis extension by high salt. Since external gustatory receptor neurons (GRNs) are not implicated, they look at Poxn mutants, which lack external chemosensory sensilla but have intact pharyngeal GRNs. High salt avoidance was reduced in Poxn mutants but was still greater than Ir60b mutants, suggesting that pharyngeal gustatory sensory neurons alone are sufficient for high salt avoidance. The authors use a new behavioral assay to demonstrate that Ir60b mutants ingest a higher volume of sucrose mixed with high salt than control flies do, suggesting that the action of Ir60b is to limit high salt ingestion. Finally, they identify that Ir60b functions within a single pair of gustatory sensory neurons in the pharynx, and that these neurons respond to high salt but not bitter tastants.

Strengths:

A great strength of this paper is that it rigorously corroborates previously published studies that have implicated specific Irs in salt taste sensation. It further introduces a new role for Ir60b in limiting high salt ingestion, demonstrating that Ir60b is necessary and sufficient for high salt avoidance and convincingly tracing the action of Ir60b to a particular subset of gustatory receptor neurons. Overall, the authors have achieved their aim by identifying a new gustatory receptor involved in limiting high salt ingestion. They use rigorous genetic, imaging, and behavioral studies to achieve this aim, often confirming a given conclusion with multiple experimental approaches. They have further done a great service to the field by replicating published studies and corroborating the roles of a number of other Irs in salt taste sensation. An aspect of this study that merits further investigation is how the same gustatory receptor neurons and Ir in the pharynx can be responsible for regulating the ingestion of both appetitive (sugar) and aversive tastants (high salt).

A previous report published in eLife from John Carlson’s lab (Joseph et al, 2017) showed that the Ir60b GRN in the pharynx responds to sucrose resulting in sucrose repulsion. Thus, stimulation of this pharyngeal GRN results in gustatory avoidance only, not both attraction and avoidance. (lines 205-207)

Weaknesses:

There are several weaknesses that, if addressed, could greatly improve this work.

(1) The authors combine the results and discussion but provide a very limited interpretation of their results. More discussion of the results would help to highlight what this paper contributes, how the authors interpret their results, and areas for future study.

We agree and have now separated the Results and Discussion, and in so doing have greatly expanded discussion of the results.

(2) The authors rename previously studied populations of labellar GRNs to arbitrary letters, which makes it difficult to understand the experiments and results in some places. These GRN populations would be better referred to according to the gustatory receptors they are known to express.

One of the corresponding authors (Craig Montell) introduced this alternative GRN nomenclature in a review in 2021: Montell, C. (Drosophila sensory receptors—a set of molecular Swiss Army Knives. Genetics 217, 1-34) (Montell, 2021). We are not fans of referring to different classes of GRNs based on the receptors that they express since it is not obvious which receptors to use. For example, the GRNs that respond to bitter compounds all express multiple GR co-receptors. The same is true for the GRNs that respond to sugars. The former system of referring to GRNs simply as sugar, bitter, salt and water GRNs is also not ideal since the repertoire of chemicals that stimulates each class is complex. For example, the Class A GRNs (formerly sugar GRNs) are also activated by low Na+, glycerol, fatty acids, and acetic acid, while the B GRNs (former bitter GRNs) are also stimulated by high Na+, acids, polyamines, and tryptophan. In addition, there are five classes of GRNs. At first mention of the Class A—E GRNs, we mention the most commonly used former nomenclature of sugar, bitter, salt and water GRNs. In addition, for added clarify, we now also include a mention of one of the receptors that mark each class. (lines 51-59)

(3) The conclusion that GRNs responsible for high salt aversion may be inhibited by those that function in low salt attraction is not well substantiated. This conclusion seems to come from the fact that overexpression of Ir60b in salt attraction and salt aversion sensory neurons still leads to salt aversion, but there need not be any interaction between these two types of sensory neurons if they act oppositely on downstream circuits.

We did not make this claim.

(4) The authors rely heavily on a new Droso-X behavioral apparatus that is not sufficiently described here or in the previous paper the authors cite. This greatly limits the reader's ability to interpret the results.

We expanded the description of the apparatus in the Droso-X assay section of the Materials and Methods. (lines 588-631)

Reviewer #3 (Public Review):

Summary:

Sang et al. successfully demonstrate that a set of single sensory neurons in the pharynx of Drosophila promotes avoidance of food with high salt concentrations, complementing previous findings on Ir7c neurons with an additional internal sensing mechanism. The experiments are well-conducted and presented, convincingly supporting their important findings and extending the understanding of internal sensing mechanisms. However, a few suggestions could enhance the clarity of the work.

Strengths:

The authors convincingly demonstrate the avoidance phenotype using different behavioral assays, thus comprehensively analyzing different aspects of the behavior. The experiments are straightforward and well-contextualized within existing literature.

Weaknesses:

Discussion

While the authors effectively relate their findings to existing literature, expanding the discussion on the surprising role of Ir60b neurons in both sucrose and salt rejection would add depth. Additionally, considering Yang et al. 2021's (https://doi.org/10.1016/j.celrep.2021.109983) result that Ir60b neurons activate feeding-promoting IN1 neurons, the authors should discuss how this aligns with their own findings.

Yang et al. demonstrated that the activation of Ir60b neurons can trigger the activation of IN1 neurons akin to pharyngeal multimodal (PM) neurons, potentially leading to enhanced feeding (Yang et al, 2021). However, our research reveals a specific pattern of activation for Ir60b neurons. Instead of being generalists, they are specialized for certain sugars, such as sucrose and high salt. Consequently, while Ir60b GRNs activate IN1 neurons, we contend that there are other neurons in the brain responsible for inhibiting feeding. (lines 412-417)

Lines 187: The discussion primarily focuses on taste sensillae outside the labellum, neglecting peg-type sensillae on the inner surface. Clarification on whether these pegs contribute to the described behaviors and if the Poxn mutants described also affect the pegs would strengthen the discussion.

We added the following to the Discussion section. “We also found that the requirement for Ir60b appears to be different when performing binary liquid capillary assay (DrosoX), versus solid food binary feeding assays. When we employed the DrosoX assay to test mutants that were missing salt aversive GRNs in labellar bristles but still retained functional Ir60b GRNs, the flies behaved the same as wild-type flies (e.g. Figure 3J and 3L). However, using solid food binary assays, Poxn mutants, which are missing labellar taste bristles but retain Ir60b GRNs (LeDue et al, 2015), displayed repulsion to high salt food that was intermediate between control flies and the Ir60b mutant (Figure 2J). Poxn mutants retain taste pegs (LeDue et al., 2015), and these hairless taste organs become exposed to food only when the labial palps open. We suggest that there are high-salt sensitive GRNs associated with taste pegs, which are accessed when the labellum contacts a solid substrate, but not when flies drink from the capillaries used in DrosoX assays. This explanation would also account for the findings that the Ir60b mutant is indifferent to 300 mM NaCl in the DrosoX assay (Figure 3B), but prefers 1 mM sucrose alone over 300 mM NaCl and 5 mM sucrose in the solid food binary assay (Figure 1B).”. (lines 430-444)

In line 261 the authors state: "We attempted to induce salt activation in the I-type sensilla by ectopically expressing Ir60b, similar to what was observed with Ir56b 8; however, this did not generate a salt receptor (Figures S6A)"

An obvious explanation would be that these neurons are missing the identified necessary co-receptors Ir76b and Ir25a. The authors should discuss here if the Gr33a neurons they target also express these co-receptors, if yes this would strengthen their conclusion that an additional receptor might be missing.

We clarified this point in the Discussion section as follows, “An open question is the subunit composition of the pharyngeal high Na+ receptor, and whether the sucrose/glucose and Na+ receptors in the Ir60b GRN are the same or distinct. Our results indicate that the high salt sensor in the Ir60b GRN includes IR25a, IR60b and IR76b since all three IRs are required in the pharynx for sensing high levels of NaCl. I-type sensilla do not elicit a high salt response, and we were unable to induce salt activation in I-type sensilla by ectopically expressing Ir60b, under control of the Gr33a-GAL4. This indicates that IR25a, IR60b and IR76b are insufficient for sensing high Na+. The inability to confer a salt response by ectopic expression of Ir60b was not due to absence of Ir25a and Ir76b in Gr33a GRNs since Gr33a and Gr66a are co-expressed (Moon et al, 2009), and Gr66a GRNs express Ir25a and Ir76b (Li et al, 2023). Thus, the high salt receptor in Ir60b GRNs appears to require an additional subunit. Given that Na+ and sugars are structurally unrelated, we suggest that the Na+ and sucrose/glucose receptors do not include the identical set of subunits, or that that they activate a common receptor through disparate sites”. (lines 464-477)

Methods

The description of the Droso-X assay seems to be missing some details. Currently, it is not obvious how the two-choice is established. Only one capillary is mentioned, I assume there were two used? Also, the meaning of the variables used in the equation (DrosoX and DrosoXD) are not explained.

We expanded the description of the apparatus in the Droso-X assay section of the Materials and Methods. (lines 588-631)

The description of the ex-vivo calcium imaging prep. is unclear in several points:

(1) It is lacking information on how the stimulus was applied (was it manually washed in? If so how was it removed?).

We expanded the description of the apparatus in the ex vivo calcium imaging section of the Materials and Methods. (lines 682-716)

(2) The authors write: "A mild swallow deep well was prepared for sample fixation." I assume they might have wanted to describe a "shallow well"?

We deleted the word “deep.”.(line 691)

(3) "...followed by excising a small portion of the labellum in the extended proboscis region to facilitate tastant access to pharyngeal organs." It is not clear to me how one would excise a small portion of the labellum, the labellum depicts the most distal part of the proboscis that carries the sensillae and pegs. Did the authors mean to say that they cut a part of the proboscis?

Yes. We changed the sentence to “…followed by excising a small portion of the extended proboscis to facilitate tastant access to the pharyngeal organs.”.(lines 693)-695

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

In this manuscript, Sang et al. proposed a pair of IR60b-expressing pharyngeal neurons in Drosophila use IR25a, IR76b, and IR60b channels to detect high Na+ and limit its consumption. Some of the key findings that support this thesis are: 1) animals that lacked any one of these channels - or with their IR60b-expressing neurons selectively silenced - showed much reduced rejection of high Na+, but restored rejection when these channels were reintroduced back in the IR60b neurons; 2) animals with TRPV artificially expressed in their IR60b neurons rejected capsaicin-laced food whereas WT did not; 3) IR60b-expressing neurons exhibited increased Ca2+ influx in response to high Na+ and such response went away when animals lacked any of the three channels. In general, I find the collective evidence presented by the authors convincing. But I feel the MS can benefit from having a discussion session and a few simple experiments. Below I listed some inconsistencies I hope the authors can address or at least discuss.

We have now added a Discussion section, and expanded the discussion.

(1) The role of IR60b neurons on suppressing PER appeared inconsistent. On the one hand, optogenetic activation of these neurons suppressed PER (Fig 1D), on the other hand, IR60b mutants were as competent to suppress PER in response to high salt as WT (Fig 2G). Are pharyngeal neurons expected to modulate PER? It might be worth including a retinal-free or genotype control to ascertain the PER suppression exhibited by IR60b>CsChrimson is genuine.

Please note that Figure 2G is now Figure 2H.

Our interpretation is that activation of aversive GRNs by high salt either in labellar bristles or in the pharynx is sufficient to inhibit repulsion to high salt. Consistent with this conclusion, optogenetic activation of Ir60b GRNs, which are specific to the pharynx, is sufficient to reduce the PER to sucrose containing food (Figure 1D). However, mutation of Ir60b has no impact on the PER to sucrose plus high (300 mM) NaCl since the high-salt activated GRNs in labellar bristles are not impaired by the Ir60b mutation. In contrast, Ir25a and Ir76b are required in both labellar bristles and in the pharynx to reject high salt. As a consequence, mutation of either Ir25a or Ir76b impairs the repulsion to high salt. Thus, there is no inconsistency between the optogenetics and PER results. We clarified this point in the Discussion section. In terms of controls for IR60b>CsChrimson, we show that UAS-CsChrimson alone or UAS-CsChrimson in combination with the Gr5a driver has no impact on the PER (Figure 1D). In addition, we now include a retinal free control (Figure 1D). These findings provide the key genetic controls and are described in the Results section. (lines 167-170)

(2) The role of labellar high-salt sensors in regulating salt intake appeared inconsistent. On the one hand, they appeared to have a role in limiting high salt consumption because poxn mutants were significantly more receptive to high salt than WT (Fig. 2J). On the other hand, selectively restoring IR76b or IR25a in only the IR60b neurons in these mutants - thus leaving the labellar salt sensors still defective - reverted the flies to behave like WT when given a choice between sucrose vs. sucrose+high salt (Fig 3J, L).

We now offer an explanation for these seemingly conflicting results in the Discussion section. When we employed the DrosoX assay with mutants with functional Ir60b GRNs, but were missing salt aversive GRNs in labellar bristles, the flies behaved the same as control flies (e.g. Figure 3J and L). However, using solid food binary assays, Poxn mutants, which are missing labellar taste bristles but retain Ir60b GRNs (LeDue et al., 2015), display aversion high salt food intermediate between control and Ir60b mutant flies (Figure 2J). Poxn mutants retain taste pegs (LeDue et al., 2015), which are exposed to food substrates only when the labial palps open. We suggest that the taste pegs harbor high salt sensitive GRNs, and they may be exposed to solid substrates, but not to the liquid in capillary tubes used in the DrosoX assays. This explanation would also account for the findings that the Ir60b mutant is indifferent to 300 mM NaCl in the DrosoX assay (Figure 3B), but prefers 1 mM sucrose alone over 300 mM NaCl and 5 mM sucrose in the solid food binary assay (Figure 1B). (lines 433-444)

(3) The behavior sensitivity of IR60b mutant to high salt again appeared somewhat inconsistent when assessed in the two different choice assays. IR60b mutant flies were indifferent to 300 mM NaCl when assayed with DrosoX (Fig 3A, B) but were clearly still sensitive to 300 mM NaCl when assayed with "regular" assay - they showed much reduced preference for 5 mM sucrose over 1 mM sucrose when the 5 mM sucrose was adulterated with 300 mM NaCl (Fig 1B).

The explanation provided above may also account for the findings that the Ir60b mutant is indifferent to 300 mM NaCl in the DrosoX assay (Figure 3B), but not when selecting between 300 mM NaCl and 5 mM sucrose versus 1 mM sucrose in the solid food binary assay (Figure 1B). Alternatively, the different behavioral responses might be due to the variation in sucrose concentrations in each of these two assays, which employed 5 mM sucrose in the solid food binary assay, as opposed to 100 mM sucrose in the DrosoX assay. This disparity in attractive valence between these two concentrations of sucrose might consequently impact feeding amount and preference. This point is now also included in the Discussion section. (lines 441-449)

(4) Given the IR60b neurons exhibited clear IR60b/IR25a/IR76b-dependent sucrose sensitivity, too, I am curious how the various mutant animals behave when given a choice between 100 mM sorbitol vs. 100 mM sorbitol + 300 mM NaCl, a food choice assay not complicated by the presence of sucrose. Similarly, I am curious if the Ca2+ response of IR60 neurons differs significantly when presented with 100 mM sucrose vs. when presented with 100 mM sucrose + 300 mM NaCl. In principle, the magnitude for the latter should be significantly larger than the former as animals appeared to be capable of discriminating these two choices solely relying on their IR60b neurons.

To investigate the aversion induced by high salt in the absence of a highly attractive sugar, such as sucrose, we combined 300 mM salt with 100 mM sorbitol, which is a tasteless but nutritive sugar (Burke & Waddell, 2011; Fujita & Tanimura, 2011). Using two-way choice assays, we found that the Ir25a, Ir60b, and Ir76b mutants exhibited substantial reductions in high salt avoidance (Figure 3—figure supplement 2A). In addition, we performed DrosoX assays using 100 mM sorbitol alone, or sorbitol mixed with 300 mM NaCl. Sorbitol alone provoked less feeding than sucrose since it is a tasteless sugar (Figure 3—figure supplement 2B and C). Nevertheless, addition of high salt to the sorbitol reduced food consumption (Figure 3—figure supplement 2B and C). (lines 300-308)

We also conducted a comparative analysis of the Ca2+ responses within the Ir60b GRN, examining its reaction to various stimuli, including 100 mM sucrose alone, 300 mM NaCl alone, and a combination of 100 mM sucrose and 300 mM NaCl. We found that the Ca2+ responses were significantly higher when we exposed the Ir60b GRN to 300 mM NaCl alone, compared with the response to 100 mM sucrose alone (Figure 4—figure supplement 1D). However, the GCaMP6f responses was not higher when we presented 100 mM sucrose with 300 mM NaCl, compared with the response to 300 mM NaCl alone (Figure 4—figure supplement 1D). (lines 360-367)

Minor issues

(1) The labels of sucrose concentration on Figure 2D were flipped.

This has been corrected.

(2) The phrasing of the sentence that begins in line 196 (i.e., "This suggests the internal sensor ...") is not as optimal.

We changed the sentence to, “We found that the aversive behavior to high salt was reduced in the Poxn mutants relative to the control (Figure 2J), consistent with previous studies demonstrating roles for GRNs in labellar bristles in high salt avoidance (Jaeger et al, 2018; McDowell et al, 2022; Zhang et al, 2013).”. (lines 217-219)

(3) In Line 231, I am not sure why the authors think ectopic expressing IR60b in labellar neurons would allow them to become activated by Na+. It seems highly unlikely to me, especially given IR60b also plays a role in sensing sugar.

We added the following paragraph to the Discussion addressing this point, “An open question is the subunit composition of the pharyngeal high Na+ receptor, and whether the sucrose/glucose and Na+ receptors in the Ir60b GRN are the same or distinct. Our results indicate that the high salt sensor in the Ir60b GRN includes IR25a, IR60b and IR76b since all three IRs are required in the pharynx for sensing high levels of NaCl. I-type sensilla do not elicit a high salt response, and we were unable to induce salt activation in I-type sensilla by ectopically expressing Ir60b, under control of the Gr33a-GAL4. This indicates that IR25a, IR60b and IR76b are insufficient for sensing high Na+. The inability to confer a salt response by ectopic expression of Ir60b was not due to absence of Ir25a and Ir76b in Gr33a GRNs since Gr33a and Gr66a are co-expressed (Moon et al., 2009), and Gr66a GRNs express Ir25a and Ir76b (Li et al., 2023). Thus, the high salt receptor in Ir60b GRNs appears to require an additional subunit. Given that Na+ and sugars are structurally unrelated, we suggest that the Na+ and sucrose/glucose receptors do not include the identical set of subunits, or that that they activate a common receptor through disparate sites.”. (lines 464-477)

Reviewer #2 (Recommendations For The Authors):

Line 41, acutely excessive salt ingestion can lead to death, not just health issues

We now state that, “consumption of excessive salt can contribute to various health issues in mammals, including hypertension, osteoporosis, gastrointestinal cancer, autoimmune diseases, and can lead to death.”. (lines 41-43)

Line 46, delete the comma after flies

Done. (line 47)

Lines 51-56: This description is unnecessarily confusing and does not cite proper sources. Renaming these GRNs arbitrarily can only create confusion, plus this description lacks nuance. If E GRNs are Ir94e positive, this description is out of date. Furthermore, If D GRNs are ppk23 and Gr66a positive then they will respond to both bitter and high salt.

Papers to consult: https://elifesciences.org/articles/37167 10.1016/j.cell.2023.04.038

We have now added citations. We prefer the A—E nomenclature, which was introduced in a 2021 Genetics review by one of the authors of this manuscript (Montell) (Montell, 2021) since naming different classes of GRNs on the basis of markers or as sweet, bitter, salt and water GRNs is misleading and an oversimplification. We cite the Genetics 2021 review, and for added clarity include both types of former names (markers and sweet, bitter, salt and water). Class D GRNs are not marked by Gr66a. The eLife reference cited above provided the initial rationale for stating that Class E GRNs are marked by Ir94e and activated by low salt. According to the Taisz et al reference (Cell 2023), the Class E GRNs, which are marked by Ir94e, are also activated by pheromones, which we now mention (Taisz et al, 2023). (lines 51-59)

Line 62, E GRNs are not required for low salt behaviors

We do not state that E GRNs are required for low salt behaviors, only that they sense low Na+ levels. (line 58)

Line 70-81 - Great deal of emphasis on labellar GRNs but then no mention of how pharyngeal GRNs fit into categories A-E

We devote the following paragraph to pharyngeal GRNs. We do not mention how they fit in with the A—E categories because it is not clear.

“In addition to the labellum and taste bristles on other external structures, such as the tarsi, fruit flies are endowed with hairless sensilla on the surface of the labellum (taste pegs), and three internal taste organs lining the pharynx, the labral sense organ (LSO), the ventral cibarial sense organ (VCSO), and the dorsal cibarial sense organ (DCSO), which also function in the decision to keep feeding or reject a food (Chen & Dahanukar, 2017, 2020; LeDue et al., 2015; Nayak & Singh, 1983; Stocker, 1994). A pair of GRNs in the LSO express a member of the gustatory receptor family, Gr2a, and knockdown of Gr2a in these GRNs impairs the avoidance to slightly aversive levels of Na+ (Kim et al, 2017). Pharyngeal GRNs also promote the aversion to bitter tastants, Cu2+, L-canavanine, and bacterial lipopolysaccharides (Choi et al, 2016; Joseph et al., 2017; Soldano et al, 2016; Xiao et al, 2022). Other pharyngeal GRNs are stimulated by sugars and contribute to sugar consumption (Chen & Dahanukar, 2017; Chen et al, 2021; LeDue et al., 2015). Remarkably, a pharyngeal GRN in each of the two LSOs functions in the rejection rather the acceptance of sucrose (Joseph et al., 2017).”. (lines 74-89)

Line 89, aversive --> aversion

We changed this part.

Line 90, gain of aversion capsaicin avoidance suggests they are sufficient for avoidance, not essential for avoidance.

We changed “essential” to “sufficient.”. (line 100)

Line 104, what are you recording from here? Labellar or pharyngeal GRNs

We added “S-type and L-type sensilla” to the sentence. (line 119)

Line 107, How are A GRNS marked with tdTomato? It is important to mention how you are defining A GRNs.

We modified the sentence as follows: “Using Ir56b-GAL4 to drive UAS-mCD8::GFP, we also confirmed that the reporter was restricted to a subset of Class A GRNs, which were marked with LexAop-tdTomato expressed under the control of the Gr64f-LexA (Figure 1—figure supplement 1D—F).”. (lines 120-123)

Line 124, should read "concentrated as sea water."

We made the change. (line 142)

Line 125, I am not sure what is meant by "alarm neurons"

We changed “additional pain or alarm neurons” to “nociceptive neurons.”. (line 144)

Line 141, Are you definitely A GRNs as only labellar GRNs, i.e. the Gr5a-GAL4 pattern with labellar plus few pharyngeal GRNs? Or are the defining it as Gr64f-GAL4 (i.e. labellar plus many pharyngeal GRNs)

We refer to the Class A—E GRNs as labellar GRNs. Therefore, in this instance, we removed the reference to A GRNs and B GRNs, and simply mention the drivers that we used (Gr5a-GAL4 and Gr66a-GAL4) to express UAS-CsChrimson. The modified sentence is, “As controls we drove UAS-CsChrimson under control of either the Gr5a-GAL4 or the Gr66a-GAL4.”. (lines 51-59, 160-161)

Line 180, labellar hairs--> labellar taste bristles

We made the change. (line 204)

Line 190, possess only --> only possess

We made the change. (line 216)

Line 202, Should this read increased?

Yes. We changed “reduced” to “increased.”. (line 225)

Line 206, The information provided here and in reference 47 was not sufficient for me to understand how the Droso-X system works and whether it has been validated. Better diagrams and much more description is required for the reader to understand this system and assess its validity

We now explain that the DrosoX “system consists of a set of five separately housed flies, each of which is exposed to two capillary tubes with different liquid food options. One capillary contained 100 mM sucrose and the other contained 100 mM sucrose mixed with 300 mM NaCl. The volume of food consumed from each capillary is then monitored automatically over the course of 6 hours and recorded on a computer.”. (lines 238-243)

Line 218-219, It would be helpful to expand on this to explain how the previous paper detected no difference. Is this because the contact time with the food is the same but the rate of ingestion is slower?

Yes. This is correct. We now clarify this point by stating that, “In a prior study, it was observed that the repulsion to high salt exhibited by the Ir60b mutant was indistinguishable from wild-type (Joseph et al., 2017). Specifically, the flies were presented with drop of liquid (sucrose plus salt) at the end of a probe, and the Ir60b mutant flies fed on the food for the same period of time as control flies (Joseph et al., 2017). However, this assay did not discern whether or not the volume of the high salt-containing food consumed by the Ir60b mutant flies was reduced relative to control flies. Therefore, to assess the volume of food ingested, we used the DrosoX system, which we recently developed (Figure 3—figure supplement 1A) (Sang et al, 2021). This system consists of a set of five separately housed flies, each of which is exposed to two capillary tubes with different liquid food options. One capillary contained 100 mM sucrose and the other contained 100 mM sucrose mixed with 300 mM NaCl. The volume of food consumed from each capillary was then monitored automatically over the course of 6 hours and recorded on a computer. We found that control flies consuming approximately four times more of the 100 mM sucrose than the sucrose mixed with 300 mM NaCl (Figure 3A). In contrast, the Ir25a, Ir60b, and Ir76b mutants consumed approximately two-fold less of the sucrose plus salt (Figure 3A). Consequently, they ingested similar amounts of the two food options (Figure 3B; ingestion index). Thus, while the Ir60b mutant and control flies spend similar amounts of time in contact with high salt-containing food when it is the only option (Joseph et al., 2017), the mutant consumes considerably less of the high salt food when presented with a sucrose option without salt.”. (lines 226-251)

Lines 231-235, Is this evidence for this, that Ir60b expression in the Ir25a or Ir76b pattern will induce high salt responses in the labellum? You should elaborate on this to clearly state what you mean rather than implying it. I do not think that overexpression of one Ir is enough evidence for this sweeping conclusion.

We agree. We eliminated this point. (lines 227-232)

Lines 261-263, Please elaborate here, how did you target the I-type sensilla and where are these neurons? So they already express Ir76b and Ir25a?

We now explain in the Results that, “We attempted to induce salt activation in the I-type sensilla by ectopically expressing Ir60b, under control of the Gr33a-GAL4. Gr33a is co-expressed with Gr66a (Moon et al., 2009), which has been shown to be co-expressed Ir25a and Ir76b (Li et al., 2023). When we performed tip recordings from I7 and I10 sensilla, we did not observe a significant increase in action potentials in response to 300 mM NaCl (Figure 4—figure supplement 1A), indicating that ectopic expression of Ir60b in combination with Ir25a and Ir76b is not sufficient to generate a high salt receptor.”. (lines 324-330)

Lines 300-303, The discussion needs to be greatly expanded. What is the proposed mechanism by which the same neurons/receptors can inhibit sucrose and high salt feeding? What is the author's interpretation of what this study adds to our understanding of taste aversion?

We have now added a Discussion section and greatly expanded the discussion.

Reviewer #3 (Recommendations For The Authors):

In line 73 there is a typo in "esophagus"

We changed this part.

In line 331, the use of a mixture of sucrose and "saponin" seems to be a mistake; "NaCl" is likely intended.

We made the correction. (lines 546 and 640)

On several occasions, the authors refer to the pharynx as a taste organ (for example 1st sentence of the abstract). I am not sure this is correct, the actual pharyngeal taste organs are the LSO, DSCO, and VSCO which are located in the pharynx.

We made the corrections. (lines 24, 90, 92, 93, and 356)

In line 155 the authors refer to Ir25a and Ir76b as "broadly tuned". I think it is not correct to refer to co-receptors this way, I'd suggest to just call them co-receptors.

We made the correction. (lines 177-178)

In line 182, stating "Gr2a is also expressed in the proboscis" is unclear. Clarify whether it refers to sensillae, pharyngeal taste organs, etc.

We clarified it refers to pharyngeal taste organs. (lines 206-207)

Line 253: "These finding imply that all three Irs are coexpressed in the pharynx." "The pharynx" is very unspecific, did the authors mean to say "the same neuron"?

We now clarify by saying “in the Ir60b GRN in the pharynx.”. (line 317)

Figures & Legends

I found it confusing that the same color scale is being reused for different panels with different meanings repeatedly and in inconsistent ways. For example in Figure 2, red and blue are being used for Ir25a² mutants, while blue is also being used for Gr64f-Gal4 and S type sensilla. It is also not easily visible nor mentioned in the caption which of the 3 color scales presented belong to which panels.

We modified the colors in the figures so that they are used in a consistent way. We now also define the colors in the legends.

In Figure 2 F-I, indicating the stimulus sequence in each panel would enhance clarity. The color scale in Figure 3 could benefit from explicit explanations of different shades in the caption for easier interpretation.

For example: "The ingestion of (a, dark color) 100 mM sucrose alone and (b, light color) in combination with 300 mM"

We made the suggested modification.

In Figure 4a the authors highlight that Ir76b and Ir25a label 2 neurons in the LSO. Did the imaging in 4c also capture the second cell, and if so did it respond to their stimulation?

No, the focal plane differs, and the signal in Figure 4C is considerably weaker compared to the immunohistochemistry shown in Figure 4A. Notably, the other neuron did not exhibit a response to NaCl.

In Figure 4f a legend for the color scale is missing, or the color might not be necessary at all. Also, the asterisks seem to be shifted to the right.

We fixed the shifted asterisks and eliminated the color.

Figure 4i is mislabeled 4f

We made the correction.

Author Response

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

This study highlights new insights into the mechanism of pheochromocytoma pathogenesis that remains poorly understood. In the context of hereditary syndromes, such as multiple endocrine neoplasia 2 (MEN-2), where RET mutation is the major driver of thyroid, parathyroid, and adrenal pathologies, including pheochromocytoma, this mechanistic dissection of RET and TMEM127 is fundamentally sound. While the significance was deemed important, the strength of the evidence was found to be solid,

Recognizing the limitations of models available for study of neuroendocrine cancers, and specifically for pheochromocytomas, we have revised and clarified the text of the current manuscript version and provide specific responses to the additional comments provided below, highlighting changes and new data.

Reviewer #1 (Recommendations For The Authors):

A current lack of pheochromocytoma cell lines and the use of generated cell lines for mechanistic studies presents a significant challenge that may undermine the inferred value of these findings in mock in vitro systems and question reproducibility in pheochromocytoma. Consideration for 3-dimensional patient-derived pheochromocytoma organoid in vitro and patient-derived organoid xenograft in vivo models will enable confirmation or refute novel findings described by the authors.

We agree completely with Reviewer 1 that ideally, we should replicate these findings with PCC-derived cells in vitro and in organoids. Despite many attempts, PCC cell lines have proved a major challenge for the field of neuroendocrine cancers. Cell line models are not available and PDOs have proven poorly growing and resistant to manipulations, such as CRISPR KOs or siRNA KD. In studies completed since the submission and review of the present manuscript, and subsequently published elsewhere, we have shown that RET protein is highly expressed in TMEM127-mutant PCC by immunohistochemistry. We also showed that the TMEM127-KO SH-SY5Y cell model does grow more robustly than Mock-KO cells in nude mice and that RET inhibition (Selpercatinib) does lead to tumor regression (Guo et al., 2023), suggesting that our findings may be reproducible in vivo. These findings, and potential caveats of the cell models used have been further discussed in the text.

Reviewer #2 (Recommendations For The Authors):

Most notably, all experiments are conducted in an isogenic single-cell line. This exposes the whole story to be potentially confounded by unknown variables.

In addition, studies would benefit from the adding back of TMEM127, or other methods to modulate endosome and plasma membrane dynamics to mechanistically secure the cause of the findings.

As suggested by Reviewer 2, we have generated a TMEM127 KO in HEK293, an unrelated cell line which expressed low levels of TMEM127 but does not express RET. Consistent with our findings in SH-SY5Y, we saw increased membrane accumulation of endogenous membrane proteins N-cadherin and transferrin receptor-1 in these cells in the absence of TMEM127. Additionally, re-expression of a wildtype TMEM127 (FLAG-TMEM127) in these cells led to dramatic decreases in membrane localization of these proteins (Supplemental Figure 1D). These data suggest that membrane accumulation is indeed TMEM127 dependent, and that these processes are not directly dependent on RET expression.

References

Guo, Q., Z.M. Cheng, H. Gonzalez-Cantu, M. Rotondi, G. Huelgas-Morales, P. Ethiraj, Z. Qiu, J. Lefkowitz, W. Song, B.N. Landry, H. Lopez, C.M. Estrada-Zuniga, S. Goyal, M.A. Khan, T.J. Walker, E. Wang, F. Li, Y. Ding, L.M. Mulligan, R.C.T. Aguiar, and P.L.M. Dahia. 2023. TMEM127 suppresses tumor development by promoting RET ubiquitination, positioning, and degradation. Cell Rep. 42:113070.

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

In this manuscript by DeHaro-Arbona et al., the authors wish to understand how a signaling pathway (Notch) is dynamically decoded to elicit a specific transcriptional output. In particular, they investigate the kinetic properties of Notch-responsive nuclear complexes (the DNA binding factor CSL and its co-activator Mastermind (mam) along with several candidate interacting partners). Their experimental model is the polytene chromosome of the Drosophila salivary gland, in which the naturally inactive Notch can be artificially induced through the expression of a constitutively active form of Notch.

The authors develop a series of CRISPR and transgenic lines enabling the live imaging of these complexes at a specific locus and in various backgrounds (genetic perturbations/drug treatments). This quantitative live imaging data suggests that Notch nuclear complexes form hubs, and the authors characterize their binding dynamics. Interestingly, they elegantly demonstrate that the content of these hubs and their kinetic properties can evolve, even within Notch ON cells. Hence, they propose the existence of distinct hubs, distinguishing an open (CSL), engaged (CSK-Mam), or active (CSL-Mam-Med-PolII) configuration in Notch ON cells and an inactive hub (in Notch OFF having previously been exposed to Notch) state, that would explain the surprising transcriptional memory that the authors observe hours after Notch withdrawal.

We thank the reviewer for this constructive summary of our work

Reviewer #2 (Public Review):

The manuscript from deHaro-Arbona et al, entitled "Dynamic modes of Notch transcription hubs conferring memory and stochastic activation revealed by live imaging the co-activator Mastermind", uses single molecule microscopy imaging in live tissues to understand the dynamics and molecular determinants of transcription factor recruitment to the E(spl)-C locus in Drosophila salivary gland cells under Notch-ON and -OFF conditions. Previous studies have identified the major players that are involved in transcription regulation in the Notch pathway, as well as the importance of general transcriptional coregulators, such as CBP/P300 and the Mediator CDK module, but the detailed steps and dynamics involved in these processes are poorly defined. The authors present a wealth of single molecule data that provides significant insights into Notch pathway activation, including:

(1) Activation complexes, containing CSL and Mam, have slower dynamics than the repressor complexes, containing CSL and Hairless.

(2) Contribution of CSL, NICD, and Mam IDRs to recruitment.

(3) CSL-Mam slow-diffusing complexes are recruited and form a hub of high protein concentrations around the target locus in Notch-ON conditions.

(4) Mam recruitment is not dependent on transcription initiation or RNA production.

(5) CBP/P300 or its associated HAT activity is not required for Mam recruitment.

(6) Mediator CDK module and CDK8 activity are required for Mam recruitment, and vice-versa, but not CSL recruitment.

(7) Mam is not required for chromatin accessibility but is dependent on CSL and NICD.

(8) CSL recruitment and increased chromatin accessibility persist after NICD removal and loss of Mam, which confers a memory state that enables rapid re-activation in response to subsequent Notch activation.

(9) Differences in the proportions of nuclei with both Pol II and with Mam enrichment, which results in transcription being probabilistic/stochastic. These data demonstrate that the presence of Mamcomplexes is not sufficient to drive all the steps required for transcription in every Notch-ON nucleus.

(10) The switch from more stochastic to robust transcription initiation was elicited when ecdysone was added.

Overall, the manuscript is well written, concise, and clear, and makes significant contributions to the Notch field, which are also important for a general understanding of transcription factor regulation and behavior in the nucleus. I recommend that the authors address my relatively minor criticisms detailed below.

We thank the reviewer for their thorough and constructive summary of our work. We are glad that they overall found it insightful and interesting. Below we have addressed the points they have raised.

Page 7, bottom. The authors speculate, "It is possible therefore that, once recruited, Mam can be retained at target loci independently of CSL by interactions with other factors so that it resides for longer." Is it possible that another interpretation of that data is that Mam is a limiting factor?

As indicated our comment is a speculation and is based on the observations summarized in the paragraph. We are not entirely sure what the reviewer is proposing as an alternate model. However, if it relates to the relative concentrations of the different factors, this would not account for the differences in trajectory durations. And for most aspects of our analysis, K[off] has the most profound influence on the results. Furthermore, differences persist even when CSL levels are considerably reduced (as in conditions with Hairless RNAi).

Page 9. The authors write, "A very low level of enrichment was evident for... for the CSL Cterminus..". The recruitment of CSL ct IDR does not appear to be statistically significant or there is no apparent difference (Figure S2C), suggesting the CSL ct IDR does not play a role in enrichment.

We agree with the comments of the reviewer and have adjusted the text on page 9 accordingly.

Page 9. The authors write, "Notably, MamnIDR::GFP fusion was present in droplets, suggesting it can self-associate when present in a high local concentration (Figure S2B)." Is this result only valid for Mam nIDR or does full-length Mam also localize into droplets, as has been previously observed for full-length mammalian Maml1 in transfected cells?

We agree that the observed foci of MamL1 that have been detected in mammalian cells are interesting. We have not tried to replicate those data because the large size of Mam has made it challenging to produce a full-length form in over-expression. We note however that another portion of Mam, MamIDR, does not make droplets when over-expressed despite it containing a large section of the disordered region of the Drosophila Mam. We have now included a comment about the mammalian data in the text (page 9) to put our findings in context.

Previous studies in mammalian cells suggest that Maml1 is a high-confidence target for phosphorylation by CDK8, see Poss et al 2016 Cell Reports https://doi.org/10.1016/j.celrep.2016.03.030. By sequence comparison, does fly Mam have similar potential phosphorylation sites, and might these be critical for Mam/CDK module recruitment?

We thank the reviewer for highlighting this point. Indeed, we were very excited when we learnt that MamL1 was found to be a high confidence CDK8 target and we looked hard in the Mam sequence for potential phosphorylation sites. Sadly, there is very little conservation between the fly and the mammalian proteins beyond the helical region that contacts CSL and NICD. Furthermore, there are no identifiable putative CDK8 phosphorylation sites based on conventional motifs. It therefore remains to be established whether or not Mam is a direct target of the CDK8 kinase activity. We have added an explanatory comment in the text (page 11).

Page 11: The authors write, "The differences in the effects on Mam and CSL imply that the CDK module is specifically involved in retaining Mam in the hub, and that in its absence other CSL complexes "win-out", either because the altered conditions favour them and/or because they are the more abundant." Are the "other" complexes the authors are referring to Hairless-containing complexes? With the reagents the authors have in hand couldn't this be explicitly shown for CSLcomplexes rather than speculated upon?

The reviewer is correct that CSL complexes containing Hairless are good candidates to be recruited in these conditions. We have compared the levels of Hairless at E(spl)-C following treatments with Senexin and have not detected a difference. However, it appears that the high proportion of unbound Hairless makes it difficult to detect/quantify the enrichment at E(spl)-C. We have therefore taken a different strategy, which is to measure the recruitment of a mutant form of CSL that is compromised for Hairless binding. Recruitment of the mutant CSL is detected in Notch-ON conditions, but is significantly reduced/absent following Senexin treatment. These data favour the model proposed by the reviewer that in the absence of CDK8 activity, the CSL-Hairless complexes win out. These new data have been added in new Supplementary Figure S3F and S3G (and see text page 11)

Page 12/13: The authors write, "Based on these results we propose that, after Notch activity decays, the locus remains accessible because when Mam-containing complexes are lost they are replaced by other CSL complexes (e.g. co-repressor complexes)." Again, why not actually test this hypothesis rather than speculate? The dynamics of Hairless complexes following the removal of Notch would be very interesting and build upon previously published results from the Bray lab.

We thank the reviewer for this comment and we agree it’s possible that the proportion of Hairless complexes increases after Notch withdrawal. However, for the reasons outlined above, it is difficult to quantify changes in Hairless, (and our preliminary experiment did not reveal any large-scale effect) and because of the complexity of the genetics we cannot straightforwardly extend the experiment to analyze the behaviour of the mutant CSL as above. Therefore, at present, we cannot say whether the loss of Mam is compensated by an increase in Hairless. We hope in future to investigate the characteristics of the memory in more depth.

Page 13: The authors write, "As Notch removal leads to a loss of Mam, but not CSL, from the hub, it should recapitulate the effects of MamDN." While the data in Figure 5B seem to support this hypothesis, it's not clear to me that the loss of Mam and MamDN should phenocopy each other, bc in the case of MamDN, NICD would still be present.

We apologise that this sentence was a bit misleading. We have now rewritten it to improve accuracy (page 13) “As Notch removal leads to a loss of Mam, but not CSL, from the hub, we hypothesised it would recapitulate the effects of MamDN on chromatin accessibility and transcription of targets.”

The temporal dynamics for Mam recruitment using the temperature- and optogenetic-paradigms are quite different. For example, in the optogenetic time course experiments, the preactivated cells are in the dark for 4 hours, while in the temperature-controlled experiments, there is still considerable enrichment of Mam at 4 hours. For the preactivated optogenetic experiments, how sure are the authors that Mam is completely gone from the locus, and alternatively, can the optogenetic experimental results be replicated in the temperature-controlled assays? My concern is whether the putative "memory" observation is just due to incomplete Mam removal from the previous activation event.

We appreciate the concerns of the reviewer. However, we are confident that the 4-hour optogenetic inactivation is much more effective than the equivalent time for temperature shifts. The temperature sensitive experiment involves a longer decay, because not only the protein but also the mRNA has to decay to fully remove NICD activity. The optogenetic experiments, involve only protein decay and so are more acute. Furthermore, we have tested (and we show in Figure 5H) that Mam is fully depleted after 4 hours “Off” in the optogenetic experiments.

In order to further strengthen the evidence in favour of the memory hub, we have extended the time-frame further to show that CSL is retained at the locus even after 24 hours “Notch OFF” in both the temperature and the optogenetic paradigm. We have also measured the effects on transcription after a 24hr OFF period using the optogenetic paradigm and seen that robust transcription is initiated in cells that have experienced a previous activation (preactivated) compared to those that have not (naïve). These new data have been added to new Figure 5 C-F and strongly support the memory model.

Reviewer #3 (Public Review):

Summary:

DeHaro-Arbona and colleagues investigate the in vivo dynamics of Notch-dependent transcriptional activation with a focus on the role of the Mastermind (MAM) transcriptional co-activator. They use GFP and HALO-tagged versions of the CSL DNA-binding protein and MAM to visualize the complex, and Int/ParB to visualize the site of Notch-dependent E(Spl)-C transcription. They make several conclusions. First, MAM accumulates at E(Spl)-C when Notch signaling is active, just like CSL. Second, MAM recruits the CDK module of Mediator but does not initiate chromatin accessibility. Third, after signaling is turned off, MAM leaves the site quickly but CSL and chromatin accessibility are retained. Fourth, RNA pol II recruitment, Mediator recruitment, and active transcription were similar and stochastic. Fifth, ecdysone enhances the probability of transcriptional initiation.

Strengths:

The conclusions are well supported by multiple lines of extensive data that are carefully executed and controlled. A major strength is the strategic combination of Drosophila genetics, imaging, and quantitative analyses to conduct compelling and easily interpretable experiments. A second major strength is the focus on MAM to gain insights into the dynamics of transcriptional activation specifically.

We thank the reviewer for their positive comments about the strengths of our work.

Weaknesses:

Weaknesses are minor. There were no p-values reported for data presented in Figure S1D and no indication of how variable measurements were. In addition, the discussion of stochasticity was not integrated optimally with relevant literature.

We thank the reviewer for noting these points. The statistical tests have now been included for Figure S1D (now Figure S1F). We have amplified the discussion about stochasticity, to include more reference to the literature and to make clear also the distinction with transcription bursting (page 19, 20).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

The authors have an elegant series of manipulations that provide strong evidence for their hypotheses and conclusions. Their exploitation of a unique biological system amenable to imaging in the larval salivary gland is well-considered and well-performed. Most of the conclusions are supported by the data. I only have the concerns below.

(1) One of the main findings is the composition of Notch nuclear complexes and their interactions within a 'hub'. Yet most of the data showing hubs focus on labeling one protein component (+the locus or transcription), but multi-color imaging is rarely used to show how CSL-Mam, Mam-Med... protein signals coalescence to form a hub. Given the powerful tool developed, it would be important to show these multi-state hubs. Related to this, if the authors expect that hubs are formed independently of transcription or Notch pathway activation, do the authors see clustering at other non-specific loci in the nucleus? If not, can the authors comment on why they think that is the case? If so, do they demonstrate consistent residence time profiles with the tracked E(spl) locus?

We apologise that it was not evident from the data shown that the proteins co-localize. First we stress that all the experiments are multicolor and most rely on very powerful methods to measure co-recruitment at a chromosomal locus- something that is very rarely achieved by others studying hubs. Second, we have in all cases confirmed that the proteins do colocalize. We have modified the diagram of our analysis pipeline to make more clear that this relies on multi-colour imaging, and adjusted all the figure labels to indicate the position of E(spl)-C. We have also added panels to new supplementary Figure S1C with examples of the co-localization between CSL and Mam and a plot confirming their levels of recruitment are correlated across multiple nuclei.

We would like to clarify that our data show that the hubs do require Notch activation for their establishment. Other regions of enrichment are detected in Notch-ON conditions, but these are less prominent and, with no independent method for identifying them, can’t be compared between nuclei. In SPT experiments, other clusters with consistent residence are detected as reported in our recent paper which expanded on the SPT data (Baloul et al, 2023). We also detect co-localizations and “hubs” in other tissues, but those analyses are ongoing and beyond the scope of this paper.

(2) The authors convincingly show that Notch hub complexes exhibit a memory. While the data showing rapid hub reformation upon Notch withdrawal are solid and convincing (Figure 5, in particular, F), the claim that this memory fosters rapid transcriptional reactivation is less clear. Yet in order to invoke transcriptional memory, it's necessary to solidify this transcriptional response angle. The authors should consider quantifying the changes in transcription activity (at the TS and not in the cytoplasm as currently shown), as well as the timing of transcriptional reactivation (with the MS2 system or smFISH). Manipulating the duration of the activation and dark recovery periods could help to draw a better correlation between the timing of hub reformation and that of transcriptional response and would also help determine how persistent this phenomenon is.

We thank the reviewer for these suggestions. We have carried out several new experiments to probe further the persistence of memory and to show the effects on transcription when Notch is inactivated/reactivated. First, we have extended the time period for Notch inactivation by temperature control and show that the CSL hub persists even at 24 hours and that no transcription from the target E(spl)m3 is detected –neither at the transcription start-site nor in the cytoplasm. Second, we have extended the Notch OFF time period to 24 hours using the optogenetic approach and show that transcription is robustly reinitiated in preactivated nuclei when Notch is re-activated with 30 mins light treatment while little if any E(spl)m3 transcription is detected in naïve nuclei with the same treatment. These new data are included in new Figure 5 C-F and see page 13-14. Both these new experiments substantiate the model that the nuclei retain transcriptional memory.

(3) The manuscript ends with the finding that the presence of a Mam hub does not always correlate with transcription. They conclude that transcription is initially stochastic. The authors find this surprising and even state that this could not be observed without their in vivo live imaging approaches. I don't understand why this result is surprising or unexpected, as we now know that transcription is generally a stochastic process and that most (if not all) loci are transcribed in a bursting manner. The fact that E(spl)-C locus is bursty is already obvious from the smFISH data. The fact that active nascent transcription does not correlate with local TF hubs was already observed in early Drosophila embryos (with Zelda hubs and two MS2 reporters, hb-MS2, sna-MS2). If, in spite of the inherent stochasticity of transcription (bursting), the data are surprising for other reasons, the authors should explain it better.

We apologise that we had not made clear the reasons why the results were unexpected. We have substantially rewritten this section, and the discussion section, to clarify. We have also moderated the language used to better reflect the overall context of our results. We briefly summarise here. As the reviewer correctly states, it is well known that transcription is inherently bursty. Indeed the MS2 transcription profiles in “ON” nuclei are bursty, which likely reflects the switching of the promoter. However, in other contexts where we have monitored transcription although it is bursty it has nevertheless been initiated synchronously in response to Notch in all nuclei in a manner that was fully penetrant. What we observe in our current conditions, is that some nuclei never initiate transcription over the time-course of our experiments (2-3 hours), and those that are ON rarely switch off. This implies that there is another rate-limiting step. Supplying a second signal can modulate this so that it occurs with much higher frequency/penetrance. We consider this to be a second tier of regulation above the fundamental transcriptional bursting.

The fact that Mam is recruited in all nuclei, whether or not they are actively transcribing was surprising because recruitment of the activation complex has been considered as the limiting step. This is somewhat different from Zelda, which is thought to be permissive and needed at an early step to prime genes for later activation rather than to be the last step needed to fire transcription. We note also that we are not monitoring the position of the hub with respect to the promoter, as in the Zelda experiments (Zelda hubs may still persist, but they are not overlapping with the nascent RNA), we are monitoring the presence or absence of Mam hub in proximity to a genomic region.

Minor suggestions:

(1) The genotypes of the samples should be indicated in the figure legends.

We thank the reviewer for this suggestion. We have provided a table (new Table S3) where all of the genetic combinations are provided in detail for each figure. We considered that this approach would be preferable because it would be quite cumbersome to have the genotypes in each legend as they would become very long and repetitive.

(2) While the schematic Fig1A explains how the locus is detected, the presence of ParS/ParB is never indicated in subsequent panels and Figure. I assume that all panels depicting enrichment profiles, use a given radius from the ParS/ParB dot to determine the zero of the x-axis (grey zone). This should be clearly stated in all panels/figure legends concerned.

We apologies if this was not made explicit. Yes, all panels depicting enrichment profiles, use immunofluorescence signal from ParA/ParB recruitment to determine the zero of the x-axis. We have now marked this more clearly In all figures (grey bar, grey shading or labelled 0). All images where the locus is indicated by an arrowhead, by a coloured bar above the intensity plots or by grey shading in the graphs have been captured with dual colour and the signal from ParA/B recruitment used to define its location. This is now clearly stated in the analysis methods and in the legend. We have also modified the diagram in new supplementary Figure S1B, showing our analysis pipeline, to make that more explicit.

(3) FRAP/SPT experiments: the author should provide more details. How many traces? Are traces showing bleaching removed?

P7: does the statement ' The residences are likely an underestimation because bleaching and other technical limitations also affect track durations' imply that traces showing bleaching have not been removed from the analysis?

The authors could justify the choice of the model for fitting FRAP/Spt experiments and be cautious about their interpretation. For example, interpreting a kinetic behavior as a DNA-specific binding event can be accurate, only if backed up with measurements with a mutant version of the DNA binding domain.

We apologise if some of this information was not evident. The number of trajectories is provided in new Figure S1F, which indicates the number of trajectories analyzed for each condition in Figure 1.

We have now added also the numbers of trajectories analyzed for the ring experiments.

The comments on page 7 about bleaching refer to the technical limitations of the SPT approach. However, as bleached particles cannot be distinguished from those that leave the plane of imaging, they have not been filtered or removed. We have not sought to make claims about absolute residence times for that reason. Rather the point is to make a comparison between the different molecules. As the same fluorescent ligand and imaging conditions are used in all the experiments, all the samples are equivalently affected by bleaching. We subdivide trajectories according to their properties and infer that those which are essentially stationary are bound to chromatin, as is common practice in the field. We note that we have previously shown that a DNA binding mutant of CSL does not produce a hub at E(spl)-C in Notch-ON conditions and has a markedly more rapid recovery in FRAP experiments (Gomez-Lamarca et al, 2018) consistent with the slow recovery being related to DNA binding. This point has been added to the text (page 8).

(4) The authors should quantify their RNAi efficiency for Hairless-RNAi, Med13-RNAi, white-RNAi, yellow-RNAi, CBP-RNAi, and CDK8-RNAi.

We thank the reviewer for this comment. We have made sure that we are using well validated RNAis in all our experiments and have included the references in Table S2 where they have been used. We have now evaluated the knock-down in the precise conditions used in our experiments by quantitative RT-PCR and added those data, which show efficient knock-down is occurring, to new Supplementary Figure S1D and Figure S3J. We note also that the RNAi experiments are complemented by experiments inhibiting the complexes with specific drugs and that these yield similar results.

(5) Figure 3 A: could the author show that transcription is indeed inhibited upon triptolide treatment with smFISH (with for example m3 probes)? Why not use alpha-amanitin?

We thank the reviewer for this suggestion. We had omitted the smFISH data from this experiment in error. These data have now been added to new Supplementary Figure S3A and clearly show that transcription is inhibited following 1 hour exposure to triptolide. Triptolide is a very fast acting and very efficient inhibitor of transcription that acts at a very early step in transcription initiation. In our experience it is much more efficient than alpha-amanitin and is now the inhibitor of choice in many transcription studies.

(6) Figure 4 typo: panel B should be D and vice versa. Accessibility panels are referred to as Figure 4D, D' in the text but presented as panel B in the Figure.

We thank the reviewer for noting this mistake, it is now changed in the main text.

(7) The authors must add their optogenetic manipulation protocol to their methods section.

The method is described in detail in a recently published paper that reports its design and use. We have now also added a section explaining the paradigm in the methods (Page 31) as requested.

(8) Figure 3G needs a Y-axis label.

Our apologies, this has now been added.

(9) The authors should note why there was a change of control in Figure 3D compared to 3E and G (yellow RNAi vs white RNAi).

This is a pragmatic choice that relates to the chromosomal site of the RNAis being tested. Controls were chosen according to the chromosome that carries the UAS-RNAi: for the second chromosome this was yellow RNAi and for the third white RNAi. This is explained in the methods.

(10) Figure 1 would benefit from a diagram describing the genomic structure of the E(spl) locus and the relative position of the labelled locus within it.

We thank the reviewer for this suggestion and have added a diagram to Supplementary Figure S1A .

Reviewer #2 (Recommendations For The Authors):

Minor criticisms and typos:

Pet peeve: in some of the figure panels they are labeled Notch ON or OFF, but in others they are not, albeit that info is included in the figure legend. For the ease of the reader/reviewer, would it be possible to label all relevant figure panels either Notch ON or OFF for clarity?

We thank the reviewer for this suggestion and have modified the figures accordingly.

Page 7, top. "In comparison to their average distribution across the nucleus, both CSL and Mam trajectories were significantly enriched in a region of approximately 0.5 μm around the target locus in Notch-ON conditions, reflecting robust Notch dependant recruitment to this gene complex." Are the authors referring to Figure 1D here?

Thank you, this figure call-out has been added in the text.

Page 9. "...reported to interact with p300 and other factors (Figure S2B)." I believe the authors mean Figure S2C and not S2B.

Thank you, this has been corrected in the text.

Page 9. There is no Figure S2D.

Apologies, this was referring to Figure S1D, and is now corrected in the text.

Page 11: "...were at very reduced levels in nuclei co-expressing MamDN (Figure 4B).." Should be Figure 4CD.

Thank you, this has been corrected in the text.

Page 12: "...which was maintained in the presence of MamDN (Figure 4D, D')." Should be Figure 4B.

Thank you, this has been corrected in the text.

Reviewer #3 (Recommendations For The Authors):

In the Results section on Hub, the paragraph starting with "Third, we reasoned . ." the callout to Figure S2D should be Fig S1D.

Thank you, this has been corrected in the text

Figures: The font size in the Figures is so small that most words and numbers cannot be read on a printout. One has to go to the electronic version and increase the size to read it. This reviewer found that inconvenient and often annoying.

We apologise for this oversight, the font size has now been adjusted on all the graphs etc.

Figure legends: the legends are terse and in some cases leave explanations to the imagination (e.g. "px" in Figure 2E). It would be useful to go through them and make sure those who are not a Drosophila Notch person and not a transcription biochemist can make sense of them.

Our apologies for the lack of clarity in the legends. We have gone over them to make them more accessible and less succinct.

Author Response

We are very pleased to hear the overall positive views and constructive criticisms of eLife Editors and Reviewers on our work. In particular, we appreciate their comments highlighting the value of our new pipeline for high-throughput quantification of fly embryonic movement and the positive views of reviewers and editors that our data on the roles of miR-2b-1 in embryonic movement are well supported.

Regarding Reviewer 1, we thank them for their positive comments that our work is experimentally sound and well-written, their kind words on the value of our new embryonic movement pipeline, and their overall appreciation of the quality, scope, and significance of our work. In a revised version of the manuscript we will consider discussing and addressing some of the interesting points raised by Rev1.

Turning to the comments by Rev2, we are grateful to them for their recognition of the novelty of our miRNA findings and appreciation of the utility of our novel quantitative pipeline for assessing embryonic movement. Nonetheless, we politely – but strongly – disagree with their suggestion that the findings are inflated by our language. For example, they criticise our use of the verb ‘control’, yet this is a standard textbook term in molecular biology to describe biological processes regulated by genetic factors: given that miR-2b-1 regulates movement patterns during embryogenesis, to say that miR-2b-1 ‘controls’ embryonic movement in the Drosophila embryo is reasonable and in line with the language used in the field. It is not inflation. In connection to other comments, in a revised manuscript we will propose a different name for the gene here described as Janus to avoid annotation issues at FlyBase due to other, unrelated genes that include this word as part of their names.

Author Response:

Reviewer #1 (Public Review):

[...] Weaknesses are the absence of correlation between the results from the animal studies and human pancreatic cancers.

Author response: We appreciate the reviewer’s attention to the importance of human pancreatic cancer studies. In a previous study (D’Amico et al. Genes & Development 2018 doi: 10.1101/gad.311852.118), we evaluated the expression of STAT3 in human pancreatic tissue microarrays and data from the Human Protein Atlas. Mutations in Stat3 are infrequent in human pancreatic cancers, however there is a trend of decreased STAT3 activity in poorly differentiated carcinomas.

In the current study, STAT3 and SMAD4 gene signature scores (computed from KO KPC cells) were aligned with human pancreatic ductal adenocarcinoma samples from the TCGA cohort, and statistical analyses supported the selective antagonism of STAT3 and SMAD4 (Fig 4D, Fig 4E).

The complex process of EMT is difficult to characterize rigorously in human cancers. Mouse models offer an opportunity to study the relationships between cancer phenotypes and genetic alterations.

Reviewer #2 (Public Review):

[...] While correlations are strong, the study would benefit from additional cause-and-effect type experiments. It would also be beneficial to better tie together the first and second parts of the paper.

Author response: We understand the Reviewer’s interest in additional experiments that could further elucidate mechanisms that drive EMT and/or KRAS dependency in relation to STAT3 and TGF-beta antagonism. We previously investigated the development of mutant KRAS knockout tumors (Ischenko et al. Nature Communications 2021 doi:10.1038/s41467-021-21736) to find loss of KRAS promotes EMT, similar to loss of STAT3. Additional experiments are underway but are outside the scope of the current study.

The first part of the paper is mechanistic and used KRAS-transformed mouse embryo fibroblasts to perform in vitro studies with foci formation. The cell-based foci formation assay has been shown to best evaluate malignant transformation and oncogenic potential. In the second part we transitioned to epithelial cells and pancreatic ductal adenocarcinomas to combine mechanistic relationships with genetic models.

Author Response

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

eLife assessment

This manuscript represents a cleanly designed experiment for assessing biological motion processing in children (mean age = 9) with and without ADHD. The group differences concerning accuracy in global and local motion processing abilities are solid, but the analyses suggesting dissociable relationships between global and local processing and social skills, age, and IQ need further interrogation. The results are useful in terms of understanding ADHD and the ontogenesis of different components of the processing of biological motion.

We thank the editors for the positive assessment of our manuscript. We have carefully considered the reviewers’ constructive and helpful comments and revised our manuscript accordingly. To address the question about the dissociable relationships between global and local BM processing, we have provided more evidence and additional analyses in this revised version.

Reviewer #1 (Public Review):

Summary:

The paper presents a nice study investigating differences in biological motion perception in participants with ADHD in comparison with controls. Motivated by the idea that there is a relationship between biological motion perception and social capabilities, the authors investigated local and global (holistic) biological motion perception, the group, and several additional behavioral variables that are affected in ADHS (IQ, social responsiveness, and attention/impulsivity). As well as local global biological motion perception is reduced in ADHD participants. In addition, the study demonstrates a significant correlation between local biological motion perception skills and the social responsiveness score in the ADHD group, but not the controls. A path analysis in the ADHD data suggests that general performance in biological motion perception is influenced mainly by global biological motion perception performance and attentional and perceptual reasoning skills.

Strengths:

It is true that there exists not much work on biological motion perception and ADHD. Therefore, the presented study contributes an interesting new result to the biological motion literature and adds potentially also new behavioral markers for this clinical condition. The design of the study is straightforward and technically sound, and the drawn conclusions are supported by the presented results.

Thank you for your positive assessment of our work.

Weaknesses:

Some of the claims about the relationship between genetic factors and ADHD and the components of biological motion processing have to remain speculative at this point because genetic influences were not explicitly tested in this paper.

We agree that the relationship between genetic factors and BM processing in ADHD needs more investigation, We have modified our statement in Discussion section as following:

“Using the classical twin method, Wang et al. found that the distinction between local and global BM processing may stem from the dissociated genetic bases. The former, to a great degree, seems to be acquired phylogenetically20,21,59,60, while the latter is primarily obtained through individual development19.” (lines 421 - 425),

Reviewer #2 (Public Review):

Summary:

Tian et al. aimed to assess differences in biological motion (BM) perception between children with and without ADHD, as well as relationships to indices of social functioning and possible predictors of BM perception (including demographics, reasoning ability and inattention). In their study, children with ADHD showed poorer performance relative to typically developing children in three tasks measuring local, global, and general BM perception. The authors further observed that across the whole sample, performance in all three BM tasks was negatively correlated with scores on the social responsiveness scale (SRS), whereas within groups a significant relationship to SRS scores was only observed in the ADHD group and for the local BM task. Local and global BM perception showed a dissociation in that global BM processing was predicted by age, while local BM perception was not. Finally, general (local & global combined) BM processing was predicted by age and global BM processing, while reasoning ability mediated the effect of inattention on BM processing.

Strengths:

Overall, the manuscript is presented in a relatively clear fashion and methods and materials are presented with sufficient detail so the study could be reproduced by independent researchers. The study uses an innovative, albeit not novel, paradigm to investigate two independent processes underlying BM perception. The results are novel and have the potential to have wide-reaching impact on multiple fields.

We appreciate your positive assessment of our work.

Weaknesses:

Except for the main analysis, it is unclear what the authors' specific predictions are regarding the three different tasks they employ. The three BM tasks are used to probe different processes underlying BM perception, but it is difficult to gather from the introduction why these three specific tasks were chosen and what predictions the authors have about the performance of the ADHD group in these tasks. Relatedly, the authors do not report whether (and if so, how) they corrected for multiple comparisons in their analyses. As the number of tests one should control for depends on the theoretical predictions (http://daniellakens.blogspot.com/2016/02/why-you-dont-need-to-adjust-you-alpha.html), both are necessary for the reader to assess the statistical validity of the results and any inferences drawn from them. The same is the case for the secondary analyses exploring relationships between the 3 individual BM tasks and social function measured by the social responsivity scale (SRS).

We appreciate these constructive suggestions. In response, we have included a detailed description in the Introduction section explaining why we employed three different tasks and our predictions about the performance in ADHD:

“Despite initial indications, a comprehensive investigation into BM perception in ADHD is warranted. We proposed that it is essential to deconstruct BM processing into its multiple components and motion features, since treating them as a single entity may lead to misleading or inconsistent findings31. To address this issue, we employed a carefully designed behavioral paradigm used in our previous study19, making slight adjustments to adapt for children. This paradigm comprises three tasks. Task 1 (BM-local) aimed to assess the ability to process local BM cues. Scrambled BM sequences were displayed and participants could use local BM cues to judge the facing direction of the scrambled walker. Task 2 (BM-global) tested the ability to process the global configuration cues of the BM walker. Local cues were uninformative, and participants used global BM cues to determine the presence of an intact walker. Task 3 (BM-general) tested the ability to process general BM cues (local + global cues). The stimulus sequences consisted of an intact walker and a mask containing similar target local cues, so participants could use general BM cues (local + global cues) to judge the facing direction of the walker.” (lines 116 - 130)

“In Experiment 1, we examined three specific BM perception abilities in children with ADHD. As mentioned earlier, children with ADHD also show impaired social interaction, which implies atypical social cognition. Therefore, we speculated that children with ADHD performed worse in the three tasks compared to TD children.” (lines 131 - 134)

Additionally, we have reported the p values corrected for multiple comparisons (false discovery rate, FDR) in the revised manuscript wherever it was necessary to adjust the alpha (lines 310 - 316; Table 2). The pattern of the results remained unchanged.

In relation to my prior point, the authors could provide more clarity on how the conclusions drawn from the results relate to their predictions. For example, it is unclear what specific conclusions the authors draw based on their findings that ADHD show performance differences in all three BM perception tasks, but only local BM is related to social function within this group. Here, the claim is made that their results support a specific hypothesis, but it is unclear to me what hypothesis they are actually referring to (see line 343 & following). This lack of clarity is aggravated by the fact that throughout the rest of the discussion, in particular when discussing other findings to support their own conclusions, the authors often make no distinction between the two processes of interest. Lastly, some of the authors' conclusions related to their findings on local vs global BM processing are not logically following from the evidence: For instance, the authors conclude that their data supports the idea that social atypicalities are likely to reduce with age in ADHD individuals. However, according to their own account, local BM perception - the only measure that was related to social function in their study - is understood to be age invariant (and was indeed not predicted by age in the present study).

Thank you for pointing out this issue. We have carefully revised the Discussion section about our findings to clarify these points:

“Our study contributes several promising findings concerning atypical biological motion perception in ADHD. Specifically, we observe the atypical local and global BM perception in children with ADHD. Notably, a potential dissociation between the processing of local and global BM information is identified. The ability to process local BM cues appears to be linked to the traits of social interaction among children with ADHD. In contrast, global BM processing exhibits an age-related development. Additionally, general BM perception may be affected by factors including attention.” (lines 387 - 393)

We have provided a detailed discussion on the two processes of interest to clarify their potential differences and the possible reasons behind the difference of the divergent developmental trajectories between local and global BM processing:

“BM perception is considered a multi-level phenomenon56-58. At least in part, processing information of local BM and global BM appears to involve different genetic and neural mechanisms16,19. Using the classical twin method, Wang et al. found that the distinction between local and global BM processing may stem from the dissociated genetic bases. The former, to a great degree, seems to be acquired phylogenetically20,21,59,60, while the latter is primarily obtained through individual development19. The sensitivity to local rather than global BM cues seems to emerge early in life. Visually inexperienced chicks exhibit a spontaneous preference for the BM stimuli of hen, even when the configuration was scrambled20. The same finding was reported in newborns. On the contrary, the ability to process global BM cues rather than local BM cues may be influenced by attention28,29 and shaped by experience24,56.” (lines 419 - 430)

“We found that the ability to process global and general BM cues improved significantly with age in both TD and ADHD groups, which imply the processing module for global BM cues tends to be mature with development. In the ADHD group, the improvement in processing general and global BM cues is greater than that in processing local BM cues, while no difference was found in TD group. This may be due to the relatively higher baseline abilities of BM perception in TD children, resulting in a relatively milder improvement. These findings also suggest a dissociation between the development of local and global BM processing. There seems to be an acquisition of ability to process global BM cues, akin to the potential age-related improvements observed in certain aspects of social cognition deficits among individuals with ADHD5, whereas local BM may be considered an intrinsic trait19.” (lines 438 -449)

In addition, we have rephased some inaccurate statements in revised manuscript. Another part of social dysfunction might be stable and due to the atypical local BM perception in ADHD individuals, although some studies found a part of social dysfunction would reduce with age in ADHD individuals. One reason is that some factors related to social dysfunction would improve with age, like the symptom of hyperactivity.

Results reported are incomplete, making it hard for the reader to comprehensively interpret the findings and assess whether the conclusions drawn are valid. Whenever the authors report negative results (p-values > 0.05), the relevant statistics are not reported, and the data not plotted. In addition, summary statistics (group means) are missing for the main analysis.

Thanks for your comments. We have provided the complete statistical results in the revised manuscript (lines 309 - 316) and supplementary material, which encompass relevant statistics and plots of negative results (Figure 4, Figure S2 and S3), in accordance with our research questions. And we have also included summary statistics in the Results section (lines 287 - 293).

Some of the conclusions/statements in the article are too strong and should be rephrased to indicate hypotheses and speculations rather than facts. For example, in lines 97-99 the authors state that the finding of poor BM performance in TD children in a prior study 'indicated inferior applicability' or 'inapplicable experimental design'. While this is one possibility, a perhaps more plausible interpretation could be that TD children show 'poor' performance due to outstanding maturation of the underlying (global) BM processes (as the authors suggest themselves that BM perception can improve with age). There are several other examples where statements are too strong or misleading, which need attention.

We thank you for pointing out the issue. We have toned down and rephrased the strong statements and made the necessary revisions.

“Another study found that children with ADHD performed worse in BM detection with moderate ratios of noise34. This may be due to the fact that BM stimuli with noise dots will increase the difficulty of identification, which highlights the difference in processing BM between the two groups33,35.” (lines 111 - 115)

Reviewer #3 (Public Review):

Summary:

The authors presented point light displays of human walkers to children (mean = 9 years) with and without ADHD to compare their biological motion perception abilities and relate them to IQ, social responsiveness scale (SRS) scores and age. They report that children with ADHD were worse at all three biological motion tasks, but that those loading more heavily on local processing related to social interaction skills and global processing to age. The important and solid findings are informative for understanding this complex condition, as well as biological motion processing mechanisms in general. However, I am unsure that these differences between local and global skills are truly supported by the data and suggest some further analyses.

Strengths:

The authors present clear differences between the ADHD and TD children in biological motion processing, and this question has not received as much attention as equivalent processing capabilities in autism. They use a task that appears well controlled. They raise some interesting mechanistic possibilities for differences in local and global motion processing, which are distinctions worth exploring. The group differences will therefore be of interest to those studying ADHD, as well as other developmental conditions, and those examining biological motion processing mechanisms in general.

We appreciate your positive feedback. In revised manuscript, we have added more analyses to support the differences between local and global motion processing. Please refer to our response to the point #3 you mentioned below.

Weaknesses:

I am unsure that the data are strong enough to support claims about differences between global and local processing wrt social communication skills and age. The mechanistic possibilities for why these abilities may dissociate in such a way are interesting, but do not seem so plausible to me. I am also concerned about gender, and possible autism, confounds when examining the effect of ADHD. Specifics:

Gender confound. There are proportionally more boys in the ADHD than TD group. The authors appear to attempt to overcome this issue by including gender as a covariate. I am unsure if this addresses the problem. The vast majority of participants in the ADHD group are male, and gender is categorically, not continuously, defined. I'm pretty sure this violates the assumptions of ANCOVA.

We appreciate your comments. We concur with you that although we observed a clear difference between local and global BM processing in ADHD, the evidence is to some extent preliminary. The mechanistic possibilities for why these abilities may dissociate have been discussed in revised manuscript. Please refer to the response to reviewer 2’s point #2. To further examine if gender played a role in the observed results, we used a statistical matching technique to obtain a sub-dataset. The pattern of results remained with the more balanced dataset (see Supplementary Information part 1). According to your suggestion, we have also presented the results without using gender as a covariate in main text and also separated the data of boys and girls on the plots (see Figure 1 and Figure S1). There were indeed no signs of a gender effect.

Autism. Autism and ADHD are highly comorbid. The authors state that the TD children did not have an autism or ADHD diagnosis, but they do not state that the ADHD children did not have an autism diagnosis. Given the nature of the claims, this seems crucial information for the reader.

Thanks for your suggestion. We have confirmed that all children with ADHD in our study were not diagnosed with autism. We used a semi-structured interview instrument (K-SADSPL-C) to confirm every recruited child with ADHD but not with ASD. The exclusion criteria for both groups were mentioned in the Materials and methods section:

“Exclusion criteria for both groups were: (a) neurological diseases; (b) other neurodevelopmental disorders (e.g., ASD, Mental retardation, and tic disorders), affective disorders and schizophrenia…” (lines 158 - 162)

Conclusions. The authors state frequently that it was the local BM task that related to social communication skills (SRS) and not the global tasks. However, the results section shows a correlation between SRS and all three tasks. The only difference is that when looking specifically within the ADHD group, the correlation is only significant for the local task. I think that if the authors wish to make strong claims here they must show inferential stats supporting (1) a difference between ADHD and TD SRS-Task 1 correlations, and (2) a difference in those differences for Task 2 and 3 relative to Task 1. I think they should also show a scatterplot of this correlation, with separate lines of best fit for the two groups, for Tasks 2 and 3 as well. I.e. Figure 4 should have 3 panels. I would recommend the same type of approach for age. Currently, they have small samples for correlations, and are reading much of theoretical significance between some correlations passing significance threshold and others not. It would be incredibly interesting if the social skills (as measured by SRS) only relate to local BM abilities, and age only to global, but I think the data are not so clear with the current information. I would be surprised if all BM abilities did not improve with age. Even if there is some genetic starter kit (and that this differs according to particular BM component), most abilities improve with learning/experience/age.

Thank you for this recommendation. We have added more statistics to test differences between the correlations (a difference between ADHD and TD in SRS-Task 1 correlations (see the first paragraph of Supplementary Information part 2), a difference in SRS-response accuracy correlations for Task 2 and 3 relative to Task 1(see the second paragraph of Supplementary Information part 2), and a difference in age-response accuracy correlations for Task 2 and 3 relative to Task 1 in ADHD group (see Supplementary Information part 3)). Additionally, we have included scatterplots for SRS-Task1, SRS-Task2, SRS-Task3 (with separate lines of best fit for the two groups in each, see Figure 4), SRS-ADHD, SRS-TD, age-ADHD and age-TD (with separate lines of best fit for the three tasks in each, see Figure S2 and S3) to make a clear demonstration. Detailed results have been presented in the revised manuscript and Supplementary Information. We expect these further analyses would strengthen our conclusions.

Theoretical assumptions. The authors make some sweeping statements about local vs global biological motion processing that need to be toned down. They assume that local processing is specifically genetically whereas global processing is a product of experience. The fact their global, but not local, task performance improves with age would tend to suggest there could be some difference here, but the existing literature does not allow for this certainty. The chick studies showing a neonatal preference are controversial and confounded - I cannot remember the specifics but I think there an upper vs lower visual field complexity difference here.

Thank you for pointing out this issue. We have toned down rephrased our claims that the difference between local and global BM processing according to your suggestion:

“These findings suggest that local and global mechanisms might play different roles in BM perception, though the exact mechanisms underlying the distinction remain unclear. Exploring the two components of BM perception will enhance our understanding of the difference between local and global BM processing, shedding light on the psychological processes involved in atypical BM perception.” (lines 87 - 92)

Reviewer #1 (Recommendations For The Authors):

I have only a number of minor points that should be addressed prior to publication:

L. 95ff: What is meant by 'inapplicability of experimental designs' ? This paragraph is somewhat unclear.

In revised manuscript, we have clarified this point (lines 111 - 115).

L. 146: The groups were not perfectly balanced for sex. Would results change fundamentally in a more balanced design, or can arguments be given that gender does not play a role, like it seems to be the case for some functions in biological motion perception (e.g. Pavlova et al. 2015; Tsang et al 2018). One could provide a justification that this disbalance does not matter or test for subsampled balanced data sets maybe.

This point is similar to the point #1 from reviewer 3, and we have addressed this issue in our response above.

L. 216 f.: In this paragraph it does not become very clear that the mask for the global task consisted of scrambles generated from walkers walking in the same direction. The mask for the local task then should consist of a balanced mask that contains the same amount of local motion cues indicating right and leftwards motion. Was this the case? (Not so clear from this paragraph.)

Regarding the local task, the introduction of mask would make the task too difficult for children. Therefore, in the local task, we only displayed a scrambled walker without a mask, which was more suitable for children to complete the task. We have made clear this point in the corresponding paragraph (lines 232 - 241).

L. 224 ff.: Here it would be helpful to see the 5 different 'facing' directions of the walkers. What does this exactly mean? Do they move on oblique paths that are not exactly orthogonal to the viewing directions, and how much did these facing directions differ?

Out of the five walkers we used, two faced straight left or right, orthogonal to the viewing directions. Two walked with their bodies oriented 45 degrees from the observer, to the left or right. The last one walked towards the observer. We have included a video (Video 4) to demonstrate the 5 facing directions.

L. 232: How was the number of 5 practicing trials determined/justified?

As mentioned in main text, global BM processing is susceptible to learning. Therefore, too many practicing trials would increase BM visual experience and influence the results. We determined the number of training trials to be 5 based on the results of the pilot experiment. During this phase, we observed that nearly all children were able to understand the task requirements well after completing 5 practicing trials.

L 239: Apparently no non-parametric statistics was applied. Maybe it would be good to mention in the Statistics section briefly why this was justified.

We appreciate your suggestion and have cited two references in the Statistics section (Fagerland et al. 2012, Rochon et al. 2012). Fagerland et al., mentioned that when the sample size increases, the t-test is more robust. According to the central limit theorem, when the sample size is greater than 30, the sampling distribution of the mean can be safely assumed to be normal.

(http://www2.psychology.uiowa.edu/faculty/mordkoff/GradStats/part%201/I.07%20normal.p df). In fact, we also ran non-parametric statistics for our data and found the results to be robust.

L 290: 'FIQ' this abbreviation should be defined.

Regarding the abbreviation ’FIQ’, it stands for the abbreviation of the full-scale intellectual quotient, which was mentioned in Materials and methods section:

“Scores of the four broad areas constitute the full-scale intellectual quotient (FIQ).”

L. 290 ff.: These model 'BM-local = age + gender etc ' is a pretty sloppy notation. I think what is meant that a GLM was used that uses the predictors gender etc. time appropriate beta_i values. This formula should be corrected or one just says that a GLM was run with the predictors gender ....

The same criticism applies to these other models that follow.

We thank you for pointing this out. We have modified all formulas accordingly in the revised manuscript (see part3 of the Results section).

All these models assume linearity of the combination of the predictors.was this assumption verified?

We referred to the previous study of BM perception in children. They found main predictor variables, including IQ (Rutherford et al., 2012; Jones et al., 2011) and age (Annaz et al., 2010; van et al., 2016), have a linear relation with the ability of BM processing.

L. 296ff.: For model (b) it looks like general BM performance is strongly driven by the predictor global BM performance in the group of patients. Does the same observation also apply to the normals?

The same phenomenon was not observed in TD children. We have briefly discussed this point in the Discussion section of the revised manuscript (lines 449 - 459).

Reviewer #2 (Recommendations For The Authors):

(1) Please add public access to the data repository so data availability can be assessed.

The data of the study will be available at https://osf.io/37p5s/.

(2) Although overall, the language was clear and understandable, there are a few parts where language might confuse a reader and lead to misconceptions. For instance, line 52: Did the authors mean to refer to 'emotions and intentions' instead of 'emotions and purposes'? See also examples where rephrasing may help to reflect a statement is speculation rather than fact.

Thanks for the comments. We have carefully checked the full text and rephrased the confused statements.

(3) Line 83/84: Autism is not a 'mental disorder' - please change to something like 'developmental disability'. Authors are encouraged to adapt their language according to terms preferred by the community (e.g., see Fig. 5 in this article:

https://onlinelibrary.wiley.com/doi/10.1002/aur.2864)

Suggestion well taken. We have changed the wording accordingly:

“In recent years, BM perception has received significant attention in studies of mental disorders (e.g., schizophrenia30) and developmental disabilities, particularly in ASD, characterized by deficits in social communication and social interaction31,32.” (lines 93 - 95)

(4) Please report how the sample size for the study was determined.

In the Materials and methods section (lines 168 - 173), we explained how the sample size was determined.

Line 94: It would be helpful to have a brief description of what neurophysiological differences have been observed upon BM perception in children with ADHD.

Thanks for the comment. We have added a brief description of neurophysiological findings in children with ADHD (lines 108 - 111).

(6) Line 106/107 and 108/109: please add references.

We have revised this part, and the relevant findings and references are in line with the revised manuscript (lines 77, 132 - 133).

(7) Line 292: Please add what order the factors were entered into each regression model.

Regarding this issue, we used SPSS 26 for the main analysis. SPSS utilizes the Type III sum of squares (default) to evaluate models. Regardless of the order in the GLM, we will obtain the same result. For more information, please refer to the documentation of SPSS 26 (https://www.ibm.com/docs/en/spss-statistics/26.0.0?topic=features-glm-univariate-analysis).

Reviewer #3 (Recommendations For The Authors)

(1) Task specifics. It is key to understanding the findings, as well as the dissociation between tasks, that the precise nature of the stimuli is clear. I think there is room for improvement in description here. Task 1 is described as involving relocating dots within the range of the intact walker. Of course, PLWs are created by presenting dots at the joints, so relocation can involve either moving to another place on the body, or random movement within the 2D spatial array (which likely involves moving it off the body). Which was done? It is said that Ps must indicate the motion direction, but what was the display of the walker? Sagittal? Task 2 requires detecting whether there is an intact walker amongst scrambled walkers. Were all walkers completely overlaid? Task 3 requires detecting the left v right facing of an intact walker at different orientations, presented amongst noise. So Task 3 requires determining facing direction and Task 1 walking direction. Are these tasks the same but described differently? Or can walkers ever walk backwards? Wrt this point, I also think it would help the reader if example videos were uploaded.

We appreciate you for bringing this to our attention. With regards to Task 1, it appears that your second speculation is correct. We scrambled the original dots and randomly presented them within the 2D spatial array (which likely involved moving them off the body). As a result, the global configuration of the 13 dots was completed disrupted while preserving the motion trajectory of each individual dot. This led to the display of scrambled dots on the monitor (which does not resemble a human). In practice, these local BM cues contain information about motion direction. In Task 2, the target walkers completely overlaid by a mask that is approximately 1.44 times the size of the intact walker. The task requirements of Task 1 and Task3 are same, which is judging the motion (walking) direction. The difference is that Task 1 displayed a scrambled walker while Task 3 displayed an intact walker within a mask. We have clarified these points and improved our descriptions in Procedure section and created example videos for each task, which we believe will be helpful for the readers to understand each task.

(2) Gender confound (see above). I think that the authors should present the results without gender as a covariate. Can they separate boys and girls on the plots with different coloured individual datapoints, such that readers can see whether it's actually a gender effect driving the supposed ADHD effect? And show that there are no signs of a gender effect in their TD group?

This point is similar to the point #1 you mentioned. Please refer to our response to that point above.

(3) Autism possible confound (see above). I think the authors must report whether any of the ADHD group had an autism diagnosis.

Please refer to the response for the point #2 your mentioned.

(4) Conclusions concerning differences between the local and global tasks wrt SRS and age (see above). I believe the authors should add stats demonstrating differences between the correlations to support such claims, as well as demonstrating appropriate scatterplots for SRS-Task 1, SRS-Task 2, SRS-Task 3 and age-Task 1, age-Task2 and age-Task 3 (with separate lines of best fit for the two groups in each).

Please refer to the response for the point #3 your mentioned.

(5) Theoretical assumptions (see above). I would suggest rephrasing all claims here to outline that these discussed mechanistic differences between local and global BM processing are only possibilities and not known on the basis of existing data.

Please refer to the response for the point #4 your mentioned.

Author Response

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

Reviewer #1 (Recommendations For The Authors):

I only have a few minor suggestions:

Abstract: I really liked the conclusion (that IM and VWM are two temporal extremes of the same process) as articulated in lines 557--563. (It is always satisfying when the distinction between two things that seem fundamentally different vanishes). If something like this but shorter could be included in the Abstract, it would highlight the novel aspects of the results a little more, I think.

Thank you for this comment. We have added the following to the abstract:

“A key conclusion is that differences in capacity classically thought to distinguish IM and VWM are in fact contingent upon a single resource-limited WM store.”

L 216: There's an orphan parenthesis in "(justifying the use".

Fixed.

L 273: "One surprising result was the observed set size effect in the 0 ms delay condition". In this paragraph, it might be a good idea to remind the reader of the difference between the simultaneous and zero-delay conditions. If I got it right, the results differ between these conditions because it takes some amount of processing time to interpret the cue and free the resources associated with the irrelevant stimuli. Recalling that fact would make this paragraph easier to digest.

That is correct. However, at this point in the text, we have not yet fitted the DyNR model to the data. Therefore, we believe that introducing cue processing and resource reallocation as concepts that differentiate between those two conditions would disrupt the flow of this paragraph. We address these points soon after, in a paragraph starting on line 341.

Figures 3, 5: The labels at the bottom of each column in A would be more clear if placed at the top of each column instead. That way, the x-axis for the plots in A could be labeled appropriately, as "Error in orientation estimate" or something to that effect.

We edited both figures, now Figure 4 and Figure 6, as suggested.

L 379: It should be "(see Eq 6)", I believe.

That is correct, line 379 (currently line 391) should read ‘Eq 6’. Fixed.

L 379--385: I was a bit mystified as to why the scaled diffusion rate produced a worse fit than a constant rate. I imagine the scaled version was set to something like

sigma^2_diff_scaled = sigma^2_base + K*(N-1)

where N is the set size and sigma^2_base and K are parameters. If this model produced a similar fit as with a constant diffusion rate, the AIC would penalize it because of the extra parameter. But why would the fit be worse (i.e., not match the pattern of variability)? Shouldn't the fitter just find that the K=0 solution is the best? Not a big deal; the Nelder-Mead solutions can wobble when that many parameters are involved, but if there's a simple explanation it might be worth commenting on.

The scaled diffusion was implemented by extending Eq 6 in the following way:

σ(t)2 = (t-toffset) * σ̇ 2diff * N

where N is set size. Therefore, the scaling was not associated with a free parameter that could become 0 if set size did not affect diffusion rate, but variability rather mandatory increased with set size. We now clarify this in the text:

“The second variant was identical to the proposed model, except that we replaced the constant diffusion rate with a set size scaled diffusion rate by multiplying the right side of Eq 6 by N.“

Figure 4 is not mentioned in the main text. Maybe the end of L 398 would be a good place to point to it. The paragraph at L 443-455 would also benefit from a couple of references to it.

Thank you for this suggestion. Figure 4 (now Figure 5) was previously mentioned on line 449 (previously line 437), but now we have included it on line 410 (previously line 398), within the paragraph spanning lines 455-467 (previously 443-455), and also on line 136 where we first discuss masking effects.

L 500: Figure S7 is mentioned before Figures S5 and S6. Quite trivial, I know....

Thank you for this comment. There was no specific reason for Figure S7 to appear after S5 & S6, so we simply swapped their order to be consistent with how they are referred to in the manuscript (i.e., S7 became S5, S5 became S6, and S6 became S7).

Reviewer #2 (Recommendations For The Authors):

(1) One potential weakness is that the model assumes sensory information is veridical. However, this isn't likely the case. Acknowledging noise in sensory representations could affect the model interpretation in a couple of different ways. First, neurophysiological recordings have shown normalization affects sensory representations, even when a stimulus is still present on the screen. The DyNR model partially addresses this concern because reports are drawn from working memory, which is normalized. However, if sensory representations were also normalized, then it may improve the model variant where subjects draw directly from sensory representations (an alternative model that is currently described but discarded).

Thank you for this suggestion. We can consider two potential mechanisms through which divisive normalization might be incorporated into sensory processing within the DyNR model.

The first possibility involves assuming that normalization is pre-attentive. In this scenario, the sensory activity of each object would be rescaled at the lowest level of sensory processing, occurring before the allocation of attentional or VWM resources. One strong prediction of such an implementation is that recall error in the simultaneous cue condition (Experiment 1) should vary with set size. However, this prediction is inconsistent with the observed data, which failed to show a significant difference between set sizes, and is more closely aligned with the hypothesis of no-difference (F(2,18) = 1.26, p = .3, η2 = .04, BF10 = 0.47). On that basis, we anticipate that introducing normalization as a pre-attentive mechanism would impair the model fit.

An alternative scenario is to consider normalization as post-attentive. In the simultaneous cueing condition, only one item is attended (i.e., the cued one), regardless of the displayed set size. Here, we would expect normalized activity for a single item, regardless of the number of presented objects, which would then be integrated into VWM. This expanded DyNR model with post-attentive normalization would make exactly the same predictions as the proposed DyNR for recall fidelity, so distinguishing between these models would not be possible based on working memory experiments.

To acknowledge the possibility that sensory signals could undergo divisive normalization and to motivate future research, we have added the following to our manuscript:

“As well as being implicated in higher cognitive processes including VWM (Buschman et al, 2011; Sprague et al., 2014), divisive normalization has been shown to be widespread in basic sensory processing (Bonin et al., 2005; Busse et al., 2009; Ni et al., 2017). The DyNR model presently incorporates the former but not the latter type of normalization. While the data observed in our experiments do not provide evidence for normalization of sensory signals (note comparable recall errors across set size in the simultaneous cue condition of Experiment 1), this may be because sensory suppressive effects are localized and our stimuli were relatively widely separated in the visual field: future research could explore the consequences of sensory normalization for recall from VWM using, e.g., centre-surround stimuli (Bloem et al., 2018).”

Bloem, I. M., Watanabe, Y. L., Kibbe, M. M., & Ling, S. (2018). Visual Memories Bypass Normalization. Psychological Science, 29(5), 845–856. https://doi.org/10.1177/0956797617747091

Bonin, V., Mante, V., & Carandini, M. (2005). The Suppressive Field of Neurons in Lateral Geniculate Nucleus. The Journal of Neuroscience, 25(47), 10844–10856. https://doi.org/10.1523/JNEUROSCI.3562-05.2005

Buschman, T. J., Siegel, M., Roy, J. E., & Miller, E. K. (2011). Neural substrates of cognitive capacity limitations. Proceedings of the National Academy of Sciences, 108(27), 11252–11255. https://doi.org/10.1073/pnas.1104666108

Busse, L., Wade, A. R., & Carandini, M. (2009). Representation of Concurrent Stimuli by Population Activity in Visual Cortex. Neuron, 64(6), 931–942. https://doi.org/10.1016/j.neuron.2009.11.004

Ni, A. M., & Maunsell, J. H. R. (2017). Spatially tuned normalization explains attention modulation variance within neurons. Journal of Neurophysiology, 118(3), 1903–1913. https://doi.org/10.1152/jn.00218.2017

Sprague, T. C., Ester, E. F., & Serences, J. T. (2014). Reconstructions of Information in Visual Spatial Working Memory Degrade with Memory Load. Current Biology, 24(18), 2174–2180. https://doi.org/10.1016/j.cub.2014.07.066

Second, visual adaptation predicts sensory information should decrease over time. This would predict that for long stimulus presentation times, the error would increase. Indeed, this seems to be reflected in Figure 5B. This effect is not captured by the DyNR model.

Indeed, neural responses in the visual cortex have been observed to quickly adapt during stimulus presentation, showing reduced responses to prolonged stimuli after an initial transient (Groen et al., 2022; Sawamura et al., 2006; Zhou et al., 2019). This adaptation typically manifests as 1) reduced activity towards the end of stimulus presentation and 2) a faster decay towards baseline activity after stimulus offset.

In the DyNR model, we use an idealized solution in which we convolve the presented visual signal with a response function (i.e., temporal filter). At the longest presentation durations, in DyNR, the sensory signal plateaus and remains stable until stimulus offset. Because our psychophysical data does not allow us to identify the exact neural coding scheme that underlies the sensory signal, we tend to favour this simple implementation, which is broadly consistent with some previous attempts to model temporal dynamics in sensory responses (e.g., Carandini and Heeger, 1994). However, we agree with the reviewer that some adaptation of the sensory signal with prolonged presentation would also be consistent with our data.

We have added the following to the manuscript:

“In Experiment 2, the longest presentation duration shows an upward trend in error at set sizes 4 and 10. While this falls within the range of measurement error, it is also possible that this is a meaningful pattern arising from visual adaptation of the sensory signal, whereby neural populations reduce their activity after prolonged stimulation. This would mean less residual sensory signal would be available after the cue to supplement VWM activity, predicting a decline in fidelity at higher set sizes. Visual adaptation has previously been successfully accounted for by a type of delayed normalization model in which the sensory signal undergoes a series of linear and nonlinear transformations (Zhou et al., 2019). Such a model could in future be incorporated into DyNR and validated against psychophysical and neural data.”

Carandini, M., & Heeger, D. J. (1994). Summation and division by neurons in primate visual cortex. Science, 264(5163), 1333–1336. https://doi.org/10.1126/science.8191289

Groen, I. I. A., Piantoni, G., Montenegro, S., Flinker, A., Devore, S., Devinsky, O., Doyle, W., Dugan, P., Friedman, D., Ramsey, N. F., Petridou, N., & Winawer, J. (2022). Temporal Dynamics of Neural Responses in Human Visual Cortex. The Journal of Neuroscience, 42(40), 7562–7580. https://doi.org/10.1523/JNEUROSCI.1812-21.2022

Sawamura, H., Orban, G. A., & Vogels, R. (2006). Selectivity of Neuronal Adaptation Does Not Match Response Selectivity: A Single-Cell Study of the fMRI Adaptation Paradigm. Neuron, 49(2), 307–318. https://doi.org/10.1016/j.neuron.2005.11.028

Zhou, J., Benson, N. C., Kay, K., & Winawer, J. (2019). Predicting neuronal dynamics with a delayed gain control model. PLOS Computational Biology, 15(11), e1007484. https://doi.org/10.1371/journal.pcbi.1007484

(2) A second potential weakness is that, in Experiment 1, the authors briefly change the sensory stimulus at the end of the delay (a 'phase shift', Fig. 6A). I believe this is intended to act as a mask. However, I would expect that, in the DyNR model, this should be modeled as a new sensory input (in Experiment 2, 50 ms is plenty of time for the subjects to process the stimuli). One might expect this change to disrupt sensory and memory representations in a very characteristic manner. This seems to make a strong testable hypothesis. Did the authors find evidence for interference from the phase shift?

The phase shift was implemented with the intention of reducing retinal after-effects, essentially acting as a mask for retinal information only; crucially the orientation of the stimulus is unchanged by the phase shift, so from the perspective of the DyNR model, it transmits the same orientation information to working memory as the original stimulus.

If our objective were to model sensory input at the level of individual neurons and their receptive fields, we would indeed need to treat this phase shift as a novel input. Nevertheless, for DyNR, conceived as an idealization of a biological system for encoding orientation information, we can safely assume that visual areas in biological organisms have a sufficient number of phase-sensitive simple cells and phase-indifferent complex cells to maintain the continuity of input to VWM.

When comparing conditions with and without the phase shift of stimuli (Fig S1B), we found performance to be comparable in the perceptual condition (simultaneous presentation) and with the longest delay (1 second), suggesting that the phase shift did not change the visibility or encoding of information into VWM. In contrast, we found strong evidence that observers had access to an additional source of information over intermediate delays when the phase shift was not used. This was evident through enhanced recall performance from 0 ms to 400 ms delay. Based on this, we concluded that the additional source of information available in the absence of a phase shift was accessible immediately following stimulus offset and had a brief duration, aligning with the theoretical concept of retinal afterimages.

(3) It seems odd that the mask does not interrupt sensory processing in Experiment 2. Isn't this the intended purpose of the mask? Should readers interpret this as all masks not being effective in disrupting sensory processing/iconic memory? Or is this specific to the mask used in the experiment?

Visual masks are often described as instantly and completely halting the visual processing of information that preceded the mask. We also anticipated the mask would entirely terminate sensory processing, but our data indicate the effect was not complete (as indicated by model variants in Experiment 2). Nevertheless, we believe we achieved our intended goal with this experiment – we observed a clear modulation of response errors with changing stimulus duration, indicating that the post-stimulus information that survived masking did not compromise the manipulation of stimulus duration. Moreover, the DyNR model successfully accounted for the portion of signal that survived the mask.

We can identify two possible reasons why masking was incomplete. First, it is possible that the continuous report measure used in our experiments is more sensitive than the discrete measures (e.g., forced-choice methods) commonly employed in experiments that found masks to be 100% effective. Second, despite using a flickering white noise mask at full contrast, it is possible that it may not have been the most effective mask; for instance, a mask consisting of many randomly oriented Gabor patches matched in spatial frequency to the stimuli could prove more effective. We decided against such a mask because we were concerned that it could potentially act as a new input to orientation-sensitive neurons, rather than just wiping out any residual sensory activity.

(4) I apologize if I missed it, but the authors did not compare the DyNR model to a model without decaying sensory information for Experiment 1.

We tested two DyNR variants in which the diffusion process was solely responsible for memory fidelity dynamics. These models assumed that the sensory signal terminates abruptly with stimuli offset, and the VWM signal encoding the stimuli was equal to the limit imposed by normalization, independent of the delay duration.

As variants of this model failed to account for the observed response errors both quantitatively (see 'Fixed neural signal' under Model variants) and qualitatively (Figure S3), we decided not to test any more restrictive variants, such as the one without sensory decay and diffusion.

(5) In the current model, selection is considered to be absolute (all or none). However, this need not be the case (previous work argues for graded selection). Could a model where memories are only partially selected, in a manner that is mediated by load, explain the load effects seen in behavior?

Thank you for this point. If attentional selection was partial, it would affect the observers’ efficiency in discarding uncued objects to release allocated resources and encode additional information about the cued item. We and others have previously examined whether humans can efficiently update their VWM when previous items become obsolete. For example, Taylor et al. (2023) showed that observers could efficiently remove uncued items from VWM and reallocate the released resources to new visual information. These findings align with results from other studies (e.g., Ecker, Oberauer, & Lewandowsky, 2014; Kessler & Meiran, 2006; Williams et al., 2013).

Based on these findings, we feel justified in assuming that observers in our current task were capable of fully removing all uncued objects, allowing them to continue the encoding process for the cued orientation that was already partially stored in VWM, such that the attainable limit on representational precision for the cued item equals the maximum precision of VWM.

Partial removal could in principle be modelled in the DyNR model by introducing an additional plateau parameter specifying a maximum attainable precision after the cue. Our concern would be that such a plateau parameter would trade off with the parameter associated with Hick’s law (i.e., cue interpretation time). The former would control the amount of information that can be encoded into VWM, while the latter regulates the amount of sensory information available for encoding. We are wary of adding additional parameters, and hence flexibility, to the model where we do not have the data to sufficiently constrain them.

Ecker, U. K. H., Oberauer, K., & Lewandowsky, S. (2014b). Working memory updating involves item-specific removal. Journal of Memory and Language, 74, 1–15. https://doi.org/10.1016/j.jml. 2014.03.006

Kessler, Y., & Meiran, N. (2006). All updateable objects in working memory are updated whenever any of them are modified: Evidence from the memory updating paradigm. Journal of Experimental Psychology: Learning, Memory, and Cognition, 32, 570–585. https://doi.org/10.1037/0278-7393.32.3.570

Taylor, R., Tomić, I., Aagten-Murphy, D., & Bays, P. M. (2023). Working memory is updated by reallocation of resources from obsolete to new items. Attention, Perception, & Psychophysics, 85(5), 1437–1451. https://doi.org/10.3758/s13414-022-02584-2

Williams, M., & Woodman, G. F. (2012). Directed forgetting and directed remembering in visual working memory. Journal of Experimental Psychology. Learning, Memory, and Cognition, 38(5), 1206–1220. https://doi.org/10.1037/a0027389

(6) Previous work, both from the authors and others, has shown that memories are biased as if they are acted on by attractive/repulsive forces. For example, the memory of an oriented bar is biased away from horizontal and vertical and biased towards diagonals. This is not accounted for in the current model. In particular, this could be one mechanism to generate a non-uniform drift rate over time. As noted in the paper, a non-uniform drift rate could capture many of the behavioral effects reported.

The reviewer is correct that the model does not currently include stimulus-specific effects, although our work on that topic provides a clear template for incorporating them in future (e.g. Taylor & Bays, 2018). Specifically on the question of generating a non-uniform drift, we have another project that currently looks at this exact question (cited in our manuscript as Tomic, Girones, Lengyel, and Bays; in prep.). By examining various datasets with varying memory delays, including the Additional Dataset 1 reported in the Supplementary Information, we found that stimulus-specific effects on orientation recall remain constant with retention time. Specifically, although there is a clear increase in overall error over time, estimation biases remain constant in direction and amplitude, indicating that the bias does not manifest in drift rates (see also Rademaker et al., 2018; Figure S1).

Taylor, R., & Bays, P. M. (2018). Efficient coding in visual working memory accounts for stimulus-specific variations in recall. The Journal of Neuroscience, 1018–18. https://doi.org/10.1523/JNEUROSCI.1018-18.2018

Rademaker, R. L., Park, Y. E., Sack, A. T., & Tong, F. (2018). Evidence of gradual loss of precision for simple features and complex objects in visual working memory. Journal of Experimental Psychology: Human Perception and Performance. https://doi.org/10.1037/xhp0000491

(7) Finally, the authors use AIC to compare many different model variants to the DyNR model. The delta-AICs are high (>10), indicating a strong preference for the DyNR model over the variants. However, the overall quality of fit to the data is not clear. What proportion of the variance in data was the model able to explain? In particular, I think it would be helpful for the reader if the authors reported the variance explained on withheld data (trials, conditions, or subjects).

Thank you for this comment.

Below we report the estimates of r2, representing the goodness of fit between observed data (i.e., RMSE) and the DyNR model predictions.

In Experiment 1, the r2 values between observations and predictions were computed across delays for each set size, yielding the following estimates: r2ss1 = 0.60; r2ss4 = 0.87; r2ss10 = 0.95. Note that lower explained variance for set size 1 arises from both data and model predictions having near-constant precision.

In Experiment 2, we calculated r2 between observations and predictions across presentation durations, separately for each set size, resulting in the following estimates: r2ss1 = 0.88; r2ss4 = 0.71; r2ss10 = 0.70. Note that in this case the decreasing percentage of explained variance with set size is a consequence of having less variability in both data and model predictions with larger set sizes.

While these estimates suggest that the DyNR model effectively fits the psychophysical data, a more rigorous validation approach would involve cross-validation checks across all conditions with a withheld portion of trials. Regrettably, due to the large number of conditions in each experiment, we could only collect 50 trials per condition. We are sceptical that fitting the model to even fewer trials, as necessary for cross-validation, would provide a reliable assessment of model performance.

Minor: It isn't clear to me why the behavioral tasks are shown in Figure 6. They are important for understanding the results and are discussed earlier in the manuscript (before Figure 3). This just required flipping back and forth to understand the task before I could interpret the results.

Thank you for this comment. We have now moved the behavioural task figure to appear early in the manuscript (as Figure 3).

Reviewer #3 (Recommendations For The Authors):

(1) Dynamics of sensory signals during perception

I believe that the modeled sensory signal is a reasonable simplification and different ways to model the decay function are discussed. I would like to ask the authors to discuss the implications of slightly more complex initial sensory transients such as the ones shown in Teeuwen (2021). Specifically for short exposure times, this might be particularly relevant for the model fits as some of the alternative models diverge from the data for short exposures. In addition, the role of feedforward (initial transient?) and feedback signaling (subsequent "plateau" activity) could be discussed. The first one might relate more strongly to sensory signals whereas the latter relates more to top-down attention/recurrent processing/VWM.

Particularly, this latter response might also be sensitive to the number of items present on the screen which leads to a related question pertaining to the limitations of attention during perception. Some work suggests that perception is similarly limited in the amount of information that can be represented concurrently (Tsubomi, 2013). Could the authors discuss the implications of this hypothesis? What happens if maximum sensory amplitude is set as a free parameter in the model?

Tsubomi, H., Fukuda, K., Watanabe, K., & Vogel, E. K. (2013). Neural limits to representing objects still within view. Journal of Neuroscience, 33(19), 8257-8263.

Thank you for this question. Below, we unpack it and answer it point by point.

While we agree our model of the sensory response is justified as an idealization of the biological reality, we also recognise that recent electrophysiological recordings have illuminated intricacies of neuronal responses within the striate cortex, a critical neural region associated with sensory memory (Teeuwen et al, 2021). Notably, these recordings reveal a more nuanced pattern where neurons exhibit an initial burst of activity succeeded by a lower plateau in firing rate, and stimulus offset elicits a second small burst in the response of some neurons, followed by a gradual decrease in activity after the stimulus disappears (Teeuwen et al, 2021).

In general, asynchronous bursts of activity in individual neurons will tend to average out in the population making little difference to predictions of the DyNR model. Synchronized bursts at stimulus onset could affect predictions for the shortest presentations in Exp 2, however the model appears to capture the data very well without including them. We would be wary of incorporating these phenomena into the model without more clarity on their universality (e.g., how stimulus-dependent they are), their significance at the population level (as opposed to individual neurons), and most importantly, their prominence in visual areas outside striate cortex. Specifically, while Teeuwen et al. (2021) described activity in V1, our model does not make strong assumptions about which visual areas are the source of the sensory input to WM. Based on these uncertainties we believe the idealized sensory response is justified for use in our model.

Next, thank you for the comment on feedforward and feedback signals. We have added the following to our manuscript:

“Following onset of a stimulus, the visual signal ascends through visual areas via a cascade of feedforward connections. This feedforward sweep conveys sensory information that persists during stimulus presentation and briefly after it disappears (Lamme et al., 1998). Simultaneously, reciprocal feedback connections carry higher-order information back towards antecedent cortical areas (Lamme and Roelfsema, 2000). In our psychophysical task, feedback connections likely play a critical role in orienting attention towards the cued item, facilitating the extraction of persisting sensory signals, and potentially signalling continuous information on the available resources for VWM encoding. While our computational study does not address the nature of these feedforward and feedback signals, a challenge for future research is to describe the relative contributions of these signals in mediating transmission of information between sensory and working memory (Semedo et al., 2022).”

Lamme, V. A., Supèr, H., & Spekreijse, H. (1998). Feedforward, horizontal, and feedback processing in the visual cortex. Current Opinion in Neurobiology, 8(4), 529–535. https://doi.org/10.1016/S0959-4388(98)80042-1

Lamme, V. A. F., & Roelfsema, P. R. (2000). The distinct modes of vision offered by feedforward and recurrent processing. Trends in Neurosciences, 23(11), 571–579. https://doi.org/10.1016/S0166-2236(00)01657-X

Semedo, J. D., Jasper, A. I., Zandvakili, A., Krishna, A., Aschner, A., Machens, C. K., Kohn, A., & Yu, B. M. (2022). Feedforward and feedback interactions between visual cortical areas use different population activity patterns. Nature Communications, 13(1), 1099. https://doi.org/10.1038/s41467-022-28552-w

Finally, both you and Reviewer 2 raised a similar interesting question regarding capacity limitations of attention during perception Such a limitation could be modelled by freely estimating sensory amplitude and implementing divisive normalization to that signal, similar to how VWM is constrained. We can consider two potential mechanisms through which divisive normalization might be incorporated into sensory processing within the DyNR model.

The first possibility involves assuming that normalization is pre-attentive. In this scenario, the sensory activity of each object would be rescaled at the lowest level of sensory processing, occurring before the allocation of attentional or VWM resources. One strong prediction of such an implementation is that recall error in the simultaneous cue condition (Experiment 1) should vary with set size. However, this prediction is inconsistent with the observed data, which failed to show a significant difference between set sizes, and is more closely aligned with the hypothesis of no-difference (F(2,18) = 1.26, p = .3, η2 = .04, BF10 = 0.47). On that basis, we anticipate that introducing normalization as a pre-attentive mechanism would impair the model fit.

An alternative scenario is to consider normalization as post-attentive. In the simultaneous cueing condition, only one item is attended (i.e., the cued one), regardless of the displayed set size. Here, we would expect normalized activity for a single item, regardless of the number of presented objects, which would then be integrated into VWM. This expanded DyNR model with post-attentive normalization would make exactly the same predictions as the proposed DyNR for recall fidelity, so distinguishing between these models would not be possible based on working memory experiments.

To acknowledge the possibility that sensory signals could undergo divisive normalization and to motivate future research, we have added the following to our manuscript:

“As well as being implicated in higher cognitive processes including VWM (Buschman et al, 2011; Sprague et al., 2014), divisive normalization has been shown to be widespread in basic sensory processing (Bonin et al., 2005; Busse et al., 2009; Ni et al., 2017). The DyNR model presently incorporates the former but not the latter type of normalization. While the data observed in our experiments do not provide evidence for normalization of sensory signals (note comparable recall errors across set size in the simultaneous cue condition of Experiment 1), this may be because sensory suppressive effects are localized and our stimuli were relatively widely separated in the visual field: future research could explore the consequences of sensory normalization for recall from VWM using, e.g., centre-surround stimuli (Bloem et al., 2018).”

Bloem, I. M., Watanabe, Y. L., Kibbe, M. M., & Ling, S. (2018). Visual Memories Bypass Normalization. Psychological Science, 29(5), 845–856. https://doi.org/10.1177/0956797617747091

Bonin, V., Mante, V., & Carandini, M. (2005). The Suppressive Field of Neurons in Lateral Geniculate Nucleus. The Journal of Neuroscience, 25(47), 10844–10856. https://doi.org/10.1523/JNEUROSCI.3562-05.2005

Buschman, T. J., Siegel, M., Roy, J. E., & Miller, E. K. (2011). Neural substrates of cognitive capacity limitations. Proceedings of the National Academy of Sciences, 108(27), 11252–11255. https://doi.org/10.1073/pnas.1104666108

Busse, L., Wade, A. R., & Carandini, M. (2009). Representation of Concurrent Stimuli by Population Activity in Visual Cortex. Neuron, 64(6), 931–942. https://doi.org/10.1016/j.neuron.2009.11.004

Ni, A. M., & Maunsell, J. H. R. (2017). Spatially tuned normalization explains attention modulation variance within neurons. Journal of Neurophysiology, 118(3), 1903–1913. https://doi.org/10.1152/jn.00218.2017

Sprague, T. C., Ester, E. F., & Serences, J. T. (2014). Reconstructions of Information in Visual Spatial Working Memory Degrade with Memory Load. Current Biology, 24(18), 2174–2180. https://doi.org/10.1016/j.cub.2014.07.066

(2) Effectivity of retro-cues at long delays

Can the authors discuss how cues presented at long delays (>1000 ms) can still lead to increased memory fidelity when sensory signals are likely to have decayed? A list of experimental work demonstrating this can be found in Souza & Oberauer (2016).

Souza, A. S., & Oberauer, K. (2016). In search of the focus of attention in working memory: 13 years of the retro-cue effect. Attention, Perception, & Psychophysics, 78, 1839-1860.

The increased memory fidelity observed with longer delays between memory array offset and cue does not result from integrating available sensory signals into VWM because the sensory signal would have completely decayed by that time. Instead, research so far has indicated several alternative mechanisms that could lead to higher recall precision for cued items, and we can briefly summarize some of them, which are also reviewed in more detail in Souza and Oberauer (2016).

One possibility is that, after a highly predictive retro-cue indicates the to-be-tested item, uncued items can simply be removed from VWM. This could result in decreased interference for the cued item, and consequently higher recall precision. Secondly, the retro-cue could also indicate which item can be selectively attended to, and thereby differentially strengthening it in memory. Furthermore, the retro-cue could allow evidence to accumulate for the target item ahead of decision-making, and this could increase the probability that the correct information will be selected for response. Finally, the retro-cued stimulus could be insulated from interference by subsequent visual input, while the uncued stimuli may remain prone to such interference.

A neural account of this retro-cue effect based on the original neural resource model has been proposed in Bays & Taylor, Cog Psych, 2018. However, as we did not use a retro-cue design in the present experiments, we have decided not to elaborate on this in the manuscript.

(3) Swap errors

I am somewhat surprised by the empirically observed and predicted pattern of swap errors displayed in Figure S2. For set size 10, swap probability does not consistently increase with the duration of the retention interval, although this was predicted by the author's model. At long intervals, swap probability is significantly higher for large compared to small set sizes, which also seems to contrast with the idea of shared, limited VWM resources. Can the authors provide some insight into why the model fails to reproduce part of the behavioral pattern for swap errors? The sentence in line 602 might also need some reconsideration in this regard.

Determining the ground truth for swap errors poses a challenge. The prevailing approach has been to employ a simpler model that estimates swap errors, such as a three-component mixture model, and use those estimates as a proxy for ground truth. However, this method is not without its shortcomings. For example, the variability of swap frequency estimates tends to increase with variability in the report feature dimension (here, orientation). This is due to the increasing overlap of response probability distributions for swap and non-swap responses. Consequently, the discrepancy between any two methods of swap estimation is most noticeable when there is substantial variability in orientation reports (e.g., 10 items and long delay or short exposure).

When modelling swap frequency in the DyNR model, our aim was to provide a parsimonious account of swap errors while implementing similar dynamics in the spatial (cue) feature as in the orientation (report) feature. This parametric description captured the overall pattern of swap frequency with set size and retention and encoding time, but is still only an approximation of the predictions if we fully modelled memory for the conjunction of cue and report features (as in e.g. Schneegans & Bays, 2017; McMaster et al, 2020).

We expanded the existing text in the section ‘Representational dynamics of cue-dimension features’ of our manuscript:

“… Although we did not explicitly model the neural signals representing location, the modelled dynamics in the probability of swap errors were consistent with those of the primary memory feature. We provided a more detailed neural account of swap errors in our earlier works that is theoretically compatible with the DyNR model (McMaster et al., 2020; Schneegans & Bays, 2017).

The DyNR model successfully captured the observed pattern of swap frequencies (intrusion errors). The only notable discrepancy between DyNR and the three-component mixture model (Fig. S2) arises with the largest set size and longest delay, although with considerable interindividual variability. As the variability in report-dimension increases, the estimates of swap frequency become more variable due to the growing overlap between the probability distributions of swap and non-swap responses. This may explain apparent deviations from the modelled swap frequencies with the highest set size and longest delay where orientation response variability was greatest. “

McMaster, J. M. V., Tomić, I., Schneegans, S., & Bays, P. M. (2022). Swap errors in visual working memory are fully explained by cue-feature variability. Cognitive Psychology, 137, 101493. https://doi.org/10.1016/j.cogpsych.2022.101493

Schneegans, S., & Bays, P. M. (2017). Neural Architecture for Feature Binding in Visual Working Memory. The Journal of Neuroscience, 37(14), 3913–3925. https://doi.org/10.1523/JNEUROSCI.3493-16.2017

(4) Direct sensory readout

The model assumes that readout from sensory memory and from VWM happens with identical efficiency. Currently, we don't know if these two systems are highly overlapping or are fundamentally different in terms of architecture and computation. In the case of the latter, it might be less reasonable to assume that information readout would happen at similar efficiencies, as it is currently assumed in the manuscript. Perhaps the authors could briefly discuss this possibility.

In the direct sensory read-out model, we did not explicitly model the efficiency of readout from either sensory or VWM store. However, the distinctive prediction of this model is that the precision of recall changes exponentially with delay at every set size, including one item. This prediction does not depend on the relative efficiency of readout from sensory and working memory, but only on the principle that direct readout from sensory memory bypasses the capacity limit on working memory. This prediction is inconsistent with the pattern of results observed in Experiment 1, where early cues did not show a beneficial effect on recall error for set size 1. While the proposal raised by the reviewer is intriguing, even if we were to model the process of readout from both the sensory and VWM stores with different efficiencies, the direct read-out model could not account for the near-constant recall error with delay for set size one.

(5) Encoding of distractors

One of the model assumptions is that, for simultaneous presentations of memory array and cue only the cued feature will be encoded. Previous work has suggested that participants often accidentally encode distractors even when they are cued before memory array onset (Vogel 2005). Given these findings, how reasonable is this assumption in the authors' model?

Vogel, E. K., McCollough, A. W., & Machizawa, M. G. (2005). Neural measures reveal individual differences in controlling access to working memory. Nature, 438(7067), 500-503.

Although previous research suggested that observers can misinterpret the pre-cue and encode one of the uncued items, our results argue against this being the case in the current experiment. Such encoding failures would manifest in overall recall error, resulting in a gradient of error with set size, owing to the presence of more adjacent distractors in larger set sizes. However, when we compared recall errors between set sizes in the simultaneous cue condition, we did not find a significant difference between set sizes, and moreover, our results were more likely under the hypothesis of no-difference (F(2,18) = 1.26, p = .3, η2 = .04, BF10 = 0.47). If observers occasionally encoded and reported one of the uncued items in the simultaneous cue condition, those errors were extremely infrequent and did not affect the overall error distributions.

Author Response

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this manuscript, Zeng and Staley provide a valuable analysis of the molecular requirements for the export of a reporter mRNA that contains a lariat structure at its 5' end in the budding yeast S. cerevisiae. The authors provide evidence that this is regulated by the main mRNA export machinery (Yra1, Mex67, Nab2, Npl3, Tom1, and Mlp1). Of note, Mlp1 has been mainly implicated in the nuclear retention of unspliced pre-mRNA (i.e. quality control), and relatively little has been done to investigate its role in mRNA export in budding yeast.

Strengths:

There is relatively little information in the current literature about the nuclear export of splicing intermediates. This paper provides one of the first analyses of this process and dissects the molecular components that promote this form of RNA export. Overall, the strength of the data presented in the manuscript is solid. The paper is well written and the message is clear and of general interest to the mRNA community.

We thank the reviewer for highlighting these strengths.

Weaknesses:

There are three problems with the paper, although these are not major and likely would not affect the final model as most aspects of the molecular details are confirmed by multiple complementary assays.

(1) The brG reporter produces both unspliced pre-mRNA and a lariat-containing intermediate RNA. Based on the primer extension assay the authors claim that only 33% of the final product is in pre-mRNA form and that this "is insufficient to account for the magnitude of the cytoplasmic signal from the brG reporter (83%)". Nevertheless, it is possible that primer extension is incomplete or that the lariat-containing RNA is inaccessible for smFISH. The authors could easily perform a dual smFISH experiment (similar to Adivarahan et l., Molecular Cell 2018) where exon 1 is labelled with probes of one color, and the region that overlaps the lariat-containing intermediate is labelled with probes of a second color. If the authors are correct, then one-third of the smFISH foci should have both labels and the rest would have only the second label. This would also confirm that the latter (i.e. the lariat-containing RNAs) are exported to the cytoplasm. Using this approach, the authors could then show that MLP1-depletion (or depletion of any of the other factors) affect(s) one pool of RNAs (i.e. those that are lariat-containing) but not the other (i.e. pre-mRNA). Including these experiments would make the evidence for their model more convincing.

We appreciate the reviewer’s comments and suggestions. Concerning the primer extension analysis, we are considering alternative assays to quantitate the pre-mRNA and lariat intermediate levels. Concerning the accessibility of the lariat intermediate in smRNA-FISH, in a dbr1∆ strain the only major species from the UAc reporter that is detected by primer extension is the lariat intermediate (Fig. S3), and this reporter is readily detected by smRNA-FISH, indicate that the lariat intermediate is accessible to smRNA-FISH. Concerning discriminating between pre-mRNA and lariat intermediate by smRNA-FISH, we agree with the reviewer that a dual smFISH experiment would directly distinguish between the signals of these species. The brG reporter we used in most smRNA-FISH experiments has a 5’ exon that is too short for smRNA-FISH probes, as is typical of most budding yeast 5’ exons. We have tried to replace the 5’ exon with a longer sequence (GFP) to allow for smRNA-FISH; however, this substitution inhibited splicing. Therefore, to distinguish signals from pre-mRNA versus lariat intermediate, we used additional reporters: G1c and brC reporters, which accumulate pre-mRNA essentially exclusively (Fig. S2A-C), and the UAc reporter, which accumulates lariat intermediate exclusively, in a dbr1∆ strain (Fig. S3). Whereas the mlp1 deletion did not change beta-galactosidase activities of the G1c and brC pre-mRNA-accumulating reporters (Fig. S2E), the mlp1 deletion in a dbr1∆ background did reduce the beta-galactosidase activities of the UAc lariat intermediate-accumulating reporter (Fig. 3D) and did increase smRNA-FISH signal of this reporter in the nucleus (Fig. 3E). These observations corroborate our interpretation based on the brG reporter that Mlp1p is required for efficient export of lariat intermediates but not pre-mRNAs.

(2) In some cases, the number of smFISH foci appears to change drastically depending on the genetic background. This could either be due to the stochastic nature of mRNA expression between cells or reflect real differences between the genetic backgrounds that could alter the interpretation of the other observations.

We thank the reviewer for raising this point. We will review our data to distinguish between these possibilities.

(3) The authors state in the discussion that "the general mRNA export pathway transports discarded lariat intermediates into the cytoplasm". Although this appears to be the case for the reporters that are investigated in this paper, I don't think that the authors should make such a broad sweeping claim. It may be that some discarded lariat intermediates are exported to the cytoplasm while others are targeted for nuclear retention and/or decay.

The reviewer’s point is well-taken. We will revise the wording accordingly.

Reviewer #2 (Public Review):

In this report, Zeng and Staley have used an elegant combination of RNA imaging approaches (single molecule FISH), RNA co-immunoprecipitations, and translation reporters to characterize the factors and pathways involved in the nuclear export of splicing intermediates in budding yeast. Their study notably involves the use of specific reporter genes, which lead to the accumulation of pre-mRNA and lariat species, in a battery of mutants impacting mRNA export and quality control.

The authors convincingly demonstrate that mRNA species expressed from such reporters are exported to the cytoplasm in a manner depending on the canonical mRNA export machinery (Mex67 and its adaptors) and the nuclear pore complex (NPC) basket (Mlp1). Interestingly, they provide evidence that the export of splicing intermediates requires docking and subsequent undocking at the nuclear basket, a step possibly more critical than for regular mRNAs.

We thank the reviewer for this overall positive assessment.

However, their assays do not always allow us to define whether the impacted mRNA species correspond to lariats and/or pre-mRNAs. This is all the more critical since their findings apparently contradict previous reports that supported a role for the nuclear basket in pre-mRNA quality control. These earlier studies, which were similarly based on the use of dedicated yet distinct reporters, had found that the nuclear basket subunit Mlp1, together with different cofactors, prevents the export of unspliced mRNA species. It would be important to clarify experimentally and discuss the possible reasons for these discrepancies.

It is true that we did not assess export of all reporters in all mutant strains by smFISH; however, we did validate the key conclusion that the export of lariat intermediates requires the nuclear basket gene MLP1: the export of both the brG reporter (mostly lariat intermediate) and the UAc reporter (exclusively lariat intermediate) showed a dependence on MLP1 (Fig. 3). Further, by beta-galactosidase activity, we tested in total five separate reporters – three that accumulated lariat intermediate and two that accumulated exclusively pre-mRNA; only the three reporters accumulating lariat intermediate showed a dependence of export on MLP1 (Fig. 4B,D; Fig S2D); the reporters accumulating pre-mRNA did not show a dependence on MLP1 (Fig. S2E), further validating our main conclusion. We are considering additional experiments to validate this key conclusion even further. Also, see response to comment 1 from reviewer 1.

We agree that the main conclusion from this manuscript differs from earlier studies. A key difference is that prior studies monitored exclusively pre-mRNA. In our study, we monitored pre-mRNA and lariat intermediate species and in doing so revealed a role for MLP1 in the export of lariat intermediates. This study, our previous study, as well as the previous studies of others have all provided evidence for efficient export of pre-mRNA; all of these studies are in conflict with the studies purporting a general role for the nuclear basked in retaining immature mRNA. Still, these past apparently conflicting studies can be re-interpreted in the context of our model that the export of such species requires docking at the nuclear basket, followed by undocking. In a revised manuscript, we will discuss the possibility that pre-mRNA apparently “retained” by the nuclear basket are stalled in export at the undocking stage.

Reviewer #3 (Public Review):

Summary:

Zeng and Stanley show that in yeast, intron-lariat intermediates that accumulated due to defects in pre-mRNA splicing, are transported to the cytoplasm using the canonical mRNA export pathway. Moreover, they demonstrate that export requires the nuclear basket, a sub-structure of the nuclear pore complex previously implicated with the retention of immature mRNAs. These observations are important as they put into question a longstanding model that the main role of the nuclear basket is to ensure nuclear retention of immature or faulty mRNAs.

Strengths:

The authors elegantly combine genetic, biochemical, and single-molecule resolution microscopy approaches to identify the cellular pathway that mediates the cytoplasmic accumulation of lariat intermediates. Cytoplasmic accumulation of such splicing intermediates had been observed in various previous studies but how these RNAs reach the cytoplasm had not yet been investigated. By using smFISH, the authors present compelling, and, for the first time, direct evidence that these intermediates accumulate in the cytoplasm and that this requires the canonical mRNA export pathway, including the RNA export receptor Mex67 as well as various RNA-binding proteins including Yra1, Npl3 and Nab2. Moreover, they show that the export of lariat intermediates, but not mRNAs, requires the nuclear basket (Mlp1) and basket-associated proteins previously linked to the mRNP rearrangements at the nuclear pore. This is a surprising and important observation with respect to a possible function of the nuclear basket in mRNA export and quality control, as it challenges a longstanding model that the role of the basket in mRNA export is primarily to act as a gatekeeper to ensure that immature mRNAs are not exported. As discussed by the authors, their finding suggests a role for the basket in promoting the export of certain types of RNAs rather than retention, a model also supported by more recent studies in mammalian cells. Moreover, their findings also collaborate with a recent paper showing that in yeast, not all nuclear pores contain a basket (PMID: 36220102), an observation that also questioned the gatekeeper model of the basket, as it is difficult to imagine how the basket can serve as a gatekeeper if not all nuclear pore contain such a structure.

We thank the reviewer for highlighting the importance and surprising nature of our findings.

Weaknesses:

One weakness of this study is that all their experiments rely on using synthetic splicing reporter containing a lacZ gene that produces a relatively long transcript compared to the average yeast mRNA.

We are considering repeating some of our experiments to monitor export of RNAs with more average lengths.

The rationale for using a reporter containing the brG (G branch point) resulting in more stable lariat intermediates due to them being inefficient substrates for the debranching enzyme Dbr1 could be described earlier in the manuscript, as this otherwise only becomes clear towards the end, what is confusing.

We thank the reviewer for this comment. We will revise the text to explain sooner the rationale for using the brG reporter to assess the export of lariat intermediates.

Discussion of their observation in the context that, in yeast, not all pores contain a basket would be useful.

Thanks for this suggestion. We will raise this point that a nuclear basket is not present on all nuclear pores and discuss the implications.

Author Response

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

Public Review:

Summary:

This paper reports how mycobacterial cAMP level is increased under stressful conditions and that the increase is important in the survival of the bacterium in animal hosts.

Strengths:

The authors show that under different stresses the response regulator PhoP represses a phosphodiesterase (PDE) that degrades cAMP specifically. Identification of a PDE specific to cAMP is significant progress in understanding Mtb pathogenesis. An increase in cAMP apparently increases bacterial survival upon infection. On the practical side, the reduction of cAMP by increasing PDE can be a means to attenuate the growth of the bacilli. The results have wider implications since PhoP is implicated in controlling diverse mycobacterial stress responses and many bacterial pathogens modulate host cell cAMP level. The results here are straightforward, internally consistent, and of both theoretical and applied interests.

We thank the reviewers for these extremely encouraging comments.

Weaknesses:

Repression of PDE promoter by binding of phosphorylated PhoP could have been shown at higher precision. The binding is now somewhere along a roughly 500 bp region. Although the regulation of PDE is shown to be by transcriptional repression only, it has been described as a homeostatic mechanism. The latter would have required a demonstration of both repression and activation by negative feedback.

We agree. We have now performed EMSA (Electrophoretic Mobility Shift Assay) experiments and included the data showing DNA binding of PhoP to the upstream regulatory region of rv0805 (rv0805up) as a supplemental figure (see Figure 2-figure supplement 1). The supplemental figure, figure caption, and the relevant results have been adjusted accordingly in the revised manuscript.

Further, as recommended by the reviewer we have now removed the term ‘homeostatic mechanism’ and rephrased it with ‘maintenance of cAMP level’ in the manuscript.

Response to Reviewers’ comments

Reviewer #1:

The authors have used homeostasis inappropriately. Homeostasis usually requires negative feedback (a clear example is the regulation of Lambda prm promoter). Here, there is no feedback from changes in PDE or cAMP level to their synthesis. Homeostasis does not belong to this paper anywhere.

As recommended by the reviewer, we have now removed “homeostasis” from the manuscript and mostly replaced it with “maintenance of cAMP level” in the revised manuscript.

The authors have frequently used adverbs at the beginning of a sentence, such as Notably (l.240, 272, 376), Importantly (l.66, 213), More importantly (l.134), Remarkably (l.264), Interestingly (l.115,301), Intriguingly (l.344), unambiguously (l.347), etc. The use of these words is generally counter-productive. The authors should scan the ms. to eliminate them as far as possible. The sentences would read more clearly and become more impactful.

Following reviewer’s recommendation, we have now eliminated most of the adverbs, mostly used at the beginning of sentences, in the revised manuscript.

Specific comments

(1) L.1: "maintenance of homeostasis" or increasing cAMP level.

As suggested by the reviewer, we have now replaced “maintenance of cAMP homeostasis” with “maintenance of cAMP level”.

(2) L.27: mechanism or reason; varying or various.

As recommended by the reviewer, we have now replaced “mechanism” with “reason” and the word “varying” is deleted while incorporating suggested changes in the abstract.

(3) L.28-29: The logic of connecting PhoP to cAMP doesn't follow well. The logic is much better in l.54, l.112-5 and l.130.

We thank the reviewer for this suggestion. We have now modified the statement within the ‘abstract’ in the revised manuscript (duplicated below):

“cAMP is one of the most widely used second messengers which impacts on a wide range of cellular responses in microbial pathogens including M. tuberculosis. Herein, we hypothesized that intra-mycobacterial cAMP level could be controlled by the phoP locus since the major regulator plays a key role in bacterial response against numerous stress conditions.”

(4) L.30: discovers or reveals (?). Also, in l.101.

As recommended by the reviewer, we have now replaced ‘discovers’ with ‘reveals’ in the Abstract and ‘uncovered’ with ‘revealed’ in the Introduction section of the manuscript.

(5) L.31: Delete "The most - - derived". It is not obvious what most fundamental means here. I suggest: We find that PhoP-dependent ---involves specific binding of the regulator---PDE gene.

As recommended by the reviewer, we have modified the statement (duplicated below): “In keeping with these results, we find specific recruitment of the regulator within the promoter region of rv0805 PDE, and absence of phoP or ectopic expression of rv0805 independently accounts for elevated PDE synthesis leading to depletion of intra-mycobacterial cAMP level.”

(6) L.36: --pathway decreases cAMP level, stress tolerance, and survival of the bacilli.

As recommended by the reviewer, we have now modified the statement (duplicated below): “Thus, genetic manipulation to inactivate PhoP-Rv0805-cAMP pathway decreases cAMP level, stress tolerance, and intracellular survival of the bacilli.

(7) L.41: 'keeps encountering" or encounters?

As suggested by the reviewer, we have replaced ‘keeps encountering’ with ‘encounters’ in the ‘Introduction’ section of the revised manuscript.

(8) L.61: responds, carries.

Our apologies for the embarrassing grammatical mistakes. We have rectified these errors in the revised manuscript.

(9) L.67: you mean burst in synthesis level, not burst of cAMP itself.

To improve clarity, we have now modified the statement in the revised manuscript (duplicated below): “Agarwal and colleagues had shown that burst in synthesis of bacterial cAMP upon infection of macrophages, improved bacterial survival by interfering with host signalling pathways (Agarwal et al., 2009)”

Reference

Agarwal N, Lamichhane G, Gupta R, Nolan S, Bishai WR (2009) Cyclic AMP intoxication of macrophages by a Mycobacterium tuberculosis adenylate cyclase. Nature 460: 98-102

(10) L.77: Change Off to Of.

We are sorry for the inaccuracy. The suggested change has been made to the text.

(11) L.83: Did not discuss "degradation" earlier.

Following reviewer’s recommendation, we have now modified the statement in the revised manuscript (duplicated below).

“Together, these results strongly suggest that a balance between cAMP synthesis by adenylate cyclases and cAMP degradation by phosphodiesterases contributes to rapid adaptive response of mycobacteria in a hostile intracellular environment (Johnson and McDonough, 2018; McDonough and Rodriguez, 2011).”

Reference

Johnson RM, McDonough KA (2018) Cyclic nucleotide signaling in Mycobacterium tuberculosis: an expanding repertoire. Pathog Dis 76 (5)

McDonough KA, Rodriguez A (2011) The myriad roles of cyclic AMP in microbial pathogens: from signal to sword. Nature reviews Microbiology 10: 27-38

(12) L.95: Isn't PhoPR a two-component signal transduction system, the terminology that is more specific than a two-protein regulatory system?

As recommended by the reviewer, we have replaced “two protein regulatory system” with more specific “two-component signal transduction system” in the revised manuscript.

(13) L.124: check-point prevents things from happening. Here the mechanism you found allows growth and survival.

We agree. As recommended by the reviewer, we have now modified the sentence in the revised manuscript (duplicated below).

“Together, the newly identified mechanism of regulation of cAMP level allows intraphagosomal survival and growth program of mycobacteria.”

(14) L.132: why not say directly-"---under normal, and NO and acid stress conditions (Fig. 1A).

As recommended by the reviewer, we have now deleted the first part of the sentence and directly stated that “we compared cAMP levels………. under normal, NO and acidic stress conditions” (duplicated below).

“We compared cAMP levels of WT and phoPR-KO (lacking both phoP and phoR), grown under normal, NO stress and acid stress conditions (Fig. 1A).”

(15) L.134: The complementation is quite variable. Also true in Fig. 2A. If no simple answer, you can say- cAMP values increased in complemented cells, although to a variable extent, for reasons unknown.

We agree with the reviewer. We have now incorporated new text in the ‘Results’ section of the revised manuscript (duplicated below):

“A higher cAMP level in the complemented strain under NO stress is possibly attributable to reproducibly higher phoP expression in the complemented mutant under specific stress conditions (Khan et al., 2022).”

(16) L.154: You rather not say "conclude" and "most likely" at the same time. How about replacing "we conclude" with suggests? In that case, no need to say "most likely". Also, in l.306-7 & l.322-3.

We thank the reviewer for these suggestions. We have now modified the statements in the revised manuscript (duplicated below).

“We suggest that lower cAMP level of the mutant is not due to its higher efficacy of cAMP secretion.”

Following reviewer’s recommendation, we have incorporated similar changes in two other places of the ‘Results’ section of the revised manuscript.

(17) L.161: introduce both the acronyms here and not in l.162.

Following reviewer’s recommendation, we have made the suggested changes.

(18) L.164: Second, (to be in line with First).

We have made the suggested change.

(19). Fig. 2C: There are no black and white bars. This is an important figure because the results appear in the abstract. The signal change from pH 7 to 4.5 is not much. An independent approach would have been desirable. If it were E. coli, I would have suggested beta-gal assay or in vivo footprints. Is a PhoP binding site recognizable in the promoter region of rv0805?

We apologize for the inaccuracy. We have corrected it in the revised manuscript. Also, we have now carried out DNA binding assays, and included the EMSA data of rv0805 upstream regulatory region binding to phosphorylated PhoP (P~PhoP) as a supplemental figure (Figure 2-figure supplement 1A-B). In this figure, we have also incorporated our results on the likely PhoP binding site within rv0805up. The new figure, figure caption and the relevant results have been adjusted accordingly in the revised manuscript.

(20) L.209: ORFs; also delete "of growth" from the sentence.

The suggested changes were made to the text.

(21) L.213: Delete Importantly and change "failed to" to 'did not' (since you did not motivate the expectation earlier, it is better to state the results in an unbiased way).

As recommended by the reviewer, both changes were included in the revised manuscript.

(22) L.217: The requirement of PhoR is a new result - why say "confirm". Change it to indicate. Also, delete "indeed" here and from L.233.

As recommended by the reviewer, both changes were included in the revised manuscript.

(23) L.224: Are the results in Fig 3-S1A under inducing conditions?

The results shown in Fig 3-S1A are not under inducing conditions of expression. For better clarity, we have modified the sentence describing Figure 3-figure supplement 1A (duplicated below).

“rv0805 ORF was cloned within the multicloning site of integrative pSTki (Parikh et al., 2013) between EcoRI and HindIII sites under the control of Pmyc1tetO promoter, and expression of rv0805 under non-inducing condition was verified by determining the mRNA level (Figure 3 - figure supplement 1A).

Reference:

Parikh et al (2013) Development of a new generation of vectors for gene expression, gene replacement, and protein-protein interaction studies in mycobacteria. Applied and environmental microbiology 79: 1718-1729

(24) L.225: ---cAMP level. Add (Fig. 3C) at the end of the next sentence.

As recommended by the reviewer, both the suggested changes were made to the revised text.

(25) L.231: Delete "Most importantly"- you didn't specify what are other less important results.

We agree. We have now deleted “most importantly” from the sentence in the revised text.

(26) L.243 & 254: Change homeostasis to level? Here you are showing mechanisms that can change cAMP level. Homeostasis here would mean how fluctuations in cAMP level are adjusted, usually requiring negative feedback.

As recommended by the reviewer, ‘homeostasis’ was replaced with ‘level’ in both places.

(27) L.256: stress response or stress? Also, in l.272

We are sorry for the inaccuracy. We have corrected these errors in the revised version of the manuscript.

(28) L.259: Change "maintenance of homeostasis" to 'repressing the rv0805 PDE gene'. It is safer to use a fact-based title. In this section, direct measurement of rv0805 mRNA, and/or cAMP levels in different genetic backgrounds seem desirable.

We agree. As recommended by the reviewer, we have modified the title of the ‘Results’ section in the revised manuscript (duplicated below).

“PhoP contributes to mycobacterial stress tolerance and intracellular survival by repressing the rv0805 PDE expression.”

Please note that direct measurements of rv0805 mRNA and cAMP levels are part of Fig. 3 and Figure 3- figure supplement 1A, respectively.

(29) Fig, 4A: White and grey symbols are not easily discriminated without zooming. Use color for phoPR-KO.

We agree. We have now indicated the phoPR-KO in blue in the revised Fig. 4.

(30) L.264: Delete remarkable or explain what is so remarkable. Aren't the results expected- the PDE level would go up in both cases. Direct measurement of PDE /cAMP levels would take the mystery out of the results.

As recommended by the reviewer, we have deleted ‘remarkably’ in the revised text. We have measured cAMP and PDE expression levels of the four strains in Fig. 3 and Figure 3-figure supplement 1.

(31) L.273: --suggesting a role of ---

We have modified this sentence in the revised version of the manuscript (duplicated below).

“A previous study had reported that phoP-deleted mutant strain was more sensitive to Cumene Hydrogen Peroxide (CHP), suggesting a role of PhoP in regulating mycobacterial stress response to oxidative stress (Walters et al., 2006).”

Reference:

Walters et al. (2006) The Mycobacterium tuberculosis PhoPR two-component system regulates genes essential for virulence and complex lipid biosynthesis. Mol Microbiol 60: 312-330

(32) L.275: Delete "transcriptome". CHP sensitivity alone doesn't speak for transcriptome.

As suggested by the reviewer, we have deleted “transcriptome”. Also, please see our response to the previous comment (above).

(33) Fig. 4D and E: % Colocalization in the Merge panels is not much different among the four strains tested (to an untrained eye). Can the results be explained to readers not used to in vivo studies?

As recommended by the reviewer, we have now incorporated new text to explain the in vivo experiment (duplicated below).

“In this assay, WT-H37Rv inhibits phagosome maturation, whereas phagosomes with phoPR-KO mature into phagolysosomes (Anil Kumar et al., 2016).”

Further, for better clarity of the results shown in Fig. 4D, we have (a) increased size of the figure to highlight the difference in the ‘merge’ panel; (b) included “white arrowheads” in the merge panels of Fig. 4D to indicate auramine labeled mycobacteria, which either have inhibited or facilitated trafficking into lysosomes, and finally (c) incorporated method used to calculate percent co-localization in greater details in the ‘Material and Methods’ section of the revised manuscript.

Reference

Anil Kumar et al. (2016) EspR-dependent ESAT-6 secretion of Mycobacterium tuberculosis requires the presence of virulence regulator PhoP. J Biol Chem. 291, 19018-19030

(34) L.275-6: Delete "next" (also in l.347) and "Note that". In this paragraph, I was expecting some explanation on how phoPR-KO and WT-Rv0805 are behaving similarly. Even if the reason is not known, it should be mentioned.

The suggested changes have been made to the text. Also, as recommended by the reviewer, we have included the following text in the revised manuscript (duplicated below):

“Together, these results reveal similar behaviour of phoPR-KO, and WT-Rv0805 by demonstrating a comparably higher susceptibility of these strains to acidic pH and oxidative stress relative to WT bacteria and indicate a link between intra-mycobacterial cAMP level and bacterial stress response. Collectively, these data suggest that at least one of the mechanisms by which PhoP contributes to global stress response is attributable to maintenance of cAMP level.”

(35) L.281: ---WT and indicate a link between cAMP level and stress response in mycobacteria. (No mention of homeostasis).

The suggested change has been made to the revised text. Please see above our response to point # 34.

(36) L.288, 290: No Thus and no clearly.

Both the suggested changes have been made to the text.

(37) L.297: Can you be more direct and state --is due to reduced cAMP level?

As recommended by the reviewer, we have now modified the sentence to make it more direct in the revised manuscript (duplicated below):

“Together, our findings facilitate an integrated view of our results, suggesting that higher susceptibility of WT-Rv0805 to stress conditions, is attributable to its reduced cAMP level.”

(38) L.307: May delete "most likely----homeostasis". cAMP is not discussed here. The same deletion is desired in l.324.

We agree. As recommended by the reviewer, we have now modified the relevant texts in the revised manuscript. These are duplicated below.

“From these results, we suggest that ectopic expression of rv0805 impacts phagosome maturation arguing in favour of a role of PhoP in influencing phagosome-lysosome fusion in macrophages.”

“Thus, we suggest that one of the reasons which accounts for an attenuated phenotype of phoPR-KO in both cellular and animal models is attributable to PhoP-dependent repression of rv0805 PDE activity, which controls mycobacterial cAMP level.”

(39) L.342: cAMP level is regulated remains---

The suggested change has been made to the revised text (duplicated below):

“Although many bacterial pathogens modulate host cell cAMP level as a common strategy, the mechanism of regulation of mycobacterial cAMP level remains unknown.”

(40) L.373: tone down "most fundamental". It is not obvious what is so profound about a stress-response system that depends on PhoP also depends on PhoR. OR justify what is most fundamental about it.

We agree. Following reviewer’s recommendation, we have modified the text in the revised manuscript (duplicated below):

“In keeping with these results, we find that PhoP-dependent rv0805 expression requires PhoR (Figs. 3A-B), the cognate kinase which activates PhoP in a signal-dependent manner (Gupta et al., 2006; Singh et al., 2023).”

References:

Gupta et al. (2006) Transcriptional autoregulation by Mycobacterium tuberculosis PhoP involves recognition of novel direct repeat sequences in the regulatory region of the promoter. FEBS Letters 580, 5328-5338.

Singh et al. (2023) Dual functioning by the PhoR sensor is a key determinant to Mycobacterium tuberculosis virulence. PLoS Genetics 19(12): e1011070.

(41) L.395: delete correspondingly (?)

The suggested change has been made to the text.

(42) L.396: Delete "appear to" and "somewhat". The uncertainty is already implied in "suggest". The evidence that ectopic expression of rv0805 is functionally equivalent to phoP deletion is quite clear in this paper and not saying that clearly is confusing.

We agree with the reviewer. The suggested changes have been made to the revised text (duplicated below):

“Thus, our results suggest that ectopic expression of rv0805 is functionally equivalent to deletion of the phoP locus.”

(43) L.401: --over-expressing bacilli, induction level of rv0805 expression was significantly different in Matange et al and our studies. The next sentence is also very wordy.

We have made changes to the text to address the reviewer’s concern. Also, the next sentence has been rewritten (duplicated below).

“Although both studies were performed with rv0805 over-expressing bacilli, the fact that important differences in the expression of PDEs, in this study (Matange et al., 2013) and in our assays - yielding significantly different levels of rv0805 expression - most likely account for this discrepancy. While we cannot rule out the possibility of cleavage of other cyclic nucleotides by Rv0805 (Keppetipola & Shuman, 2008; Shenoy et al., 2007; Shenoy et al., 2005), consistent with a previous study our results correlate rv0805 expression with intra-mycobacterial cAMP level (Agarwal et al., 2009).”

References:

Matange et al. (2013) Overexpression of the Rv0805 phosphodiesterase elicits a cAMP-independent transcriptional response. Tuberculosis (Edinb) 93: 492-500.

Keppetipola N, Shuman S (2008) A phosphate-binding histidine of binuclear metallophosphodiesterase enzymes is a determinant of 2',3'-cyclic nucleotide phosphodiesterase activity. J Biol Chem 283: 30942-30949

Shenoy et al. (2007) Structural and biochemical analysis of the Rv0805 cyclic nucleotide phosphodiesterase from Mycobacterium tuberculosis. Journal of molecular biology 365: 211-225

Shenoy et al. (2005) The Rv0805 gene from Mycobacterium tuberculosis encodes a 3',5'-cyclic nucleotide phosphodiesterase: biochemical and mutational analysis. Biochemistry 44: 15695-15704

Agarwal N, Lamichhane G, Gupta R, Nolan S, Bishai WR (2009) Cyclic AMP intoxication of macrophages by a Mycobacterium tuberculosis adenylate cyclase. Nature 460: 98-102

(44) L.409: To avoid saying "conclude" and "most likely" at the same time, can you start the sentence thus: 'We infer that Pho-----rv0805 is a---.

We agree. We have made suggested changes to the text. The modified sentence is duplicated below:

“We infer that PhoP-dependent regulation of Rv0805 is a critical regulator of intra-mycobacterial cAMP level.”

(45) L.424. Delete "According to this model". In the preceding sentence, the subject is results, not model. This whole paragraph needs to be rewritten in fewer lines. The shorter the summary statement, the greater would be its impact (less is more here). I would delete the red circles from the figure- it appears that in the repressed state, you are making more products. Replace the circles with an arrow. The legend could be "Increased cAMP level and effective stress response" and "Decreased cAMP---and reduced---.

We thank the reviewer for these suggestions. Following reviewer’s recommendations, we have made numerous changes and rewritten the paragraph in the revised manuscript (duplicated below):

“In summary, upon sensing low acidic pH as a signal PhoR activates PhoP, P~PhoP binds to rv0805 upstream regulatory region and functions as a specific repressor of Rv0805. Therefore, we observed (a) a reproducibly lower level of cAMP in phoPR-KO relative to WT-H37Rv, (b) a significantly reduced expression of rv0805 in WT-H37Rv, grown under acidic pH relative to normal conditions, and (c) comparable cAMP levels in phoPR-KO and WT-Rv0805. This is why the two strains remain ineffective to mount an appropriate stress response, most likely due to their inability to coordinate regulation of gene expression because of dysregulation of intra-mycobacterial cAMP level. However, without uncoupling regulatory control of PhoPR and rv0805 expression, we cannot confirm that dysregulation of cAMP level accounts for virulence attenuation of phoPR-KO. Given the fact that rv0805-depleted M. tuberculosis is growth attenuated in vivo (McDowell et al., 2023), paradoxically ectopic expression of rv0805 leads to dysregulated metabolic adaptation, thereby resulting in reduced stress tolerance and intracellular survival.”

Also, the suggested changes have been incorporated in Fig. 6 and the figure caption.

Reference

McDowell JR, Bai G, Lasek-Nesselquist E, Eisele LE, Wu Y, Hurteau G, Johnson R, Bai Y, Chen Y, Chan J et al (2023) Mycobacterial phosphodiesterase Rv0805 is a virulence determinant and its cyclic nucleotide hydrolytic activity is required for propionate detoxification. Mol Microbiol 119: 401-422

(46) L.458 & 500: ---was used to transform.

Following reviewer’s recommendation, the suggested changes were made to the text in the Materials and Methods section of the revised manuscript.

(47) L.460: --- antibiotics plates.

Both suggested changes were made to the text.

(48) L.466-7: --they were transferred-pH 4.5) and grown for further-

We thank the reviewer for these suggestions. The suggested changes were made to the text.

(49) L.486: ---full-length ORFs of interest were---

The suggested changes were incorporated in the revised manuscript.

(50) L.497: The RNAs were 20 nt long and complementary---

As recommended by the reviewer, we have modified the text in the revised manuscript (duplicated below).

“The RNAs were 20 nt long and complementary to the non-template strand of the target gene.”

Reviewer #2:

(1) Rephrase this sentence in the abstract: “Because growing evidence connects PhoP with varying stress response, we hypothesized that the level of 3’,5’ cAMP, one of the most widely used second messengers, was regulated by the phoP locus, linking numerous stress responses with cAMP production”.

As recommended by the reviewer, we have now rewritten the sentence. The modified text is incorporated in the revised manuscript (duplicated below):

“cAMP is one of the most widely used second messengers, which impacts on a wide range of cellular responses in microbial pathogens including M. tuberculosis. Herein, we hypothesized that intra-mycobacterial cAMP level could be controlled by the phoP locus since the major regulator plays a key role in bacterial responses against numerous stress conditions.”

Also, please see our response to specific comments #1-3 of Reviewer 1.

(2) Line 134: please describe the complementation strain features as it is mentioned for the first time (plasmid, copy number, promoter etc.) in the manuscript. Especially under NO stress what could be the authors' justification regarding the high cAMP concentration in the complementation strain?

As recommended by the reviewer, the details of construction of the complemented strain have been incorporated in the ‘Materials and Methods’ section of the revised manuscript (duplicated below):

“To complement phoPR expression, pSM607 containing a 3.6- kb DNA fragment of M. tuberculosis phoPR including 200-bp phoP promoter region, a hygromycin resistance cassette, attP site and the gene encoding phage L5 integrase, as detailed earlier (Walters et al., 2006) was used to transform phoPR mutant to integrate at the L5 attB site.”

To address the reviewer’s other concern, we have now included the following sentence in the ‘Results’ section of the revised manuscript (duplicated below):

“A higher cAMP level in the complemented strain under NO stress is possibly attributable to reproducibly higher phoP expression in the complemented mutant under specific stress condition (Khan et al., 2022).”

Reference:

Khan et al. (2022) Convergence of two global regulators to coordinate expression of essential virulence determinants of Mycobacterium tuberculosis. eLife 2022, 11:e80965.

(3) In Figure 1C, it is a bit confusing to see the numbers 1,2,3 and 4 and nothing is referred to these numbers in the figure legend so it's better to remove them.

We agree with the reviewer. We have now removed the lane numbers from the figure (Fig. 1C) in the revised manuscript.

(4) Line 852: rephrase it "insignificantly different".

The suggested change has been made to the text. The modified text is incorporated in the manuscript (duplicated below):

“Note that the difference in expression levels of rv0805 between WT and phoPR-KO was significant (p<0.01), whereas the fold difference in mRNA level between WT and the complemented mutant (Compl.) remains nonsignificant (not indicated).”

(5) Line198-200: There are no open/black bars, they all are coloured bars. Correct the same. The significance test should be done for the same gene (suppose rv0805 up) in different pH conditions. Right now, it is not revealing anything and misleading.

We apologize for the inaccuracy. We have now rectified the error. As recommended by the reviewer, Fig. 4C was modified, and the significance tests were carried out between samples involving identical promoter enrichments under different pH conditions. The modified figure, figure legend, and the relevant results have been adjusted accordingly in the revised manuscript.

(6) Line 213: Is there any difference between this complementation strain (phoPR-KO:: phoPphoR with the one used in Figure 1A, 1B, and 2A? If yes, then please describe it.

The same complemented mutant strain, which has been described in the ‘Materials and Methods’ section of the revised manuscript, was used in the experiments described in Fig. 1A, Fig.1B and Fig. 2A.

(7) Line 223: Please mention the copy number and promoter of the vector construct.

As recommended by the reviewer, we have now mentioned the promoter of the vector and incorporated new text with regard to copy number of the expression vector in the revised manuscript (duplicated below).

“Although copy number of episomal vectors with pAl5000 origin of replication (oriM) have been reported to be 3 by Southern hybridization (Ranes et al, 1990), in this case wild-type and mutant Rv0805 proteins were expressed from single-copy chromosomal integrants (Parikh et al., 2013).”

References

Ranes et al., (1990) Functional analysis of pAL5000, a plasmid from Mycobacterium fortuitum: construction of a "mini" mycobacterium-Escherichia coli shuttle vector. J Bacteriol 172: 2793-2797

Parikh et al., (2013) Development of a new generation of vectors for gene expression, gene replacement, and protein-protein interaction studies in mycobacteria. Applied and environmental microbiology 79: 1718-1729

(8) Figure 3 - Figure Supplement 1: not sure why the authors measured mRNA levels of rv1357 and rv2387? These genes were not overexpressed!

The mRNA levels of rv1357 and rv2387 were measured to show that overexpression of either the wild-type or mutant Rv0805 did not influence expression of other PDEs like Rv1357 and Rv2387. We have now mentioned it explicitly in the revised manuscript (duplicated below).

“In contrast, other PDE encoding genes (rv1357 and rv2387), under identical conditions, demonstrate comparable expression levels in WT-H37Rv and rv0805 over-expressing strains.”

(9) Line 234: Wrong interpretation it should be PDE mRNA levels in WT-Rv0805 and WT-Rv0805M.

As recommended by the reviewer, we have now modified the statement to improve clarity (duplicated below).

“The corresponding mRNA levels of PDEs (wild-type and the mutant) are over-expressed approximately 4.5-6 -fold relative to the genomic rv0805 level of WT-H37Rv (Figure 3-figure supplement 1A).”

(10) Line 237: Remove the sentence "Thus, we conclude......identical expression strategy", you have already talked about why phosphodiesterase activity is crucial for cAMP concentration and it is well understood.

Following reviewer’s recommendation, we have now removed the sentence from the revised manuscript.

(11) Figure 3E: Authors should comment on why the cAMP concentration is not significantly changed even though the mRNA level changes are drastic (~90%). How do you correlate that? Is it because of other PDEs?

We agree. As suggested by the reviewer, we have now incorporated new text in the revised manuscript (duplicated below).

“We speculate that effective knocking down of phoP or rv0805 is not truly reflected in the extent of variation of cAMP levels possibly due to the presence of numerous other mycobacterial PDEs.”

(12) Line 505,506: Is it the translation start site or the transcription start site? Because mRNA level changes are reported.

It is the translational start sites, and gene-specific small guide RNAs were designed to inhibit mRNA expression.

(13) Line 292: There is a difference between red and green bars. Authors should do statistical analysis and then comment on whether overexpression of WT and mutant pde are different or similar, to me they are different; also, explain why the WT-Rv0805 strain is different than the phoPR-KO strain in the context of cell wall metabolism.

As recommended by the reviewer, we have now included statistical significance of the data in the revised version, and modified the text accordingly in the manuscript.

Also, we included text explaining why WT-Rv0805 is different compared to phoPR-KO strain in the context of cell wall metabolism (duplicated below).

“Together, these results suggest that both strains expressing wild type or mutant PDEs share a largely similar cell-wall properties and are consistent with (a) a recent study reporting no significant effect of cAMP dysregulation on mycobacterial cell wall structure/permeability (Wong et al., 2023), and (b) role of PhoP in cell wall composition and complex lipid biosynthesis (Walters et al., 2006; Asensio et al., 2006; Goyal et al., 2011).”

References:

Wong et al. (2023) Cyclic AMP is a critical mediator of intrinsic drug resistance and fatty acid metabolism in M. tuberculosis. eLife 2023; 12: e81177

Walters et al. (2006) The Mycobacterium tuberculosis PhoPR two-component system regulates genes essential for virulence and complex lipid biosynthesis. Mol Microbiol 60: 312-330

Asensio et al. (2006) The Virulence-associated Two-component PhoP-PhoR System Controls the Biosynthesis of Polyketide-derived Lipids in Mycobacterium tuberculosis. J Biol Chem 281: 1313-1316.

Goyal et al. (2011) Phosphorylation of PhoP protein plays direct regulatory role in lipid biosynthesis of Mycobacterium tuberculosis. J Biol Chem 286: 45197-45208

(14) Line 299-303: Authors should explain how the colocalization % are calculated. Also, in the figure 4D merge panel please highlight the difference.

As suggested by the reviewer, we have now explained the methodology used to calculate percent colocalization in greater details. Also, we have modified Figure 4D to highlight the difference between samples shown in merge panel. Please see our response to comment # 33 from the Reviewer 1.

(15) General comment: There are multiple instances where writing needs to be improved.

We are sorry for the inaccuracies. We have now done thorough editing of the manuscript and made numerous corrections throughout.

Author Response

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

Public Reviews:

Reviewer #1 (Public Review):

Weaknesses:

The weaknesses are the brevity of the simulations, the concomitant lack of scope of the simulations, the lack of depth in the analysis, and the incomplete relation to other relevant work.

A 1 µs simulation of CCh (Video 1, part 2) shows that m3 (ACHA) is stable, throughout. The DG comparisons, in silico versus in vitro, indicate that 200 ns simulations are sufficient to identify LA versus HA conformational populations. Figure 6-table supplement 1 shows distances. New citations have been added.

Reviewer #2 (Public Review):

Weaknesses:

After carrying out all-atom molecular dynamics, the authors revert to a model of binding using continuum Poisson-Boltzmann, surface area, and vibrational entropy. The motivations for and limitations associated with this approximate model for the thermodynamics of binding, rather than using modern atomistic MD free energy methods (that would fully incorporate configurational sampling of the protein, ligand, and solvent) could be provided. Despite this, the authors report a correlation between their free energy estimates and those inferred from the experiment. This did, however, reveal shortcomings for two of the agonists. The authors mention their trouble getting correlation to experiment for Ebt and Ebx and refer to up to 130% errors in free energy. But this is far worse than a simple proportional error, because -24 Vs -10 kcal/mol is a massive overestimation of free energy, as would be evident if the authors were to instead express results in terms of KD values (which would have an error exceeding a billion fold). The MD analysis could be improved with better measures of convergence, as well as a more careful discussion of free energy maps as a function of identified principal components, as described below. Overall, however, the study has provided useful observations and interpretations of agonist binding that will help understand pentameric ligand-gated ion channel activation.

The objective of the calculations was to identify structural populations, not to estimate binding free energies. We knew the actual LA and HA energies (for all 4 agonists) from real-world electrophysiology experiments. We conclude that the simple PBSA method worked as a tool for identification because the calculated efficiencies match those from experiments (Figure 4B, Figure 4-Source Data 1). We discuss the mismatches in absolute G in the Results and Discussion. Methods for estimating experimental binding free energies are described in a cited, eLife companion paper. The G ratio relates to agonist efficiency.

Main points:

Regarding the choice of model, some further justification of the reduced 2 subunit ECD-only model could be given. On page 5 the authors argue that, because binding free energies are independent of energy changes outside the binding pocket, they could remove the TMD and study only an ECD subunit dimer. While the assumption of distant interactions being small seems somewhat reasonable, provided conformational changes are limited and localised, how do we know the packing of TMD onto the ECD does not alter the ability of the alpha-delta interface to rearrange during weak or strong binding? They further write that "fluctuations observed at the base of the ECD were anticipated because the TMD that offers stability here was absent.". As the TMD-ECD interface is the "gating interface" that is reshaped by agonist binding, surely the TMD-ECD interface structure must affect binding. It seems a little dangerous to completely separate the agonist binding and gating infrastructure, based on some assumption of independence. Given the model was only the alpha and delta subunits and not the pentamer with TMD, I am surprised such a model was stable without some heavy restraints. The authors state that "as a further control we carried out MD simulation of a pentamer docked with ACh and found similar structural changes at the binding pocket compared to the dimer." Is this sufficient proof of the accuracy of the simplified model? How similar was the model itself with and without agonist in terms of overall RMSD and RMSD for the subunit interface and the agonist binding site, as well as the free energy of binding to each model to compare?

The statement that distant interactions are small is not an "assumption", but rather a conclusion based on data. Mutant cycle analysis of 83 pairs shows (with a few exceptions) non-additivity of free energy change prevails only with separations <~15 A (Fig.3 in Gupta et al 2017). Regardless, the adequacy of dimers and convergence by 200 ns are supported by the calculated and experimental agonist efficiencies match (Figure 4B) and the 1 ms simulation (Video 1 part 2). Apo 200ns simulation of the ECD dimer is now added (Figure 2-figure supplement 2) and the dimer interface seems to be adequate (stable).

Although the authors repeatedly state that they have good convergence with their MD, I believe the analysis could be improved to convince us. On page 8 the authors write that the RMSD of the system converged in under 200 ns of MD. However, I note that the graph is of the entire ECD dimer, not a measure for the local binding site region. An additional RMSD of local binding site would be much more telling. You could have a structural isomerisation in the site and not even notice it in the existing graph. On page 9 the authors write that the RMSF in Figure S2 showed instability mainly in loops C and F around the pocket. Given this flexibility at the alpha-delta interface, this is why collecting those regions into one group for the calculation of RMSD convergence analysis would have been useful. They then state "the final MD configuration (with CCh) was well-aligned with the CCh-bound cryo-EM desensitized structure (7QL6)... further demonstrating that the simulation had converged." That may suggest a change occurred that is in common with the global minimum seen in cryo EM, which is good, but does not prove the MD has "converged". I would also rename Figure S3 accordingly.

The description is now changed to “aligns well” with desensitized structure (7QL6.PDB)”. RMSD of not just the binding pocket but the whole ECD dimer is well aligned with first apo (m1) and with desensitized state (m3).

The authors draw conclusions about the dominant states and pathways from their PCA component free energy projections that need clarification. It is important first to show data to demonstrate that the two PCA components chosen were dominant and accounted for most of the variance. Then when mapping free energy as a function of those two PCA components, to prove that those maps have sufficient convergence to be able to interpret them. Moreover, if the free energies themselves cannot be used to measure state stability (as seems to be the case), that the limitations are carefully explained. First, was PCA done on all MD trajectories combined to find a common PC1 & PC2, or were they done separately on each simulation? If so, how similar are they? The authors write "the first two principal components (PC-1 and PC-2) that capture the most pronounced C. displacements". How much of the total variance did these two components capture? The authors write the changes mostly concern loop C and loop F, but which data proves this? e.g. A plot of PC1 and PC2 over residue number might help.

The PCA analyses have been enriched. Figure 3-Source Data 1. shows the dominance of PC1 and PC2. Because the binding energy match was sufficient to identify affinity states, we did not explore additional PCs. Residue-wise PC1 and PC2 analysis and comparison with RMSF are in Figure 2-figure supplement 2. PC1 and PC2 both correlate with fluctuations in loops C and F. Overlap analysis in different runs is shown in Figure 3-figure supplement 1. Lower variance in a particular region of the PCA landscape indicates that the system frequently visits these states, suggesting stability (a preference for these conformations).

The authors map the -kTln rho as a free energy for each simulation as a function of PC1 & PC2. It is important to reveal how well that PC1-2 space was sampled, and how those maps converged over time. The shapes of the maps and the relative depths of the wells look very different for each agonist. If the maps were sampled well and converged, the free energies themselves would tell us the stabilities of each state. Instead, the authors do not even mention this and instead talk about "variance" being the indicator of stability, stating that m3 is most stable in all cases. While I can believe 200ns could not converge a PC1-2 map and that meaningful delta G values might not be obtained from them, the issue of lack of sampling must be dealt with. On page 12 they write "Although the bottom of the well for 3 energy minima from PCA represent the most stable overall conformation of the protein, they do not convey direct information regarding agonist stability or orientation". The reasons why not must be explained; as they should do just that if the two order parameters PC1 and PC2 captured the slowest degrees of freedom for binding and sampling was sufficient. The authors write that "For all agonists and trajectories, m3 had the least variance (was most stable), again supporting convergence by 200 ns." Again the issue of actual free energy values in the maps needs to be dealt with. The probabilities expressed as -kTln rho in kcal/mol might suggest that m2 is the most stable. Instead, the authors base stability only on variance (I guess breadth of the well?), where m3 may be more localised in the chosen PC space, despite apparently having less preference during the MD (not the lowest free energy in the maps).

The motivations and justifications for the use of approximate PBSA energetics instead of atomistic MD free energies should be dealt with in the manuscript, with limitations more clearly discussed. Rather than using modern all-atom MD free energy methods for relative or absolute binding free energies, the author selects clusters from their identified states and does Poisson-Boltzmann estimates (electrostatic, vdW, surface area, vibrational entropy). I do believe the following sentence does not begin to deal with the limitations of that method: "there are limitations with regard to MM-PBSA accurately predicting absolute binding free energies (Genheden & Ryde, 2015; Hou et al., 2011) that depends on the parameterization of the ligand (Oostenbrink et al., 2004)." What are the assumptions and limitations in taking continuum electrostatics (presumably with parameters for dielectric constants and their assignments to regions after discarding solvent), surface area (with its assumptions and limitations), and of course assuming vibration of a normal mode can capture entropy. On page 30, regarding their vibrational entropy estimate, they write that the "entropy term provides insights into the disorder within the system, as well as how this disorder changes during the binding process". It is important that the extent of disorder captured by the vibrational estimate be discussed, as it is not obvious that it has captured entropy involving multiple minima on the system's true 3N-dimensional energy surface, and especially the contribution from solvent disorder in bound Vs dissociated states.

As discussed above, errors in the free energy estimates need to be more faithfully represented, as fractional errors are not meaningful. On page 21 the authors write "The match improved when free energy ratios rather than absolute values were compared." But a ratio of free energies is not a typical or expected measure of error in delta G. They also write "For ACh and CCh, there is good agreement between.Gm1 and GLA and between.Gm3 and GHA. For these agonists, in silico values overestimated experimental ones only by ~8% and ~25%. The agreement was not as good for the other 2 agonists, as calculated values overestimated experimental ones by ~45%(Ebt) and ~130% (Ebt). However, the fractional overestimation was approximately the same for GLA and GHA." See the above comment on how this may misrepresent the error. On page 21 they write, in relation to their large fractional errors, that they "do not know the origin of this factor but speculate that it could be caused by errors in ligand parameterization". However the estimates from the PBSA approach are, by design, only approximate. Both errors in parameterisation (and their likely origin) and the approximate model used, need discussion.

Again, the goal of calculating binding free energy was to identify structural correspondence to LA and HA and not to obtain absolute binding free energy values. Along with the least variance (distribution) for the principle component for m3, it also had the highest binding free energy. An association of m1 to LA and m3 to HA was done after comparing them to experimental values (efficiencies). This comparison not only validates our approach but also underscores the utility of PBSA in supplementing MD and PCA analyses with broader energetics perspectives.

Reviewer #3 (Public Review):

Weaknesses:

Although the match in simulated vs experimental energies for two ligands was very good, the calculated energies for two other ligands were significantly different than the experiment. It is unclear to what extent the choice of method for the energy calculations influenced the results. See above.

A control simulation, such as for an apo site, is lacking. Figure 2-figure supplement 2. shows the results of 200 ns MD simulations of the apo structure (n=2).

Reviewer #4 (Public Review):

Weaknesses:

Timescales (200 ns) do not capture global rearrangements of the extracellular domain, let alone gating transitions of the channel pore, though this work may provide a launching point for more extended simulations. A more general concern is the reproducibility of the simulations, and how representative states are defined. It is not clear whether replicates were included in principal component analysis or subsequent binding energy calculations, nor how simulation intervals were associated with specific states.

We are interested eventually in using MD to study the full isomerization, but these investigations are for the future and likely will involve full length pentamers and longer timescales. However, in response to this query we have in the Discussion raised this issue and offer speculations. See above, PCA has be compared between replicates (Figure 3-figure supplement 1).

Structural analysis largely focuses on snapshots, with limited direct evidence of consistency across replicates or clusters. Figure legends and tables could be clarified.

Snapshots and distance measurements (Figure 6-table supplement 1) were extracted from m1, m2 and m3 plateau regions of trajectories. Incorporated in the legend.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

This study gives interesting insights into the possible dynamics of ligand binding in ACh receptors and establishes some prerequisites for necessary and urgent further work. The broad interest in this receptor class means this work will have some reach.

Suggestions:

(1) I found the citation of relevant literature to be rather limited. In the following paper, the agonist glutamate was shown to bind in two different orientations, and also to convert. These are much longer simulations than what is presented here (nearly 50 µs), which allowed a richer view of conformational changes and ligand binding dynamics in the AMPA Receptor. Albert Lau has published similar work on NMDA, delta, and kainate receptors, including some of it in eLife. Perhaps the authors could draw some helpful comparisons with this work.

Yu A et al. (2018) Neurotransmitter Funneling Optimizes Glutamate Receptor Kinetics. Neuron

Likewise, the comparison to a similar piece of work on glycine receptors (not cited, https://pubs.acs.org/doi/10.1021/bi500815f) could be instructive. Several similar computational techniques were used, and interactions observed (in the simulations) between the agonist and the receptor were tested in the context of wet experiments. In the absence of an equivalent process in this paper (no findings were tested using an orthogonal approach, only compared against known results, from perhaps a narrow spectrum of papers), we have to view the major findings of the paper (docking in cis that leads to a ligand somersault) with some hesitancy.

The Gharpure 2019 paper is cited in the context of the delta subunit but this paper was about a3b4 neuronal nicotinic receptors. This could be tidied up. Also, the simulations from that paper could be used as an index of the stability of the HA state (if ligand orientation is being cited as transferrable, other observations could be too).

New citations have been added. It is difficult to generalize from Yu A and Yu R eta al, because in neither study was the ligand orientation associated with LA versus HA binding energy.

(2) "To start, we associated the agonist orientation in the hold end states as cis in AC-LA versus trans in AC-HA."

I think this a valid start, but one is left with the feeling that this is all we have and the validity of the starting state is not tested. What was really shown here? Is the docking reliable? What evidence can the authors summon for the ligand orientation that they use as a starting structure? In addition to docking energies, the match between PBSA and electrophysiology Gs and temporal sequence (m1-m2-m3) support the assignment.

Given that these simulations cover a circumscribed part of the binding process, I think the limitations should be acknowledged. Indeed the authors do mention a number of remaining open questions.

Paragraphs regarding 'catch' have been added to the Discussion.

(3) Results around line 90. Hypothetical structures and states that were determined from Markov analyses are discussed as if they are well understood and identified. Plausible though these are, I think the text should underline at least the source of such information. In these simulations, a further intermediate has been identified.

The model in Figure 1B was first published in 2012 and has been used and extended over the intervening years. In our lab, catch-and-hold is standard. We have published many papers (in top journals), plus reviews, regarding this scheme. We made presentations that are on Youtube. Here, at the end of the Introduction we now cite a new review article (Biophysical Journal, 2024). I am not sure what more we can do to raise awareness regarding catch and hold.

(4) The figures are dense and could be better organised. Figure 2 is key but has a muddled organization. The placement of the panel label (C) makes it look like the top row (0 ns) is part of (A). Panel B- what is shown in the oval inset (not labeled or in legend). Why not show more than one view, perhaps a sequence of time points? It is confusing to change the colour of the loops in (C). Please show the individual values in D.

Figure 2 has been redone.

(5) A lot is made of the aK145 salt bridge with aD200 and the distances - but I didn't see any measurements, or time course. This part is vague to the point of having no meaning ("bridge tightening").

We present a Table of distance measurements in the SI (Figure 6-table supplement 1).

Reviewer #2 (Recommendations For The Authors):

All main comments have been given in the above review. There are a few other minor comments below.

The 4 agonists examined were acetylcholine (ACh), carbamylcholine (CCh), epibatidine (Ebt), and epiboxidine (Ebx). Could the choices be motivated for the reader?

New in Methods: the agonists are about the same size yet represent different efficiency classes (citation to companion eLife paper). One of our (unmet) objectives was to understand the structural correlates of agonist efficiency.

The authors write that state structures generated in the MD simulation were identified by aligning free energy values with those from experiments. It would be good to explain to the reader, in the introduction, how LA and HA free energies were extracted from experiments, rather than relying on them to read older papers.

In the Introduction, we say that to get G, just measure an equilibrium constant and take the log. We think it is excessive to explain in detail in this paper how to measure the equilibrium binding constants (several methods suffice). However, we have added in Methods our basic approach: measure KLA and L2 by using electrophysiology, and compute KHA from the thermodynamic cycle using L0. We think this paper is best understood in the context of its companion, also in eLife.

In all equilibrium equations of the type A to B (e.g. on page 5), rather than using "=" signs it would be much better to use equilibrium reversible arrow symbols.

It is incorporated.

Reviewer #3 (Recommendations For The Authors):

(1) Although the match in simulated vs experimental energies for two ligands was very good, the calculated energies for Ebt and Ebx were significantly different than the experiment. Are there any alternative methods for calculating binding energies from the MD simulations that could be readily compared to?

See above. We did not use more sophisticated energy calculations because we already knew the answers. Our objective was to identify states, not to calculate energies.

(2) It would be nice to see control simulations of an apo site to ensure that the conformational changes during the MD are due to the ligands and not an artifact of the way the system is set up. I am primarily asking about this as the simulation of the isolated ECDs for the binding site interface seems like it may be unhappy without the neighboring domains that would normally surround it. On that note, was the protein constrained in any way during the MD?

Apo simulation results are presented in Figure 2-figure supplement 2. The dimer interface seems to be adequate (stable).

(3) Figure 4A-B: Should the colors for m1 and m3 be reversed?

Colors have been changed and a bar chart has been added.

Reviewer #4 (Recommendations For The Authors):

(1) Although simulations are commendably run in triplicate, it is difficult in some places to discern their consistency.

(1a) Table S1 provides important quantification of deviations in different replicates and with different agonists. Please confirm that the reported values are accurate. All values reported for the epibatidine system are identical to those reported for carbamylcholine, which seems statistically improbable. Similarly, runs 1 and 3 with epiboxidine seem identical to one another, and runs 1 and 2 with acetylcholine are nearly the same.

Figure 2-Source Data 1 has been corrected.

(1b) In reference to Figure S3, the authors comment that the simulated system (one replicate with carbamylcholine) converges within 0.5 Å RMSD of a desensitized experimental structure. This seems amazing; please specify over what atoms this deviation was calculated and with reference to what alignment. It would be interesting to know the reproducibility of this remarkable convergence in additional replicates or with other ligands; for example, Figure 5 indicates that loop C transitions to a lesser extent in the context of epibatidine than other agonists.

The comparison was for the entire dimer ECD; 0.5 Å is the result. It may be worthwhile to pursue this remarkable convergence, but not in this paper. Here, we are concerned with identifying ACLA and ACHA. Similarity between ACHA and AD structures is for a different study.

(1c) For principal-component and subsequent analyses, it appears that only one trajectory was considered for each system. Please clarify whether this is the case; if so, a rationale for the selection would be helpful, and some indication of how reproducible other replicates are expected to be.

We have added new PCA results (Results, Figure 3-figure supplement 1) that show comparable principal components in other replicates.

(2) Figure 3 shows free energy landscapes defined by principal components of fluctuation in Cα positions.

(2a) Do experimental structures (e.g. PDB IDs 6UWZ, 7QL6u) project onto any of these landscapes in informative ways?

6UWZ.pdb matches well with the apo (7QKO.pdb), comparable to m1, and 7QL6.pdb with the m3.

(2b) Please indicate the meaning of colored regions in the righthand panels.

The color panels in the top left panel indicate the colored regions in the righthand panel also, which is indicative of direction and magnitude of changes with PC1 and PC2.

(2c) Please also check the legend; do the porcupine plots really "indicate the direction and magnitude of changes between PC1 and PC2," or rather between negative and positive values of each principal component?

It indicates the direction and magnitude of changes with PC1 and PC2.

(3) It would be helpful to clarify how trajectory segments were assigned to specific minima, particularly m2 and m3.

(3a) Please verify the timeframes associated with the m2 minima, reported as "20-50 ns [with acetylcholine], 50-60 ns [with carbamylcholine], 60-100 ns [with epibatidine, and] 100-120 ns [with epiboxidine]." It seems improbable that these intervals would interleave so precisely in independent systems. Furthermore, the intervals associated with acetylcholine and epiboxidine do not appear to correspond to the m2 regions indicated in Figure S8.

Times are given in Figure 4-Source Data 1 and Figure 3-figure supplement 2. The m2 classification is based on loop displacement as well as agonist orientation. For all agonists, the selection was strictly from PCA and cluster analysis.

(3b) The text (and legend to Figure 3) indicate that 180+ ns of each trajectory was assigned to m3, which seems surprisingly consistent. However, Figure S5 indicates this minimum is more variable, appearing at 160 ns with acetylcholine but at 186 ns with carbamylcholine. Please clarify.

see above: the selection was from PCA and cluster analysis. Times are in Figure 3-figure supplement 2 and also in Figure 4-Source Data 1 (none in Fig. 3 legend).

(3c) Figures 5, 6, S6, and S7 illustrate structural features of free-energy minima in each ligand system. Please clarify what is shown, e.g. a representative snapshot, centroid, or average structure from a particular prominent cluster associated with a given minimum.

They are all representative snapshots (now in Methods). Snapshots and distance measurements (Figure 6-table supplement 1) were extracted from m1, m2 and m3 plateau regions of trajectories.

(4) Figure S4 helpfully shows the behavior of a pentameric control system; however, some elements are unclear.

(4a) The 2.5-6.5 Å jump in RMSD at ~40 ns seems abrupt; can it be clarified whether this corresponds to a transition to either m2 or m3 poses, or to another feature of e.g. alignment?

Figure 2-figure supplement 4 left bottom is just the ligand. The jump is the flip, m1 to m2.

(4b) It seems difficult to reconcile the apparently bimodal distribution of states with the proposed 3-state model. Into which RMSD peak would the m2 intermediate fall?

The simulations are only to 100 ns, where we found a complete flip of the agonist represented in the histograms. This confirmed that dimer showed similar pattern as the pentamer. In depth analysis was only done only on dimers.

(4c) The top panel is labeled "Com" with a graphical legend indicating "ACh." Does this indicate the ligand or, as described in the text legend, "the pentamer" (i.e. the receptor)? For both panels, please verify whether they are calculated on the basis of center-of-mass, heavy atoms, Cα, etc.

"Com" (for complex) has been changed to system (protein+ligand).

(5) Minor concerns:

(5a) In Figures 1 and S3, correct the PDB references (6UWX and 7QL7 are not nAChRs).

They are now corrected.

(5b) In Figure 4, do all panels represent mean {plus minus} standard deviation calculated across all cluster-frames reported in Table 1?

Yes.

Also check the graphical legend in panel A: presumably the red bars correspond to m1/LA, and the blue to m3/HA?

Corrected

(5c) In the legend to Figure S1, please clarify that panel B is reproduced from Indurthi & Auerbach 2023.

This figure has been deleted.

(5d) As indicated in Figure S2, it seems surprising that the RMSF is so apparently low at the periphery, where the subunits should contact neighbors in the extracellular domain; how might the authors account for this? Specify whether these results apply to all replicates of each system.

The redness in the periphery for all four systems indicates the magnitude of fluctuation. As we focus on the orthosteric site, we highlight the loops around the agonist binding pocket and kept other regions 75% transparent. We now include Apo simulations and the dimer appears to be stable even without an agonist present.

(5e) Within each minimum in Figure S5, three "prominent" clusters appear to be colored (by heteroatom) with carbons in cyan, pink, and yellow respectively. If this is correct, note these colors in the text legend.

Colors have been added to the legend.

(5f) In Figure S6, note in the legend that key receptor sidechains are shown as spheres, with the ligand as balls-and-sticks, and that ligand conformations in both low- and high-affinity complexes are shown in both receptor states for comparison.

This is now added in the legend.

(5g) The legend to Figure S6 also notes "The agonists are as in Fig S4," but that figure contains a single replicate of a different system; please check this reference.

This has been updated to Figure 5.

(5h) In Figure S8, the colors in the epibatidine system appear different from the others.

The colors are the same for m1, m2 and m3 in all systems including epibatidine.

(5i) In Table 1, does "n clusters" indicate the number of simulation frames included in the three prominent clusters chosen for MM-PBSA analysis? Perhaps "n frames" would be more clear.

It was a good suggestion. It has now been changed to ‘n frames’

(5j) Pg 24-ln 453 presumably should read "...that separate it from m1 and m3..."

This sentence is now changed in the discussion.

Author Response

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

Thank you and the two reviewers for the thorough review of our manuscript. We thank you very much for the positive evaluation of our manuscript and your encouragement to continue in this fascinating topic. In this version we made minor changes in the text to address the comments and suggestion of the second reviewer and increase the clarity of the text.

Reviewer #2 Recommendation to the authors

We thank the reviewer for the sharp comments that help us improve the clarity of the paper. Below we list the changes we made to correct and revise the paper in accordance to the reviewer’s comments.

(1) Line 90. Isn't the genus Paracentrotus?

Yet it is, thank you. We corrected the typo.

(2) Figure 1 and supplementary figure 2. To this reviewer supplementary Figure 2 doesn't really help the story as written in the paragraph from line 96-110. You want to report expression of ROCK in skeletogenic cells. You do that quite well in Figure 1. Since Fig. S2 reports whole embryo expression of ROCK when only 5% of the cells in the embryo are the subject of interest here, and the Axitinib is selective, presumably for skeletogenic cells, the relative lack of effect in Fig. S2 is not surprising and again, doesn't really help the theme you wish to establish by focusing on the role of ROCK in skeletogenic cells over time. If anything, the data reported in Fig. S2 shows that perturbation of VEGF signaling has very little effect embryo-wide, while Fig. 1 shows that perturbation of VEGF signaling has a noticeable effect on ROCK expression in skeletogenic cells. If you choose to keep Fig. S2, I recommend that you indicate that embryo-wide vs skeletogenic cell difference more succinctly than given at present. It will also strengthen your paragraph in lines 110-127.

The importance of the western blot presented in Fig. S2 is to validate that the antibody recognizes a protein of the expected size. This strengthen the credibility of this commercial antibody to detect the sea urchin ROCK protein. We agree with the reviewer that the fact that the skeletogenic cells are less than 5% of the embryonic cells is important to explain why we didn’t see an affect of VEGFR inhibition in the western blot, and we changed the text to express it (lines 108-111): “Yet, this measurement was done on proteins extracted from whole embryos, of which the skeletogenic cells, where VEGFR is active, are less than 5% of the total cell mass (42). We therefore wanted to study the spatial expression of ROCK and specifically, its regulation in the skeletogenic cells.”

(3) Comparison of Fig. 2 and Fig. S3. To me the reader is confused when Fig. S3 is 33hpf as reported in the text (but not in the figure legend), and Fig. 2 shows 2 day old embryos - on the figure and figure legend but not in the text. So, the reader sees the text indicating 33hpf and looks around and the figure 2 says 2dpf. Does that mean 33hpf = 2dpf, the reader is thinking. To clarify, I suggest including the 2dpf in the text or simply drop the time in the text and report it in the two figures. Further, in the middle of the paragraph 130-143 you switch from reporting on Fig.S3 to Fig. 2, yet the reader doesn't know that. The reader is still looking at Fig. S3. The problem here is that at 33hpf the skeleton doesn't yet show the reduction or abnormalities that are shown later at 2dpf in Fig. 2. In clarifying this paragraph both the reduction in ROCK expression and the subsequent alterations in growth and patterning of the skeleton will be clear to the reader.

Thank you for raising this point. We added in the caption of Fig. S3 that the measurements were done in 33hpf. We also added in the text, that the observations of the skeletogenic phenotypes were done at 2dpf (48hpf). We made a break between the first paragraph discussing Fig. S3 and the paragraph discussing Fig. 2.

(4) The experiment with Y27632, an inhibitor of ROCK, is significantly improved in this revision. The concern earlier was the possibility that at the concentration used there might be off-target effects since other kinases are affected by higher concentrations of this selective inhibitor. The authors have modified this component of the paper and performed experiments at lower concentrations where other reports indicate the inhibitor is highly selective for ROCK, and they still demonstrate an inhibition of skeletal production. This, plus the added citations greatly increases confidence that this inhibition is selective for ROCK, thus enabling a stronger conclusion that ROCK has a role in skeletal growth and patterning.

Thank you for asking us to test this lower concentration which improved the credibility of our findings.

Line 239 - should be: indicating instead of indicting We corrected that.

(5) Line 402-403."The first step in generating the sea urchin spicules is the construction of the spicule cavity, a membrane filled with calcium carbonate and coated with F-actin (Fig. 8A)". I suggest more precise language. The way this now reads (above) is that somehow the spicule cavity is a membrane and that membrane is filled with CaCO3. And further the membrane is coated with F-actin. Isn't the spicule cavity what is filled with CaCO3? And isn't that cavity surrounded by a membrane? And the F-actin must be in the cortex of the cell since there is very little cytoplasm associated with the pseudopodial extensions that surround the spicule.

We change this sentence to: “The first step in generating the sea urchin spicules is the construction of the spicule cavity where the mineral is engulfed in a membrane coated with F-actin” (lines 403-404). Our observations show that F-actin is enriched around the spicule cavity. It could be an extension of the cell cortex, but we did not prove it, so we prefer to simply describe what we saw.

Line 405-408. Thank you for putting in this unknown. It is important to point out that while you've shown that ROCK contributes to regulation of actomyosin, it is not clear whether this is direct or indirect. You have also shown that ROCK somehow contributes to regulation of the GRN that leads to skeletogenesis. Thus, your data are consistent in showing that ROCK perturbation cripples normal skeletogenesis both via morpholino and with a selective inhibitor. Your last part of the discussion then offers speculation as to what might be affected specifically. That discussion sets the stage for digging even deeper to identify specific targets of ROCK activity.

Thank you, we agree with you that there is an exciting road ahead of us!

Author Response

Reviewer #1 (Public Review):

Weaknesses:

The manuscript needs proper editing and is not complete. Some wordings lack precision and make it difficult to follow (e.g. line 98 "we assembled a chromosome-scale genome of ..." should read instead "we assembled a chromsome-scla genome sequence of ...". Also, panel Figure 2E is missing.

We will make the suggested change of adding “sequence”. Concerning additional changes, we have carefully edited our manuscript and looked for any incomplete sections. Unfortunately, it is difficult to see what other issues are being raised here without any further information. And the example given is not helpful to ascertain what other changes may be necessary, since we cannot see any problem with the sentence “we assembled a chromosome-scale genome of” as this phrase is widely used in many similar publications.

As for panel E of figure 2, it is not missing. The panel located to the right, just below “Target Cells”.

The shortcomings of the manuscripts are not limited to the writing style, and important technical and technological information is missing or not clear enough, thereby preventing a proper evaluation of the resolution of the genomic resources provided:

• Several RNASeq libraries from different tissues have been built to help annotate the genome and identify transcribed regions. This is fine. But all along the manuscript, gene expression changes are summarized into a single panel where it is not clear at all which tissue this comes from (whole embryo or a specific tissue ?), or whether it is a cumulative expression level computed across several tissues (and how it was computed) etc. This is essential information needed for data interpretation.

No fertilised eggs or embryos have been sequenced, individual tissues derived from juvenile fish were used for the genome annotation and whole larval fish for the developmental analysis. We will specify in the figures and text that the results shown are from whole larvae, and add more detail to the material and methods section about which type of sample was analysed in which way.

• The bioinformatic processing, especially of the assemble and annotation, is very poorly described. This is also a sensitive topic, as illustrated by the numerous "assemblathon" and "annotathon" initiatives to evaluate tools and workflows. Importantly, providing configuration files and in-depth description of workflows and parameter settings is highly recommended. This can be made available through data store services and documents even benefit from DOIs. This provides others with more information to evaluate the resolution of this work. No doubt that it is well done,but especially in the field of genome assembly and annotation, high resolution is VERY cost and time-intensive. Not surprisingly, most projects are conditioned by trade-offs between cost, time, and labor. The authors should provide others with the information needed to evaluate this.

We will upload the code used to assemble and annotate this genome to a public repository or add it to the supplementary material.

The genome assembly did not use a specific workflow (e.g., nextflow), but was done with a simple command and standard parameters in IPA. Scaffolding was carried out by Phase Genomics using their standardised proprietary workflow, of which a detailed description provided by Phase Genomics can be found in the supplementary material. The annotation workflow has been described in a previous publication already, but an in-depth description can also be found in the Material and methods section, including parameters used for specific steps. The RNA-seq mapping and analysis part has also been described in the Material and Methods section, including parameters and models for DESEq2.

• Quantifications of T3 and T4 levels look fairly low and not so convincing. The work would clearly benefit from a discussion about why the signal is so low and what are the current technological limitations of these quantifications. This would really help (general) readers.

We will add a comment on this in the manuscript as suggested. Basically, the T3/T4 levels are consistent with other published work in fish. In the present manuscript for grouper we have a peak level of 1.2 ng/g (1,200 pg/g) of T4 and 0.06 ng/g (60 pg/g) of T3. This is a higher level of T4 and comparable level of T3 to what was found in convict tang (Holzer et al. 2017; Figure 2) with 30 pg/g of T4 and 100 pg/g of T3. Of course, there are also examples with higher levels, such as clownfish (Roux et al. 2023; Figure 1), with 10 ng/g (10,000 pg/g) of T4 and 2 ng/g (2,000 pg/g) of T3.

The differences could be due to different structure of fish tissues and therefore different hormone extraction efficiency, different hormone measurement protocols, different fish physiology, different fish size (e.g., the weighting of tiny grouper larvae is difficult and less precise than in convict tang). What is important is not the absolute level but the relative level, which shows the change within different larval stages of a species with identical extraction and measurement protocols. Which means our data is internally consistent and coherent with what the grouper literature says.

Holzer, Guillaume, et al. "Fish larval recruitment to reefs is a thyroid hormone-mediated metamorphosis sensitive to the pesticide chlorpyrifos." Elife 6 (2017): e27595.

Roux, Natacha, et al. "The multi-level regulation of clownfish metamorphosis by thyroid hormones." Cell Reports 42.7 (2023).

• Differential analysis highlights up to ~ 15,000 differentially expressed genes (DEG), out of a predicted 26k genes. This corresponds to more than half of all genes. ANOVA-based differential analysis relies on the simple fact that only a minority of genes are DEG. Having >50% DEG is well beyond the validity of the method. This should be addressed, or at least discussed.

As the reviewer notes, there are a large number of differentially expressed genes due to the fact that this is coming from a larval developmental transcriptome going from one day old larva to fully metamorphosed juveniles at around day 60.

While DESeq2 indeed works on an assumption that most genes are not differentially expressed, this affects normalization but not hypothesis testing (Wald-test, LRT tests or ANOVA). Normalisation in DESeq2 is fairly robust to this assumption. According to the author of DESeq2, Micheal Love, DESeq2 is using the median ratio for normalisation, and as long as the number of up and down regulated genes is relatively even, DESeq2 will be able to handle the data. As part of our general quality control for this project we consulted the MA plots, which do not show any overrepresented up or down expression patterns. Additionally see Michael Love comment on comparing different tissues, which is also applicable here when comparing vastly different larval stages (https://support.bioconductor.org/p/63630/): “For experiments where all genes increase in expression across conditions, the median ratio method will not be able to capture this difference, but this is typically not the case for a tissue comparison, as there are many "housekeeping" genes with relatively similar expression pattern across tissues.”

Reviewer #3 (Public Review):

Weaknesses:

However, the authors make substantial considerations that are not proven by experimental or functional data. In fact, this is a descriptive study that does not provide any functional evidence to support the claims made.

We agree with the reviewer that our paper lacks functional experiments but despite that, the transcriptomic data clearly show the activation of TH and corticoid pathways during two distinct periods; an early activation between D1 and D10, and a second one between D32 and juvenile stage. These data are interesting as they call for further examination of 1) the possible interaction of corticoids and TH during metamorphosis, a question that is certainly not settled yet in teleost fishes, and 2) the existence of an early larval developmental step also involving TH and corticosteroids.

Especially 2) is of interest and importance, since this early activation (unique to our knowledge in any teleost fish studied so far) raises a lot of new questions and once again will certainly be scrutinised by other groups in the years to come, therefore ensuring a good citation impact of our study. We hope that the reviewer, while disagreeing with some our statements, will recognize that our study will be stimulating at that level and that this is what scientific studies should do.

The consideration that cortisol is involved in metamorphosis in teleosts has never been shown, and the only example cited by the authors (REF 20) clearly states that cortisol alone does not induce flatfish metamorphosis. In that work, the authors clearly state that in vivo cortisol treatment had no synergistic effect with TH in inducing metamorphosis. Moreover, in Senegalensis, the sole pre-otic CRH neuron number decreases during metamorphosis, further arguing that, at least in flatfish, cortisol is not involved in flatfish metamorphosis (PMID: 25575457).

We will do our best to improve the clarity of the revised manuscript to avoid any misunderstanding about our claims. However, we would like to point out the semantic shift in the reviewer first sentence: Indeed “being involved” is not the same as “cortisol alone does not induce”. In ref 20 the authors explicitly wrote that “Cortisol further enhanced the effects of both T4 and T3, but was ineffective in the absence of thyroid hormones” and in our view this indeed corresponds to ”being involved in metamorphosis”.

We are not claiming that cortisol alone is involved in metamorphosis as the reviewer suggests, but simply that there is a possible involvement of cortisol together with TH in metamorphosis. We stand on this claim as we indeed observed an activation of corticoid pathway genes around D32, which is sufficient to say it is involved. We do agree that functional experiments will be needed to properly demonstrate the involvement of corticoids in grouper metamorphosis, but this was not possible in the current study as it would imply to set up a full grouper life cycle in lab conditions which is impossible for the scope of this manuscript.

We also mentioned in the discussion that the role of corticoids in fish larval development is still debated, and we agree that this remain a contentious issue.

We wrote that “there is contrasting evidence of communication between these two pathways [TH and corticosteroids] in teleost fish with some data suggesting a synergic and other an antagonistic relationship. In terms of synergy, an increase in cortisol level concomitantly with an increase in TH levels has been observed in flatfish (ref 19), golden sea bream (ref 100) and silver sea bream (ref 101). Cortisol was also shown to enhance in vitro the action of TH on fin ray resorption (phenomenon occurring during flatfish metamorphosis) in flounder (ref 20). TH exposure increases MR and GR genes expression in zebrafish embryo (ref 55). It has also been shown that cortisol regulates local T3 bioavailability in the juvenile sole via regulation of deiodinase 2 in an organ-specific manner (ref 56) On the antagonistic side, it has been shown that experimentally induced hyperthyroidism in common carp, decreasing cortisol levels (ref 57), whereas cortisol exposure decreases TH levels in European eel (ref 58). Given this scattered evidence, the existence of a crosstalk active during teleost metamorphosis has never been formally demonstrated. The results we obtained in grouper are clearly indicating that HPI axis and cortisol synthesis are activated (i) during early development and (ii) during metamorphosis. This may suggest that in some aspect cortisol synthesis can work in concert with TH, as has been shown in several different contexts in amphibians (ref 17).” In the revised manuscript, we will also add the interesting case of the Senegal sole mentioned by the reviewer.

In the last revision, we had also added that our results “brought a first insight into the potential role of corticoids in the metamorphosis of E. malabaricus and call for functional experiments directly testing a possible synergy” meaning that we clearly acknowledge that we are only revealing a hypothesis that remains to be tested. We later follow up with a discussion about the most novel observation and focus of our study, the increase in THs and cortisol during early development, which was unexpected and very intriguing. Again, these results suggest that there might be a link between the two, as has been shown in amphibians. This is typically the kind of results that should encourage more investigations into other fish species. Indeed, this has been pointed out by other authors and in particular by Bob Denver (probably the foremost expert on this topic) in Crespi and Denver 2012: “Elevation in HPA/I axis activity has been described prior to Metamorphosis in amphibians and fish, birth in mammals (reviewed in Crespi & Denver 2005a; Wada 2008)”. B. Denver also adds that: “Experiments in which GCs were elevated prior to metamorphosis or prior to hatching or birth (e.g. Weiss, Johnston & Moore 2007) or inhibited by treatments with GC synthesis blockers (e.g. metyrapone) or receptor antagonists (e.g. RU486, Glennemeir & Denver 2002) demonstrate that GCs play a causal role in precipitating these life-history transitions (also reviewed in Crespi & Denver 2005a; Wada 2008).” We believe the reviewer will be convinced by these elements coming from a colleague unanimously respected in the field.

Furthermore, the authors need to recognise that the transcriptomic analysis is whole-body and that HPA axis genes are upregulated, which does not mean they are involved in regulating the HPT axis. The authors do not show that in thyrotrophs, any CRH receptor is expressed or in any other HPT axis-relevant cells and that changes in these genes correlate with changes in TSH expression. An in-situ hybridisation experiment showing co-expression on thyrotrophs of HPA genes and TSH could be a good start. However, the best scenario would be conducting cortisol treatment experiments to see if this hormone affects grouper metamorphosis.

We agree that functional experiments are needed to validate our hypothesis. As the early peaks of expression levels observed for many genes were very intriguing for us, we did carry out thyroid hormones and goitrogenic treatment on young grouper larvae to test their effect on the morphological changes. Unfortunately, such experiments, already tricky on metamorphosing larvae, are even more risky on such tiny individuals just after hatching and we encountered high mortality rates. We must add that because we cannot establish a full grouper life cycle under lab conditions, we have done these experiment in the context of a commercial husbandry system in Japan, which while excellent limits the scope of possible experiments. We were thus not able to provide functional validation of our hypothesis. Such experiments will be a full project in itself, requiring setting up a rearing system suitable for both larval survival and economical constraints related to drug treatments. We were further limited by the spawning times of the grouper in the operational aquaculture farm, which are limited to a short time during each year. So even if we strongly agree with the necessity of conducting such experiments, we think that this is not in the scope of the present paper, but something future research can explore.

High TSH and Tg levels usually parallel whole-body TH levels during teleost metamorphosis. However, in this study, high Tg expression levels are only achieved at the juvenile stage, whereas high TSH is achieved at D32, and at the juvenile stage, they are already at their lowest levels.

This is exactly our point. We observe two peaks in TSH expression, one at D3 and one at D32. The peak at D3 coincides with high thyroid hormone levels on the same day, and while we have not measured TH at D32, existing literature shows that there is a peak in TH during that time (e.g., de Jesus et al., 1998). Similarly, there is a small peak of Tg at D3. Our manuscript focused more on the upregulation of these genes at D3, which has not been reported before in the literature and raised the question of the role of TH so early in the larval development, outside of the metamorphosis period.

Regarding the respective levels of TSH and Tg, we first would like to add that their respective order of appearance before metamorphosis (TSH at D32, Tg after) is consistent with what we would expect. We agree however that the strong increase of Tg and TPO expression is later than expected. We will make this clear in the revised manuscript.

It is very difficult to conclude anything with the TH and cortisol levels measurements. The authors only measured up until D10, whereas they argue that metamorphosis occurs at D32. In this way, these measurements could be more helpful if they focus on the correct developmental time. The data is irrelevant to their hypothesis.

We respectfully disagree with the reviewer, considering that 1) TH levels have already been investigated in groupers coinciding with pigmentation changes and fin rays resorption, 2) that there is also evidence in numerous fish species that TH level increase is concomitant with increase of TH related genes, and 3) that we observed in our data an increase in the expression of TH related genes as well as pigmentation changes and fin rays resorption. Based on our experience in fish metamorphosis and the literature we can say confidently that those observations indicate that metamorphosis is occurring between D32 and the juvenile stage. To reinforce our point, we plan to add a figure to the revised manuscript, which puts our data in the context of earlier studies done in grouper. This will clearly show that our inference is correct. Additionally, we would like to point out that from our experience in several fish species transcriptomic data are more robust and precise than hormone measurements.

However, as we were surprised by the activation of TH and corticoid pathway genes very early in the larval development (at D3), which is clearly outside of the metamorphosis period, we decided to measure TH and cortisol levels during this period of time to determine if whether or not there this surprising early activation was indeed corresponding to an increase in both TH and cortisol. As such observation has never been made in other teleost species (to our knowledge), and as we were wondering if gene activation was accompanied by hormonal increase, the measurements we did for TH and cortisol between D1 and D10 are relevant. We will make sure to improve the clarity of the revised version of the manuscript to avoid any confusion between the two periods we are studying: early larval development (between D1 and D10) and metamorphosis (between D32 and juvenile stage).

Moreover, as stated in the previous review, a classical sign of teleost metamorphosis is the upregulation of TSHb and Tg, which does not occur at D32 therefore, it is very hard for me to accept that this is the metamorphic stage. With the lack of TH measurements, I cannot agree with the authors. I think this has to be toned down and made clear in the manuscript that D32 might be a putative metamorphic climax but that several aspects of biology work against it. Moreover, in D10, the authors show the highest cortisol level and lowest T4 and T3 levels. These observations are irreconcilable, with cortisol enhancing or participating in TH-driven metamorphosis.

We thank the reviewer for this comment, but we think that there might be a misunderstanding here.

(1) We clearly observed an increase of TSHb (that occurs between D18 and juvenile stage) and an increase of tg from D32 which coincide with the activation of other genes involved in TH pathway (dio2, dio3, and also a strong increase of TRb). All this and put in the context of what we know from previous grouper studies, clearly supports our conclusion that TH-regulated metamorphosis is starting at around D32 in grouper. We also observed morphological changes such as fin rays resorption and pigmentation changes between D32 and juvenile stage. Such morphological changes have already been associated as corresponding to metamorphosis in groupers (De Jesus et al 1998) as they occur during TH level increase, and they also happen to be under the control of TH in grouper (De Jesus et al 1998). Based on this study but also on studies (conducted on many other teleost species) showing that the increase of TH levels is always associated with an activation of TH pathway genes and morphological and pigmentation changes we concluded that metamorphosis of E. malabaricus occurs between D32 and juvenile stage. We will improve the clarity of the manuscript to make sure that our conclusion is based on our transcriptomic and morphological data plus the available literature.

(2) We clearly observed another activation of TH related gene earlier in the development (between D1 and D10, with a surge of trhrs, tg and tpo at D3. As this activation was very unexpected for us, we decided to focus the analysis of TH levels between D1 and D10 and very interestingly we observed high level of T4 at D3 indicating that THs are instrumental very precociously in the larval development of the malabar grouper which has never been shown before. We declared line 195 that our “data reinforce the existence of two distinct periods of TH signalling activity, one early on at D3 and one late corresponding to classic metamorphosis at D32”. However, we agree that we could have been clearer and clearly explained that this early activation was very intriguing for us and that we wanted to investigate hormonal levels around that period. However, we never claimed anywhere in the manuscript that this early developmental period corresponds to metamorphosis. Something else is occurring and both TH and cortisol seem to be involved but further experiments need to be conducted to understand their role and their possible interaction.

(3) Finally, regarding the comment about cortisol enhancing or participating in TH driven metamorphosis, our data clearly showed an activation of the corticoid pathway genes around metamorphosis (between D32 and juvenile stage) suggesting a potential implication of corticoids in metamorphosis, but we agree with the reviewer that further experiment are needed to test that. We never claimed that cortisol was enhancing or participating in metamorphosis, on the contrary we are “suggesting a possible interaction between TH and corticoid pathway during metamorphosis”. And we also say that our “results brought a first insight into the potential role of corticoids in the metamorphosis of E. malabaricus and call for functional experiments directly testing a possible synergy.” Nonetheless, we agree that some parts of our manuscript can be confusing in regards of cortisol synthesis during metamorphosis as we did not measure cortisol levels between D32 and juvenile stage. We will correct this in the revised version.

Given this, the authors should quantify whole-body TH levels throughout the entire developmental window considered to determine where the peak is observed and how it correlates with the other hormonal genes/systems in the analysis.

We did not measure TH levels at later stages as it has already been measured during Epinephelus coioides metamorphosis and the morphological changes observed in this species around the TH peak corresponds to what we observed in Epinephelus malabaricus around the peak of expression of TH pathway genes (see De Jesus et al., 1998 General and Comparative Endocrinology, 112:10-16). We are planning to add a figure reconciling all these data together. However, the main focus of this manuscript is the novel observation of the existence of an early activation period observed at D3, and for which we needed TH levels to determine if they were involved in another early developmental process (not related to metamorphosis). Our hypothesis is that this early activation might be related to the growth of fin rays necessary to enhance floatability during the oceanic larval dispersal. As we may have arrived at the explanation of this hypothesis too rapidly without setting up the context well enough, we will pay attention to improve that part too.

Even though this is a solid technical paper and the data obtained is excellent, the conclusions drawn by the authors are not supported by their data, and at least hormonal levels should be present in parallel to the transcriptomic data. Furthermore, toning down some affirmations or even considering the different hypotheses available that are different from the ones suggested would be very positive.

We thank the reviewer for acknowledging the solidity of the method of our paper and the quality of the results. We agree that there were several parts where our message is unclear, which we will address in the revised version of the manuscript to make sure there is no more confusion between the two distinct periods we studied in this paper (early larval development and metamorphosis). We will also make sure that our claims about TH/corticoids interaction during both periods remain hypothetical as we cannot yet, despite trials, sustain them with functional experiment.

Author Response

We provide here a provisional response to the Public Comments and main issues raised by the reviewers. We appreciate the opportunity to submit a revision and will give all of the reviewers’ comments careful consideration when modifying the manuscript.

(1) BioRxiv version history.

Reviewer 1 correctly noted that we have posted different versions of the paper on bioRxiv and that there were significant changes between the initial version and the one posted as part of the eLife preprint process. Here we provide a summary of that history.

We initially posted a bioRxiv preprint in November, 2021 (Version 1) that included the results of two experiments. In Experiment 1, we compared conditions in which the stimulation frequency was at 2 kHz, 3.5 kHz, or 5.0 kHz. In Experiment 2, we replicated the 3.5 kHz condition of Experiment 1 and included two amplitude-modulated (AM) conditions, with a 3.5 kHz carrier signal modulated at 20 Hz or 140 Hz. Relative to the sham stimulation, non-modulated kTMP at 2 kHz and 3.5 kHz resulted in an increase in cortical excitability in Experiment 1. This effect was replicated in Experiment 2.

In the original posting, we reported that there was an additional boost in excitability in the 20 Hz AM condition above that of the non-modulated condition. However, in re-examining the results, we recognized that the 20 Hz AM condition included an outlier that was pulling the group mean higher. We should have caught this outlier in the initial submission given that the resultant percent change for this individual is 3 standard deviations above the mean. Given the skew in the distribution, we also performed a log transform on the MEPs (which improves the normality and homoscedasticity of MEP distributions) and repeated the analysis. However, even here the participant’s results remained well outside the distribution. As such, we removed this participant and repeated all analyses. In this new analysis, there was no longer a significant difference between the 20 Hz AM and nonmodulated conditions in Experiment 2. Indeed, all three true stimulation conditions (nonmodulated, AM 20 Hz, AM 140 Hz) produced a similar boost in cortical excitability compared to sham. Thus, the results of Experiment 2 are consistent with those of Experiment 1, showing, in three new conditions, the efficacy of kHz stimulation on cortical excitability. But the results fail to provide evidence of an additional boost from amplitude modulation.

We posted a second bioRxiv preprint in May, 2023 (Version 2) with the corrected results for Experiment 2, along with changes throughout the manuscript given the new analyses.

Given the null results for the AM conditions, we decided to run a third experiment prior to submitting the work for publication. Here we used an alternative form of amplitude modulation (see Kasten et. al., NeuroImage 2018). In brief, we again observed a boost in cortical excitability in from non-modulated kTMP at 3.5 kHz, but no additional effect of amplitude modulation. This work is included in the third bioRrxiv preprint (Version 3), the paper that was submitted and reviewed at eLife.

(2) Statistical analysis.

Reviewer 1 raised a concern with the statistical analyses performed on aggregate data across experiments. We recognize that this is atypical and was certainly not part of an a priori plan. Here we describe our goal with the analyses and the thought process that led us to combine the data across the experiments.

Our overarching aim is to examine the effect of corticospinal excitability of different kTMP waveforms (carrier frequency and amplitude modulated frequency) matched at the same estimated cortical E-field (2 V/m). Our core comparison was of the active conditions relative to a sham condition (E-field = 0.01 V/m). We included the non-modulated 3.5 kHz condition in Experiments 2 and 3 to provide a baseline from which we could assess whether amplitude modulation produced a measurable difference from that observed with non-modulated stimulation. Thus, this non-modulated condition as well as the sham condition was repeated in all three experiments. This provided an opportunity to examine the effect of kTMP with a relatively large sample, as well as assess how well the effects replicate, and resulted in the strategy we have taken in reporting the results.

As a first step, we present the data from the 3.5 kHz non-modulated and sham conditions (including the individual participant data) for all three experiments in Figure 4. We used a linear mixed effect model to examine if there was an effect of Experiment (Exps 1, 2, 3) and observed no significant difference within each condition. Given this, we opted to pool the data for the sham and 3.5 kHz non-modulated conditions across the three experiments. Once data were pooled, we examined the effect of the carrier frequency and amplitude modulated frequency of the kTMP waveform.

(3) Carry-over effects

As suggested by Reviewer 1, we will examine in the revision if there is a carry-over effect across sessions (for the most part, 2-day intervals between sessions). For this, we will compare MEP amplitude in baseline blocks (pre-kTMP) across the four experimental sessions.

Reviewer 1 also commented that mixing the single- and paired-pulse protocols might have impacted the results. While our a priori focus was on the single-pulse results, we wanted to include multiple probes given the novelty of our stimulation method. Mixing single- and different paired-pulse protocols has been relatively common in the noninvasive brain stimulation literature (e.g., Nitsche 2005, Huang et al, 2005, López-Alonso 2014, Batsikadze et al 2013) and we are unaware of any reports suggested that mixed designs (single and paired) distort the picture compared to pure designs (single only).

(4) Sensation and Blinding

Reviewer 2 bought up concerns about the sham condition and blinding of kTMP stimulation. We do think that kTMP is nearly ideal for blinding. The amplifier does emit an audible tone (at least for individuals with normal hearing) when set to an intensity to produce a 2 V/m E-field. For this reason, the participants and the experimenter wore ear plugs. Moreover, we played a 3.5 kHz tone in all conditions, including the sham condition, which effectively masked the amplifier sound. We measured the participant’s subjective rating of annoyance, pain, and muscle twitches after each kTMP session (active and sham). Using a linear mixed effect model, we found no difference between active and sham for each of these ratings suggesting that sensation was similar for active and sham (Fig 8). This matches our experience that kHz stimulation in the range used here has no perceptible sensation induced by the coil. To blind the experimenters (and participants) we used a coding system in which the experimenter typed in a number that had been randomly paired to a stimulation condition that varied across participants in a manner unknown to the experimenter.

Reviewer 1 asked why we did not explicitly ask participants if they thought they were in an active or sham condition. This would certainly be a useful question. However, we did not want to alert them of the presence of a sham condition, preferring to simply describe the study as one testing a new method of non-invasive brain stimulation. Thus, we opted to focus on their subjective ratings of annoyance, pain, and finger twitches after kTMP stimulation for each experimental session.

Author Response

Provisional Response to Public Reviews

Reviewer #1 (Public Review):

Summary:

The work by Zeng et al. comprehensively explored the differences in the effects of leaf and soil microbes on the seed germination, seedling survival, and seedling growth of an invasive forb, Ageratina adenophora, and found evidence of stronger effects of leaf microbes on Ageratina compared with soil microbes, which were negative for seed germination and seedling survival but positive for seedling growth. By further DNA sequencing and fungal strain cultivation, the authors were able to identify some of the key microbial guilds that may facilitate such negative and positive feedback.

Thank you very much for your assessment.

Strengths:

(1) The theoretic framework is well-established.

(2) Relating the direction of plant-microbe feedback to certain microbial guilds is always hard, but the authors have done a great job of identifying and interpreting such relationships.

Thank you very much for your assessment.

Weaknesses:

(1) In the G0 and G21 inoculation experiments, allelopathic effects from leaf litters had not been accounted for, while these two experiments happened to be the ones where negative feedback was detected.

We did not directly test the allelopathic effects. However, our inoculation of sterile litter or soil indicated the potential allelopathic role in germination and seedling mortality. Interestingly, such allelopathic effects are elicited by leaf litter not by soil, which include delaying germination time (see Fig. 1a) and killing some seedlings (see Fig. 1c). Nonetheless, microbial effects are significantly more adverse than allelopathic (also see Fig. 1e). We will discuss this point in the resubmitted version.

(2) The authors did not compare the fungal strains accumulated in dead seedlings to those accumulated in live seedlings to prove that the live seedlings indeed accumulated lower abundances of the strains that were identified to increase seedling mortality.

Thanks for your concerns. We have not isolated fungi from healthy seedlings to make a comparative study. However, our team work previously found that the seedling-killing Allophoma strains obtained in this study had the same ITS genes as the leaf endophyte and leaf spot pathogen Allophoma associated with mature A. adenophora individual; some seedling-killing Alternaria also occur in healthy seedlings inoculated by leaf litter. We thus assumed that these seedling-killing fungi, e.g., Allophoma and Alternaria, likely exist in A. adenophora mature individual by a lifestyle switch from endophytic to pathogenic, and these fungi can kill seedling only at very early life stage of A. adenophora.

Thus, we discussed this point as: “We did not isolate fungi from healthy seedlings in this study. However, a previous report revealed that the dominant genera in healthy seedlings inoculated with leaf litter were Didymella and Alternaria (Kai Fang et al., 2019). Based on these results, these fungal genera likely exist in A. adenophora by a lifestyle switch from endophytic to pathogenic. The virulence of these strains for seedling survival under certain conditions may play an essential role in limiting the population density of A. adenophora monocultures.” See Lines 416-435.

Here, we also will consider adding more sentences to discuss your concerns in the resubmitted version as: “It is worth to explore the dynamic of these strains along with seedling development and to determine if these strains kill seedling only at very early stage.”

(3) The data of seed germination and seedling mortality could have been analyzed in the same manner as that of seedling growth, which makes the whole result section more coherent. I don't understand why the authors had not calculated the response index (RI) for germination/mortality rate and conducted analyses on the correlation between these RIs with microbial compositions.

Thanks so much. Response index (RI) was calculated as: (variablenon-sterile–variablesterile)/variablesterile)). Because mortality rates of some sterile groups were zero values, it is impossible to calculate their RIs. Relatively, microbes rarely affect seed germination time (GT) and rate (GR) (see Fig. 1a,b). Therefore, we preferred to make a direct comparison of their difference between non-sterile and sterile treatments (see also Figure S2), and we also conducted a correlation by these values with microbial compositions rather than by RIs (see Fig. 4).

We will emphasis this point in the Materials and Methods when resubmit our revision.

(4) The language of the manuscript could be improved to increase clarity.

We will improve this in the resubmitted version.

Reviewer #2 (Public Review):

Summary:

The study provides strong evidence that leaf microbes mediate self-limitation at an early life stage. It highlights the importance of leaf microbes in population establishment and community dynamics.

Thank you very much for your assessment.

The authors conducted three experiments to test their hypothesis, elucidating the effects of leaf and soil microbial communities on the seedling growth of A. adenophora at different stages, screening potential microbial sources associated with seed germination and seedling performance, and identifying the fungus related to seedling mortality. The conclusions are justified by their results. Overall, the paper is well-structured, providing clear and comprehensive information.

Thank you very much for your assessment.

Author Response

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

Response to Public Reviewer Comments

We again thank the reviewers for the time and effort they clearly put into reviewing our manuscript. We have revised our manuscript to take into account the majority of their suggestions, primary among them being refinements of our model and classification approach, detailed sensitivity analysis of our model, and several new simulations. Their very constructive feedback has resulted in what we feel is a much-improved paper. In what follows, we respond to each of their points.

Reviewer #1:

COMMENT: The reviewer suggested that our control policy classification thresholds should be increased, especially if the behavioral labels are to be subsequently used to guide analyses of neural data which “is messy enough, but having trials being incorrectly labeled will make it even messier when trying to quantify differences in neural processing between strategies.”

REPLY: We appreciate the observation and agree with the suggestion. In the revised manuscript, we simplified the model (as another reviewer suggested), which allowed for better training of the classifier. This enabled an increase in the threshold to 95% to have more confidence in the identified control strategies. Figures 7 and 8 were regenerated based on the new threshold.

COMMENT: The reviewer asked if we could discuss what one might expect to observe neurally under the different control policies, and also suggested that an extension of this work could be to explore perturbation trials, which might further distinguish between the two control policies.

REPLY: It is indeed interesting to speculate what neural activity could underlie these different behavioral signatures. As this task is novel to the field, it is difficult to predict what we might observe once we examine neural activity through the lens of these control regimes. We hope this will be the topic of future studies, and one aspect worthy of investigation is how neural activity prior to the start of the movement may reflect two different control objectives. Previous work has shown that motor cortex is highly active and specific as monkeys prepare for a cued movement and that this preparatory activity can take place without an imposed delay period (Ames et al., 2014; Cisek & Kalaska, 2005; Dekleva et al., 2018; Elsayed et al., 2016; Kaufman et al., 2014; Lara et al., 2018; Perich et al., 2018; Vyas et al., 2018; Zimnik & Churchland, 2021). It seems possible that the control strategies we observed correspond to different preparatory activity in the motor cortex. We added these speculations to the discussion.

The reviewer’s suggestion to introduce perturbations to probe sensory processing is very good and was also suggested by another reviewer. We therefore conducted additional simulations in which we introduced perturbations (Supplementary Material; Figure S10). Indeed, in these model simulations the two control objectives separated more. However, testing these predictions via experiments must await future work.

COMMENT: “It seems like a mix of lambda values are presented in Figure 5 and beyond. There needs to be some sort of analysis to verify that all strategies were equally used across lambda levels. Otherwise, apparent differences between control strategies may simply reflect changes in the difficulty of the task. It would also be useful to know if there were any trends across time?”

REPLY: We appreciate and agree with the reviewer’s suggestion. We have added a complementary analysis of control objectives with respect to task difficulty, presented in the Supplementary Material (Figures S7 and S8). We demonstrate that, overall, the control objectives remain generally consistent throughout trials and difficulty levels. Therefore, it can be concluded that the difference in behavior associated with different control objectives does not depend on the trial sequence or difficulty of the task. A statement to this extent was added to the main text.

COMMENT: “Figure 2 highlights key features of performance as a function of task difficulty. …However, there is a curious difference in hand/cursor Gain for Monkey J. Any insight as to the basis for this difference?”

REPLY: The apparently different behavior of Monkey J in the hand/cursor RMS ratio could be due to subject-to-subject variability. Given that we have data from only two monkey subjects, we examined inter-individual variations between human subjects in the Supplementary Material by presenting individual hand/cursor gain data for all individual human subjects (Figure S1). As can be seen, there was indeed variability, with some subjects not exhibiting the same clear trend with task difficulty. However, on average, the RMS ratio shows a slight decrease as trials grow more difficult, as was earlier shown in Figure 2. We added a sentence about the possibility of inter-individual variations to address the difference in behavior of monkey J with reference to the supplementary material.

Reviewer #2:

(Reviewer #2's original review is with the first version of the Reviewed Preprint. Below is the authors' summary of those comments.)

COMMENT: The reviewer commends the care and effort taken to characterize control policies that may be used to perform the CST, via dual human and monkey experiments and model simulations, noting the importance of doing so as a precursor to future neural recordings or BMI experiments. But the reviewer also wondered if it is all that surprising that different subjects might choose different strategies: “... it makes sense that different subjects might choose to favor different objectives, and also that they can do so when instructed. But has this taught us something about motor control or simply that there is a natural ambiguity built into the task?”

REPLY: The redundancy in the task that allowed different solutions to achieve the task was deliberate, and the motivation for choosing this task for this study. We therefore did not regard the resulting subject-to-subject variability as a finding of our study. Rather, redundancy and inter-individual variability are features ubiquitous in all everyday actions and we explicitly wanted to examine behavior that is closer to such behavior. As commended by the reviewers, CST is a rich task that extends our research beyond the conventional highly-constrained reaching task. The goal of our study was to develop a computational account to identify and classify such differences to better leverage future neural analyses of such more complex behaviors. This choice of task has now been better motivated in the Introduction of the revised manuscript.

COMMENT: The reviewer asks about our premise that subjects may use different control objectives in different trials, and whether instead a single policy may be a more parsimonious account for the different behavioral patterns in the data, given noise and instability in the system. In support of this view, the reviewer implemented a simple fixed controller and shared their own simulations to demonstrate its ability to generate different behavioral patterns simply by changing the gain of the controller. The reviewer concludes that our data “are potentially compatible with any of these interpretations, depending on which control-style model one prefers.”

REPLY: We first address the reviewer’s concern that a simple “fixed” controller can account for the two types of behavioral patterns observed in Experiment 2 (instructed groups) by a small change in the control gain. We note that our controller is also fixed in terms of the plant, the actuator, and the sensory feedback loop; the only change we explore is in the relative weights of position vs. velocity in the Q matrix. This determines whether it is deviations in position or in velocity that predominate in the cost function. This, in turn, generates changes in the gain vector L in our model, since the optimal solution (i.e. the gains L that minimize the cost function) depends on the Q matrix as well as the dynamics of the plant (specifically, the lambda value). Hence, one could interpret the differences arising from changes in the control objective (the Q matrix) as changes in the gains of our “fixed” controller.

More importantly, while the noise and instability in the system may indeed occasionally result in distinct behavioral patterns (and we have observed such cases in our simulations as well), these factors are far from giving an alternative account for the structural differences in the behavior that we attribute to the control objective. To substantiate this point, we performed additional simulations that are provided in the Supplementary Material (Figures S4—6). These simulations show that neither a change in noise nor in the relative cost of effort can account for the two distinct types of behavior. These differences are more consistently attributed to a change in the control objective.

In addition, our approach provides a normative account of the control gains needed to simulate the observed data, as well as the control objectives that underlie those gains. As such, the two control policies in our model (Position and Velocity Control) resulted in control gains that captured the differences in the experimental groups (Experiment 2), both at the single trial and aggregate levels and across different task difficulties. Figure S9 in the Supplementary Material shows how the control gains differ between Position and Velocity Control in our model across different difficulty levels.

We agree,with the reviewer’s overall point, that there are no doubt many models that can exhibit the variability observed in our experimental data, our simulations, or the reviewer’s simulations. Our study aimed to explore in detail not only the model’s ability to generate the variable behavior observed in experimental data, but also to match experimental results in terms of performance levels, gains, lags and correlations across a wide range of lambda values, wherein the only changes in the model were the lambda value and the control objective. Without the details of the reviewer’s model, we are unable to perform a detailed analysis of that model. Even so, we are not claiming that our model is the ‘ground truth,’ only that it is certainly a reasonable model, adopted from the literature, that provides intuitive and normative explanation about the performance of humans and monkeys over a range of metrics, system dynamics, and experimental conditions.

Finally, we understand the reviewer’s concern regarding whether the trial-by-trial identification of control strategy in Figure 8 suggests that (uninstructed) subjects constantly switch control objectives between Position and Velocity. Although it is not unreasonable to imagine that individuals would intuitively try different strategies between ‘keeping the cursor still’ and ‘keeping the cursor at the center’ across trials, we agree that it is generally difficult to determine such trial-to-trial changes, especially when the behavior lies somewhere in between the two control objectives. In such cases, as we originally discussed in the manuscript, an alternative explanation could be a mixed control objective that generates behavior at the intersection of Position and Velocity Control, i.e., between the two slopes in Figure 8. We believe, however, that our modeling approach is still helpful in cases where performance is predominantly based on Position or Velocity Control. After all, the motivation for this study was to parse neural data into two classes associated with each control objective to potentially better identify structure underlying these behaviors.

We clarified these points in the main text by adding further explanation in the Discussion section.

COMMENT: The reviewer suggested additional experiments, such as perturbation trials, that might be useful to further explore the separability of control objectives. They also suggested that we temper our conclusion that our approach can reliably discriminate amongst different control policies on individual trials. Finally, the reviewer suggested that we modify our Introduction and/or Discussion to note past human/monkey research as well as investigations of minimization of velocity-error versus position-error in the smooth pursuit system.

REPLY: We have expanded our simulations to investigate the effects of perturbation on the separability of different control objectives (Figure S10 in Supplementary Materials). We demonstrated that introducing perturbations more clearly differentiated between Position and Velocity Control. These results provide a good basis for further experimental verifications of the control objectives, but we defer these for future work.

We also appreciate the additional past work that bridges human and monkey research that the reviewer highlights, including the related discussions in the eye movement literature on position versus velocity control. We have modified our Introduction and Discussion accordingly.

Reviewer #3:

COMMENT: The reviewer asked whether the observed differences in behavior might be due to some other factors besides the control policy, such as motor noise or effort cost, and suggested that we more systematically ruled out that possibility.

REPLY: We appreciate and have heeded the reviewer’s suggestion. The revised manuscript now includes additional simulations in which the control objective was fixed to either Position or Velocity Control, while other parameters were systematically varied. Specifically, we examined the influence of the relative effort cost, the sensory delay, and motor noise, on performance. The results of these sensitivity analyses are presented in the Supplementary Material, Figures S4—6. In brief, we found that changing the relative effort cost, delay, or noise levels, mainly affected the success rate in performance (as expected), but did not affect the behavioral features originally associated with control objectives. We include a statement about this result in the main text with reference to the details provided in the Supplementary Material.

COMMENT: The reviewer questioned our choice of classification features (RMS position and velocity) and wondered if other features might yield better class separation, such as the hand/cursor gain. In a similar vein, reviewer 2 suggested in their recommendations that we examine the width of the autocorrelation function as a potentially better feature.

REPLY: We note first that our choice of cursor velocity and position stems from a dynamical systems perspective, where position-velocity phase-space analysis is common. However, we also explored other features as suggested. We found that they, too, exhibited overlap between the two different control objectives, and did not provide any significant improvement in classification performance (Figures S2 and S3; Supplementary Materials). Of course, that is not to say that a more exhaustive examination of features may not find ones that yield better classification performance than those we investigated, but that is beyond the scope of our study. We refer to this consideration of alternative metrics in the discussion.

COMMENT: The reviewer notes that “It seems that the classification problem cannot be solved perfectly, at least on a single-trial level.” To address this point, the reviewer suggested that we conduct additional simulations under the two different control objectives, and quantify the misclassifications.

REPLY: We appreciate the reviewer’s suggestion, and have conducted the additional simulations as suggested, the results of which are included in the revised manuscript.

COMMENT: “The problem of inferring the control objective is framed as a dichotomy between position control and velocity control. In reality, however, it may be a continuum of possible objectives, based on the relative cost for position and velocity. How would the problem differ if the cost function is framed as estimating a parameter, rather than as a classification problem?”

REPLY: A blended control strategy, formulated as a cost function that is a weighted combination of position and velocity costs, is indeed a possibility that we briefly discussed in the original manuscript. This possibility arises particularly for individuals whose performance metrics lie somewhere between the purely Position or purely Velocity Control. While our model allows for a weighted cost function, which we will explore in future work, we felt in this initial study that it was important to first identify the behavioral features unique to each control objective.

Response to Recommendations for the Authors:

Reviewer #1 (Recommendations For The Authors):

None beyond those stated above.

Reviewer #2 (Recommendations For The Authors):

COMMENT: Line 166 states "According to equation (1), this behavior was equivalent to reducing the sum (𝑝 + 𝑥) when 𝜆 increased, so as to prevent rapid changes in cursor velocity". This doesn't seem right. In equation 1, velocity (not acceleration) depends on p+x. So a large p+x doesn't create a "rapid change in cursor velocity", but rather a rapid change in cursor position.

REPLY: The reviewer is correct and we have corrected this misworded sentence; thank you for catching that.

COMMENT: The reviewer points out the potential confusion readers may have, given our unclear use of ‘control strategy’ vs. ‘control policy’ vs. ‘control objective’. The reviewer suggests that “It would be helpful if this could be spelled out early and explicitly. 'Control strategy' seems perilously close to 'control policy', and it would be good to avoid that confusion. The authors might prefer to use the term 'cost function', which is really what is meant. Or they might prefer 'control objective', a term that they introduce as synonymous with 'control strategy'.”

REPLY: We thank the reviewer for noting this ambiguity. We have clarified the language in the Introduction to explicitly note that by strategy, we mean the objective or cost function that subjects attempt to optimize. We then use ‘control objective’ consistently and removed the term ‘policy’ from the paper to avoid confusion. We also now use Position Control and Velocity Control as the labels for our two control objectives.

COMMENT: The reviewer notes that in Figure 2B and the accompanying text in the manuscript, we need to be clearer about what is being correlated; namely, cursor and hand position.

REPLY: Thank you for pointing out this lack of clarity, which we have corrected as suggested.

COMMENT: The reviewer questions our attribution of decreasing lag with task difficulty as a consequence of subjects becoming more attentive/responsive when the task is harder, and points out that our model doesn’t include this possible influence yet the model reproduces the change in lag. The reviewer suggests that a more likely cause is due to phase lead in velocity compared to position, with velocity likely increasing with task difficulty, resulting in a phase advance in the response.

REPLY: Our attribution of the decrease in lag with task difficulty being due to attention/motivation was a recapitulation of this point made in the paper by Quick et al. [2018]. But as noted by the reviewer, this potential influence on lag is not included in our model. Accordingly, the change in lag is more likely a reflection of the phase response of the closed loop system, which does change with task difficulty since the optimal gains depend upon the plant dynamics (i.e., the value of lambda). We have, therefore, deleted the text in question.

COMMENT: “The Methods tell us rather a lot about the dynamics of the actual system, and the cost functions are also well defined. However, how they got from the cost function to the controller is not described. I was also a bit confused about the controller itself. Is the 50 ms delay assumed when deriving the controller or only when simulating it (the text seems to imply the latter, which might make sense given that it is hard to derive optimal controllers with a hard delay)? How similar (or dissimilar) are the controllers for the two objectives? Is the control policy (the matrix that multiplies state to get u) quite different, or only subtly?”

REPLY: Thanks for pointing this out. For brevity, we had omitted the details and referred readers to the original paper (Todorov, 2005). However, we now revised the manuscript to now include all the details in the Methods section. Hence, the entire section on the model is new. This also necessitated updating all data figures (Figures 3, 4, 5, 6, 7, 8) as they contain modeling results.

COMMENT: “Along similar lines, I had some minor to moderate confusions regarding the OFC model as described in the main text. Fig 3 shows a model with a state estimator, but it isn't explained how this works. …Here it isn't clear whether there is sensory noise, or a delay. The methods say a delay was included in the simulation (but perhaps not when deriving the controller?). Noise appears to have been added to u, but I'm guessing not to x or x'? The figure legend indicates that sensory feedback contains only some state variables, and that state estimation is used to estimate the rest. Presumably this uses a Kalman filter? Does it also use efference copy, as would be typical? My apologies if this was stated somewhere and I missed it. Either way, it would be good to add a bit more detail to the figure and/or figure legend.”

REPLY: As the lack of detail evidently led to some confusion, we now more clearly spell out the details of the model in the Methods, including the state estimation procedure.

COMMENT: The reviewer wondered why we chose to plot mean velocity vs. mean position as in Figure 5, noting that, “ignoring scale, all scatter plots would be identical if the vertical axis were final position (because mean velocity determines final position). So what this plot is really examining is the correlation between final position and average position. Under position control, the autocorrelation of position is short, and thus final position tends to have little to do with average position. Under velocity control, the autocorrelation of position is long, and thus final position tends to agree with average position. Given this, why not just analyze this in terms of the autocorrelation of position? This is expected to be much broader under velocity control (where they are not corrected) than under position control (where they are, and thus disappear or reverse quickly). To me, thinking of the result in terms of autocorrelation is more natural.”

REPLY: The reviewer is correct that the scatter plots in Fig. 5 would be the same (to within a scale factor of the vertical axis) had we plotted final position vs. mean position instead of mean velocity vs. mean position as we did. Our preference for mean velocity vs. mean position stems from a dynamical systems perspective, where position-velocity phase-space analysis is common. We now mention these perspectives in the revised manuscript for the benefit of the reader.

As suggested, we also investigated the width of the (temporal) autocorrelation function (acf) of cursor position for 200 simulated position control trials and 200 simulated velocity control trials, at four different lambda values (50 simulated trials per lambda). Figs. S2A and B (Supplementary Materials) show example trials and histograms of the acf width, respectively. As the reviewer surmised, velocity control trials tend to have wider acfs than position control trials. However, as with the metrics we chose to analyze, there is overlap and there is no visible benefit for the classification.

COMMENT: “I think equation ten is incorrect, but would be correct if the identity matrix were added? Also, why is the last term of B set to 1/(Tau*M). What is M? Is it mass (which above was lowercase m)? If so, mass should also be included in A (it would be needed in two places in the last column). Or if we assume m = 1, then just ignore mass everywhere, including here and equation 5. Or perhaps I'm confused, and M is something else?”

REPLY: Thanks for pointing this out. The Matrix A shown in the paper is for the continuous-time representation of the model. However, as the reviewer correctly mentioned, for the discrete-time implementation of the model, a modification (identity matrix) was added in our simulations. We have now clarified this in the Methods section of the revised manuscript. Also, as correctly pointed out, M is the mass of the hand, which depending on whether the hand acceleration (d^2 p/dt^2) or hand force (F) are taken as the state, it can be included in the A matrix. In our case, the A matrix is modified according to the state vector. Similarly, the B matrix is also modified. This is now clarified in the Methods section of the manuscript.

Reviewer #3 (Recommendations For The Authors):

COMMENT: “Equations 4-8 are written in continuous time, but Equation 9 is written in discrete time. Then Equation 10 is in discrete time. This needs to be tidied up. … I would suggest being more detailed and systematic, perhaps formulating the control problem in continuous time and then converting to discrete time.”

REPLY: Thank you for this helpful suggestion. The model section in the Methods has been expanded to provide further details of the equation of motion, the discretization process, the control law calculation and the state estimation process.

COMMENT: “It seems slightly odd for the observation to include only position and velocity of the cursor. Presumably participants can also observe the state of their own hand through proprioception (even if it were occluded). How would it affect the model predictions if the other states were observable?”

REPLY: Thanks for pointing this out. We initially included only cursor position and velocity since we felt that was the most prominent state feedback, and the system is observable in that case. Nevertheless, we revised the manuscript and repeated all simulations using a full observability matrix. Our findings and conclusions remain unchanged. With the changes in the modeling, the figures were also updated (Fig.3, 4, 5, 6, 7, 8).

COMMENT: “It seems unnecessary to include the acceleration of the cursor in the formulation of the model. …the acceleration is not even part of the observed state according to line 668… I think the model could therefore be simplified by omitting cursor acceleration from the state vector.”

REPLY: We agree. We have simplified the model, and generated new simulations and figures. Our results and conclusions were unchanged by this modification. With the changes in the modeling, the figures were also updated (Fig.3, 4, 5, 6, 7, 8).

COMMENT: “In the cost function, it's not clear why any states other than position and velocity of the cursor need to have non-zero values. …The choice to have the cost coefficient for these other states be 1 is completely arbitrary… If the point is that the contribution of these other costs should be negligible, then why not just set them to 0?”

REPLY: We agree, and have made this change in the Methods section. Our findings and conclusions were unaffected.

COMMENT: “It seems that the cost matrices were specified after transforming to discrete-time. It is possible however (and perhaps recommended) to formulate in continuous time and convert to discrete time. This can be done cleanly and quite straightforwardly using matrix exponentials. Depending on the discretization timestep, this can also naturally lead to non-zero costs for other states in the discrete-time formulation even if they were zero under continuous time. … A similar comment applies to discretization of the noise.”

REPLY: Thanks for the suggestion. We have expanded on the discretization process in our Methods section, which uses a common approximation of the matrix exponentiation method.

COMMENT: “Most of the parameters of the model seem to be chosen arbitrarily. I think this is okay as the point is to illustrate that the kinds of behaviors observed are within the scope of the model. However, it would be helpful to provide some rationale as to how the parameters were chosen. e.g. Were they taken directly from prior literature, or were they hand-tuned to approximately match observed behavior?”

REPLY: We have revised the manuscript to more clearly note that the noise parameters, as well as parameters of the mechanical system (mass, muscle force, time scale, etc) in our model were taken from previous publications (Todorov, 2005, Cluff et al. 2019). As described in the manuscript, the parameter values of the cost function (Q matrix) were obtained by tuning the parameters to achieve a similar range of success rate with the model as observed in the experimental data. This is now clarified in the Methods section.

COMMENT: “The ‘true’ cost function for this task is actually a 'well' in position space - zero cost within the screen and very high cost elsewhere. In principle, it might be possible to derive the optimal control policy for this more veridical cost function. It would be interesting to consider whether or not this model might reproduce the observed behaviors.”

REPLY: This is indeed a very interesting suggestion, but difficult to implement based on the current optimal feedback control framework. However, this is interesting to consider in future work.

Minor Comments:

COMMENT: “In Figs 4 and 5, the data points are drawn from different conditions with varying values of lambda. How did the structure of this data depend on lambda? Might it be possible to illustrate in the figure (e.g. the shade/color of each dot) what the difficulty was for each trial?”

REPLY: We performed additional analyses to show the effects of task difficulty on the choice of control objective. Overall, we found that the main behavioral characteristics of the control objective remained fairly unchanged across different task difficulties or across time. The results of this analysis are included in Fig. S7 and S8 of the Supplementary Materials.

COMMENT: “Should mention trial duration (6s) in the main narrative of the intro/results.”

REPLY: We now mention this detail when we describe the task for the first time.

COMMENT: “As an alternative to training on synthetic data (which might not match behavior that precisely, and was also presumably fitted to subject data at some level) it might be worth considering to do a cross-validation analysis, i.e. train the classifier on subsets of the data with one participant removed each time, and classify on the held-out participant.”

REPLY: This is indeed a valid point. The main reason to train the classifier based on model simulations was two-fold: first, to have confidence in the training data, as the experimental data was limited and noisy, which would result in less reliable classifications; and second, the model simulations are available for different contexts and conditions, where experimental data is not necessarily available. The latter is a more practical reason to be able to identify control objectives for any subject (who received no instructions), without having to collect training data from matching control subjects who received explicit instructions. Nonetheless, we appreciate the reviewer’s recommendation and will consider that for our future studies.

COMMENT: “line 690 - Presumably the optimal policy was calculated without factoring in any delay (this would be tricky to do), but the 50ms delay was incorporated at the time of simulation?”

REPLY: The discretization of the system equations allowed us to incorporate the delay in the system dynamics and solve for the optimal controller with the delay present. This was done simply by system augmentation (e.g., Crevecoeur et al., 2019), where the states of the system in the current time-step were augmented with the states from the 5 preceding time-steps to form the new state vector x(t)_aug =[x(t) , x(t-1) , … , x(t-d) ]. Similarly, the matrices A, B, and H from the system dynamics could be expanded accordingly to form the new dynamical system:

$$x(t+1){aug} = A{aug} * x(t){aug} + B{aug} * u$$

Then, the optimal control was implemented on the new (augmented) system dynamics.

We have revised the manuscript (Methods) to clarify this issue.

Author Response

Reviewer #1 (Public Review):

Summary:

The present study's main aim is to investigate the mechanism of how VirR controls the magnitude of MEV release in Mtb. The authors used various techniques, including genetics, transcriptomics, proteomics, and ultrastructural and biochemical methods. Several observations were made to link VirR-mediated vesiculogenesis with PG metabolism, lipid metabolism, and cell wall permeability. Finally, the authors presented evidence of a direct physical interaction of VirR with the LCP proteins involved in linking PG with AG, providing clues that VirR might act as a scaffold for LCP proteins and remodel the cell wall of Mtb. Since the Mtb cell wall provides a formidable anatomical barrier for the entry of antibiotics, targeting VirR might weaken the permeability of the pathogen along with the stimulation of the immune system due to enhanced vesiculogenesis. Therefore, VirR could be an excellent drug target. Overall, the study is an essential area of TB biology.

Strengths:

The authors have done a commendable job of comprehensively examining the phenotypes associated with the VirR mutant using various techniques. Application of Cryo-EM technology confirmed increased thickness and altered arrangement of CM-L1 layer. The authors also confirmed that increased vesicle release in the mutant was not due to cell lysis, which contrasts with studies in other bacterial species.

Another strength of the manuscript is that biochemical experiments show altered permeability and PG turnover in the mutant, which fits with later experiments where authors provide evidence of a direct physical interaction of VirR with LCP proteins.

Transcriptomics and proteomics data were helpful in making connections with lipid metabolism, which the authors confirmed by analyzing the lipids and metabolites of the mutant.

Lastly, using three approaches, the authors confirm that VirR interacts with LCP proteins in Mtb via the LytR_C terminal domain.

Altogether, the work is comprehensive, experiments are designed well, and conclusions are made based on the data generated after verification using multiple complementary approaches.

Weaknesses:

The major weakness is that the mechanism of VirR-mediated EV release remains enigmatic. Most of the findings are observational and only associate enhanced vesiculogenesis observed in the VirR mutant with cell wall permeability and PG metabolism. The authors suggest that EV release occurs during cell division when PG is most fragile. However, this has yet to be tested in the manuscript - the AFM of the VirR mutant, which produces thicker PG with more pore density, displays enhanced vesiculogenesis. No evidence was presented to show that the PG of the mutant is fragile, and there are differences in cell division to explain increased vesiculogenesis. These observations, counterintuitive to the authors' hypothesis, need detailed experimental verification.

Response: We thank the reviewer for this comments. We would like to convince this reviewer about the fact that the VirR mutant is truly caring a more fragile PG. We will perfume additional experiments that would support this notion. We will determine the degree of PG release to the extracellular space and run additional mass spectrometry data on isolated PG.

Transcriptomic data only adds a little substantial. Transcriptomic data do not correlate with the proteomics data. It remains unclear how VirR deregulates transcription. TLCs of lipids are not quantitative. For example, the TLC image of PDIM is poor; quantitative estimation needs metabolic labeling of lipids with radioactive precursors. Further, change in PDIMs is likely to affect other lipids (SL-1, PAT/DAT) that share a common precursor (propionyl- CoA).

Response: We agree with the reviewer that TLC analysis is not quantitative. Additional TLCs will be run to investigate other lipids sharing common precursors. At the present time, we can not run radioactive experiments on the lab.

The connection of cholesterol with cell wall permeability is tenuous. Cholesterol will serve as a carbon source and contribute to the biosynthesis of methyl-branched lipids such as PDIM, SL-1, and PAD/DAT. Carbon sources also affect other aspects of physiology (redox, respiration, ATP), which can directly affect permeability and import/export of drugs. Authors should investigate whether restoration of the normal level of permeability and EV release is not due to the maintenance of cell wall lipid balance upon cholesterol exposure of the VirR mutant.

Response: We concur with the reviewer that cholesterol as sole carbon source is introducing many changes in Mtb cells beside permeability. Our central hypothesis regarding this data is that cholesterol will make Mtb cell membrane less fluid and this fact will make Ev release to be reduced. We will try to measure membrane fluidity in the presence and absence of cholesterol. However, permeability changes in Mtb cells can be manifested at different levels of the cell envelope. This would suggest that the increased permeability observed in the VirR mutant, could be different than that of observed upon TRZ treatment. The main point on this is that vesiculogenesis could be a general process responding to changes in permeability regardless of the cell envelope compartment affected. We need to define experiments here, but we will try to demonstrate this.

Finally, protein interaction data is based on experiments done once without statistical analysis. If the interaction between VirR and LCP protein is expected on the mycobacterial membrane, how the SPLIT_GFP system expressed in the cytoplasm is physiologically relevant. No explanation was provided as to why VirR interacts with the truncated version of LCP proteins and not with the full-length proteins.

Response: Split-GFP has been previously used with cell membrane proteins with success. However, we will repeat the experiments and perform statistics.

Reviewer #2 (Public Review):

Summary:

In this work, Vivian Salgueiro et al. have comprehensively investigated the role of VirR in the vesicle production process in Mtb using state-of-the-art omics, imaging, and several biochemical assays. From the present study, authors have drawn a positive correlation between cell membrane permeability and vasculogenesis and implicated VirR in affecting membrane permeability, thereby impacting vasculogenesis.

Strengths:

The authors have discovered a critical factor (i.e. membrane permeability) that affects vesicle production and release in Mycobacteria, which can broadly be applied to other bacteria and may be of significant interest to other scientists in the field. Through omics and multiple targeted assays such as targeted metabolomics, PG isolation, analysis of Diaminopimelic acid and glycosyl composition of the cell wall, and, importantly, molecular interactions with PG-AG ligating canonical LCP proteins, the authors have established that VirR is a central scaffold at the cell envelope remodelling process which is critical for MEV production.

Response: We thank the reviewer for this kind words.

Weaknesses:

Throughout the study, the authors have utilized a CRISPR knockout of VirR. VirR is a non-essential gene for the growth of Mtb; a null mutant of VirR would have been a better choice for the study.

Response: We thank the reviewer for bringing up this issue. Contrary to predictions, we believe that virR is an essential gene as we have tried to delete it several times with no success. We used in the study a transposon mutant and its complementing strain since they have been the base of previous studies to establish their genetic implications in vesiculogenesis in Mtb. The choice of CRISPRi was run similar experiments in a background different from transposon mutagenesis. Our data, support similar phenotypes in term of vesicle release.

Author Response

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

Reviewer #1

More details about the classification and how it is trained

We included a sentence in the introduction to clarify which data we are using: "In order to demonstrate this improvement, we apply our methods to two classification datasets: a synthetic dataset and a public clinical dataset where the predicted outcome is the survival of the patient"

And about how the classifier is trained in the "Results" section: "we used the default parameters of the classifier, since our focus is comparing the different imputation methods"

Availability of the code

Now the code is publicly available in a github repository https://github.com/AstraZeneca/dpp_imp/ (see Availability of Data and Code section)

Reviewer #2

Clarifying that Determinantal Point Processes and their deterministic version have been introduced before but are applied for the first time for data imputation in this work:

We added explanation in the 6th paragraph of the introduction that we use pre-existing DPP and deterministic-DPP algorithms for our imputation methods and include the references to avoid confusion

We also added a paragraph at the end of the introduction to summarize this work's contribution

Explaining the claim about the computational advantage of using quantum determinantal point processes for the imputation methods:

In the fourth paragraph of the "Discussion" section (page 8), we give an imputation example by numerically comparing the classical and quantum algorithms running time for DPP sampling, which shows the advantage of using the quantum algorithm.

Regarding running time for classical DPP and quantum DPP sampling algorithms:

We included Table VIII (page 13) that compares the preprocessing and sampling complexities for both classical and quantum DPP algorithms, we consider the case where we sample d rows from an (n,d) matrix and n=O(d) which is usually the case for our DPP-Random Forest algorithm

We added some details regarding the quantum advantage in the first paragraph of page 12

Regarding the comment about the modest improvement of the DPP methods and questions about their practical benefit:

As mentioned in the third paragraph of the "Discussion" section, we point out that the consistency of the improvement and the removal of variance as a result of using the DPP and deterministic DPP methods make our methods very beneficial to use on clinical data. Further exploration with different data sets can provide a more result in a more complete understanding of the practical advantages of the methods

Algorithmic complexity of the deterministic DPP algorithm:

Detailed in the last sentence of the "Determinantal Point Processes" subsection of the "Methods" section: O(N^2 d) for the preprocessing step and O(Nd^3) for the sampling step

Running time for the quantum deterministic DPP sampling and how it is done in practice:

While it is difficult to assess the real running time for the quantum detDPP algorithm for large circuits (100 or more qubits), due to the unavailability of such devices, we give more details about our practical implementation in the last paragraph of the "Methods" section. In our case (up to 10 qubits) we used 1000 shots to sample the highest probability elements.

On which quantum simulator was used

We point out in the first paragraph of page 5 that we employ the qiskit noiseless simulator

Author Response

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

eLife assessment

This important study identifies the gene mamo as a new regulator of pigmentation in the silkworm Bombyx mori, a function that was previously unsuspected based on extensive work on Drosophila where the mamo gene is involved in gamete production. The evidence supporting the role of Bm-nano in pigmentation is convincing, including high-resolution linkage mapping of two mutant strains, expression profiling, and reproduction of the mutant phenotypes with state-of-the-art RNAi and CRISPR knock-out assays. While the discussion about genetic changes being guided or accelerated by the environment is extremely speculative and has little relevance for the findings presented, the work will be of interest to evolutionary biologists and geneticists studying color patterns and evolution of gene networks.

Response: Thank you very much for your careful work. In the revised version, we conducted a comparative genomic analysis of the upstream regions of the Bm-mamo gene in 51 wild silkworms and 171 domesticated local silkworms. The analysis of nucleotide diversity (pi) and the fixation index (FSTs) of the Bm-mamo genome sequences in the wild and domesticated silkworm populations were also performed. The results showed that the Bm-mamo genome sequence of local silkworms was relatively conserved, while the upstream sequence of wild silkworms exhibited high nucleotide diversity. This finding suggested a high degree of variability in the regulatory region of the Bm-mamo gene, in wild strains. Additionally, the sequence in this region may have been fixed by domestication selection. We have optimized the description in the discussion section.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This papers performs fine-mapping of the silkworm mutants bd and its fertile allelic version, bdf, narrowing down the causal intervals to a small interval of a handful of genes. In this region, the gene orthologous to mamo is impaired by a large indel, and its function is later confirmed using expression profiling, RNAi, and CRISPR KO. All these experiments are convincingly showing that mamo is necessary for the suppression of melanic pigmentation in the silkworm larval integument.

The authors also use in silico and in vitro assays to probe the potential effector genes that mamo may regulate.

Strengths:

The genotype-to-phenotype workflow, combining forward (mapping) and reverse genetics (RNAi and CRISPR loss-of-function assays) linking mamo to pigmentation are extremely convincing.

This revision is a much improved manuscript and I command the authors for many of their edits.

Response: Thank you very much for your careful work. With the help of reviewers and editors, we have revised the manuscript to improve its readability.

I find the last part of the discussion, starting at "It is generally believed that changes in gene expression patterns are the result of the evolution of CREs", to be confusing.

In this section, I believe the authors sequentially:

• emphasize the role of CRE in morphological evolution (I agree)

• emphasize that TF, and in particular their own CRE, are themselves important mutational targets of evolution (I agree, but the phrasing need to insist the authors are here talking about the CRE found at the TF locus, not the CRE bound by the TF).

• use the stickleback Pel enhancer as an example, which I think is a good case study, but the authors also then make an argument about DNA fragility sites, which is hard to connect with the present study.

• then continue on "DNA fragility" using the peppered moth and butterfly cortex locus. There is no evidence of DNA fragility at these loci, so the connection does not work. "The cortex gene locus is frequently mutated in Lepidoptera", the authors say. But a more accurate picture would be that the cortex locus is repeatedly involved in the generation of color pattern variants. Unlike for Pel fragile enhancer, we don't know if the causal mutations at this locus are repeatedly the same, and the haplotypes that have been described could be collateral rather than causal. Overall, it is important to clarify the idea that mutation bias is a possible factor explaining "genetic hotspots of evolution" (or genetic parallelism sensu 10.1038/nrg3483), but it is also possible that many genetic hotspots are repeated mutational targets because of their "optimal pleiotropy" (e.g. hub position in GRNs, such as mamo might be), or because of particularly modular CRE region that allow fine-tuning. Thus, I find the "fragility" argument misleading here. In fact the finding that "bd" and "bdf" alleles are different in nature is against the idea of a fragility bias (unless the authors can show increased mutation rates at this locus in a wild silkmoth species?). These alleles are also artificially-selected ie. they increased in frequency by breeding rather than natural selection in the wild, so while interesting for our understand of the genotype-phenotype map, they are not necessarily representative of the mutations that may underlie evolution in the wild.

Response: Thank you very much for your careful work. DNA fragility is an interesting topic, but some explanations for DNA fragility are confusing. One study measured the rate of DNA double-strand breaks (DSBs) in yeast artificial chromosomes (YACs), which are chromosomes containing marine Pel that broke ~25 to 50 times more frequently than did the control. These authors believe that the increase in the mutation rate is caused by DNA sequence characteristics, particularly TG-dinucleotide repeats. Moreover, they found that adding a replication origin on the opposite side of Pel did not cause the fungus to switch fragile, making the forward sequence stable and the reverse complement fragile. Thus, Pel fragility is also dependent on the direction of DNA replication. In summary, they suggested that the special DNA sequence is the cause of DNA fragility. In addition, the sequence features associated with DNA fragility in the Pel region are also found in thousands of other positions in the stickleback and human genomes (Xie KT et al, 2019, science).

In yeast artificial chromosomes (YACs), the characteristics of DNA sequences, such as TG-dinucleotide repeat sequences, may be important reasons for DNA fragility, and these breaks occur during DNA replication. However, the inserted sequence of YAC often undergoes deletion or recombination during cultivation and passage. In addition, yeast is a single-celled organism. Therefore, the results in yeast cannot represent the situation in multicellular organisms. If multicellular organisms are like this, there are several issues as follows:

(1) The DNA replication process occurs separately in different multicellular organisms. Because DNA breakage and repair are independent, they can lead to the presence of different alleles in different cells. This can potentially lead to the occurrence of extensive chimeric organisms. However, we have not found such a situation in the genome sequencing of many multicellular organisms.

(2) If the DNA sequence, TG-dinucleotide repeats, is the determining factor, the mutations near the sequence lose their strong correlation with environmental changes. The researchers conducted yeast artificial chromosome experiments in the same environment and found that the frequency of DNA breaks containing TG dinucleotide repeat sequences was 25 to 50 times greater than that of the control group. This means that, whether in the marine population or the lake population, this part of the sticklebacks’ genome has undergone frequent mutations. However, according to related research, populations of lake sticklebacks, rather than marine populations, often exhibit a decrease in the pelvic phenotype.

(3) Researchers have found thousands of loci in the genome of sticklebacks and humans that contain such sequences (TG-dinucleotide repeats). This means that thousands of sites undergo frequent mutations during DNA replication. Unless these sites do not possess functionality, they will have some impact on the organism, even causing damage. Even if they are not functional sequences, these sequences will gradually be discarded or replaced during frequent mutations rather than being present in large quantities in the genome.

Therefore, the study of DNA fragility in yeast cannot explain the situation in multicellular organisms.

As you noted, we want to express that the frequent variation in the cortex gene should be regulated by targeted regulation involving the GRN in Lepidoptera. In addition, studies on specific epigenetic modifications discovered through the referenced fragile DNA sites suggest that DNA fragility is not determined by the DNA sequence (Ji F, 2020, Cell Res) but rather by other factors, such as epigenetic factors. The sequence features discovered at fragile DNA sites are traces of frequent mutations, not causes.

In this revision, we analyzed the nucleotide diversity of the mamo genome in 51 wild and 171 domestic silkworms. We found high nucleic acid diversity from the third exon to the upstream region of this gene in wild silkworms. We randomly selected 12 wild silkworms and 12 domestic silkworms and compared their upstream sequences to approximately 1 kb. In wild silkworms, there is significant diversity in their upstream sequences. In domestic silkworms, the sequences are highly conserved, but in some silkworms, a long interspersed nuclear element (LINE) is inserted. This finding suggested that there is frequent variation in the sequence of this region in wild silkworms, while fixation occurs in domesticated silkworms. These genomic data are sourced from the pangenome of silkworms (Tong X, 2022, Nat Commun.). In the pangenomic research, 1078 strains (205 local strains, 194 improved strains, 632 mutant strains, and 47 wild silkworms), which included 545 third-generation sequencing genomes, were obtained. An online website was built to utilize these data (http://silkmeta.org.cn/). We warmly welcome you to use these data.

In summary, for clearer expression, we have rewritten this section.

Xie KT, Wang G, Thompson AC, Wucherpfennig JI, Reimchen TE, MacColl ADC, Schluter D, Bell MA, Vasquez KM, Kingsley DM. DNA fragility in the parallel evolution of pelvic reduction in stickleback fish. Science. 2019 Jan 4;363(6422):81-84. doi: 10.1126/science.aan1425.

Ji F, Liao H, Pan S, Ouyang L, Jia F, Fu Z, Zhang F, Geng X, Wang X, Li T, Liu S, Syeda MZ, Chen H, Li W, Chen Z, Shen H, Ying S. Genome-wide high-resolution mapping of mitotic DNA synthesis sites and common fragile sites by direct sequencing. Cell Res. 2020 Nov;30(11):1009-1023. doi: 10.1038/s41422-020-0357-y.

Tong X, Han MJ, Lu K, Tai S, Liang S, Liu Y, Hu H, Shen J, Long A, Zhan C, Ding X, Liu S, Gao Q, Zhang B, Zhou L, Tan D, Yuan Y, Guo N, Li YH, Wu Z, Liu L, Li C, Lu Y, Gai T, Zhang Y, Yang R, Qian H, Liu Y, Luo J, Zheng L, Lou J, Peng Y, Zuo W, Song J, He S, Wu S, Zou Y, Zhou L, Cheng L, Tang Y, Cheng G, Yuan L, He W, Xu J, Fu T, Xiao Y, Lei T, Xu A, Yin Y, Wang J, Monteiro A, Westhof E, Lu C, Tian Z, Wang W, Xiang Z, Dai F. High-resolution silkworm pan-genome provides genetic insights into artificial selection and ecological adaptation. Nat Commun. 2022 Sep 24;13(1):5619. doi: 10.1038/s41467-022-33366-x.

Lu K, Pan Y, Shen J, Yang L, Zhan C, Liang S, Tai S, Wan L, Li T, Cheng T, Ma B, Pan G, He N, Lu C, Westhof E, Xiang Z, Han MJ, Tong X, Dai F. SilkMeta: a comprehensive platform for sharing and exploiting pan-genomic and multi-omic silkworm data. Nucleic Acids Res. 2024 Jan 5;52(D1):D1024-D1032. doi: 10.1093/nar/gkad956.

Curiously, the last paragraph ("Some research suggests that common fragile sites...") elaborate on the idea that some sites of the genome are prone to mutation. The connection with mamo and the current article are extremely thin. There is here an attempt to connect meiotic and mitotic breaks to Bm-mamo, but this is confusing: it seems to propose Bm-mamo as a recruiter of epigenetic modulators that may drive higher mutation rates elsewhere. Not only I am not convinced by this argument without actual data, but this would not explain how the mutations at the Bm-mamo itself evolved.

Response: Thank you very much for your careful work. This section mainly illustrates that DNA fragility is not determined by sequence but is regulated by other factors in animals. In fruit flies, they found that mamo is an important candidate gene for recombination hotspot setting in meiosis. First, we evaluated PRDM9, which plays an important role in setting recombination hotspots during meiosis. Our purpose in mentioning this information is to illustrate that chromosome recombination is a process of programmed double strand breaks and to answer another reviewer's question about programmed events in the genome. In summary, we suggest that some variations in DNA sequences are procedural results. We have optimized the description of this section in this version.

On a more positive note, I find it fascinating that the authors identified a TF that clearly articulates or orchestrate larval pattern development, and that when it is deleted, can generate healthy individuals. In other words, while it is a TF with many targets, it is not too pleiotropic. This idea, that the genetically causal modulators of developmental evolution are regulatory genes, has been described elsewhere (e.g. Fig 4c in 10.1038/s41576-020-0234-z, and associated refs). To me, the beautiful findings about Bm-mamo make sense in the general, existing framework that developmental processes and regulatory networks "shape" the evolutionary potential and trajectories of organisms. There is a degree of "programmability" in the genomes, because some loci are particularly prone to modulate a given type of trait. Here, Bm-mamo, as a potentially regulator of both CPs and melanin pathway genes, appear to be a potent modulator of epithelial traits. Claiming that there are inherent mutational biases behind this is unwarranted.

Response: Thank you very much for your careful work. I completely agree with your statement that the genome exhibits a certain degree of programmability. On the one hand, some transcription factors can precisely control the spatiotemporal expression levels of some structural genes (such as pigment synthesis genes). On the other hand, these transcription factors are also subject to strict expression regulation. Because the color pattern is complex, changes in single or minority structural genes result in incomplete or imprecise changes in coloring patterns. Nevertheless, several regulatory factors can regulate multiple downstream target genes. Changes in their expression patterns can lead to holistic and significant changes in color patterns. There are long intergenic regions upstream of many important transcription factors, dozens of kilobase pairs (Kb) to hundreds of Kb, which may contain many different regulatory elements for better control of their expression patterns. Therefore, gene regulatory networks can directly regulate transcription factors to modulate a given type of trait. Transcription factors and their downstream target genes can form a functional module, which is similar to a functional module in software or operating systems. This regulation of transcription factors is simpler in terms of steps, which are similar to a single click switch button. The gene regulatory network regulates these modules in response to environmental changes and is widely recognized.

Some people do not agree that genetic variations can also be regulated. They claim that this is completely random. The infinite monkey theorem (Félix-Édouard-Justin-Émile Borel, 1909) states that if an infinite number of monkeys were given typewriters and an infinite amount of time, they would eventually produce the complete works of Shakespeare. Although this theory advocates randomness on the surface, its conclusions are full of inevitability (tail event). In nature, some things we observe do not have obvious regularity because they involve relatively complex factors, and the underlying logic is obscure and difficult to understand. We often name them random. However, as we gradually understand the logic behind this complex event, we can also recognize the procedural nature of this randomness.

Previously, chromosomal recombination during meiosis was believed to be a random event. However, currently, it is believed that the process is procedural. The occurrence of meiotic recombination mentioned earlier indicates that the genome has the ability to self-set the position of double-strand breaks to form new allelic forms. Because meiotic recombination is programmed, transcription factors that recognize DNA sites, enzymes that cleave double strands, and DNA repair systems exist, programming can also introduce genetic variation. A study in plants has provided insights into this programmed mutation (Monroe JG, 2023, nature). Frequent changes in the expression patterns of some transcription factors occur between and/or within species. In this article, we only discuss the possible reasons for variations in the expression patterns of some transcription factors in a general manner and simple reasoning. We have added an analysis of the response of wild silkworms and improved the relevance of the discussion.

Monroe JG, Srikant T, Carbonell-Bejerano P, Becker C, Lensink M, Exposito-Alonso M, Klein M, Hildebrandt J, Neumann M, Kliebenstein D, Weng ML, Imbert E, Ågren J, Rutter MT, Fenster CB, Weigel D. Mutation bias reflects natural selection in Arabidopsis thaliana. Nature. 2022 Feb;602(7895):101-105. doi: 10.1038/s41586-021-04269-6. Epub 2022 Jan 12. Erratum in: Nature. 2023 Aug;620(7973):

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

• Please structure your Discussion with section headers.

Response: Thank you very much for your careful work. We have added relevant section headers.

• As explained in my public review, I found the two last sections of the Discussion to be dispersed and confusing. I also must say that I carefully read the Response to Reviewers on this, which helped me to better understand the authors' intentions here. Please consider the revision of this Discussion as this feels extremely speculative difficult to connect with Bm-mamo.

Response: Thank you very much for your careful work. We have rewritten this part of the content.

• typo: were found near the TTS of yellow --> TSS

Response: Thank you very much for your careful work. We have made these modifications.

• l. 234 :"expression level of the 18 CP genes in the integument". Consider adding a mention of Figure 7 here, as only Fig. S10 is cited here.

Response: Thank you very much for your careful work. We have made these modifications.

• Editorial comment on the second half of the Abstract:

Wu et al : "We found that Bm-mamo can comprehensively regulate the expression of related pigment synthesis and cuticular protein genes to form color patterns. This indicates that insects have a genetic basis for coordinate regulation of the structure and shape of the cuticle, as well as color patterns. This genetic basis provides the possibility for constructing the complex appearances of some insects. This study provides new insight into the regulation of color patterns."

I respectfully suggest a more accurate rephrasing, where the methods are mentioned, and where the logical argument is more straightforward. For example

"Using RNAi and CRISPR we show that Bm-mamo is a repressor or dark melanin patterns in the larval epithelium. Using in-vitro binding assays and gene expression profiling in wild-type and mutant larvae, we also show that Bm-mamo likely regulate the expression of related pigment synthesis and cuticular protein genes in a coordinated manner to mediate its role in color pattern formation. This mechanism is consistent with a dual role of this transcription factor in regulating both the structure and shape of the cuticle and pigments that are embedded within it. This study provides new insight into the regulation of color patterns as well as in the construction more complex epithelial features in some insects."

I hope this let the ideas of the original version transpire as the authors intended.

Response: Thank you very much for your careful work. We have made these modifications.

Author Response

We would like to thank the reviewers for their thoughtful feedback on our work. One important point that they bring up is a potential issue with our method for accounting for excess NCO events that are detected due to increased marker resolution in the introgressed regions. The method we chose was to simulate average sized NCO tracts over both introgressed and non-introgressed windows to determine the expected increase in NCO detection due to marker density. We then took that expected increase and used it to correct our per-window NCO counts in all windows. We used these corrections for all results and analysis involving genomic windows (maps and genomewide comparisons) but did not include them when focusing on introgression-specific characteristics (e.g. analyzing fine-scale sequence differences around NCO tracts in introgressed regions). We chose this method based on previous work in the field and after some additional analyses on our own data that we did not include in the final manuscript. We will attempt to better communicate our decision making process and include some of the exploratory results that guided us in our revised manuscript. We look forward to responding to all comments and highlighting additional aspects of our findings that we think are of interest to the evolution and recombination communities, including significant changes to the recombination landscape between closely related strains and the impact of introgression on allelic shuffling.

Author Response

Reviewer #1 (Public Review):

Summary:

The study investigates the role of cylicin-1 (CYLC1) in sperm acrosome-nucleus connections and its clinical relevance to male infertility. Using mouse models, the researchers demonstrate that cylicin-1 is specifically expressed in the post acrosomal sheath-like region in spermatids and plays a crucial role in mediating acrosome-nucleus connections. Loss of CYLC1 results in severe male subfertility, characterized by acrosome detachment and aberrant head morphology in sperm. Further analysis of a large cohort of infertile men reveals CYLC1 variants in patients with sperm head deformities. The study provides valuable insights into the role of CYLC1 in male fertility and proposes CYLC1 variants as potential risk factors for human male infertility, emphasizing the importance of mouse models in understanding the pathogenicity of such variants.

We appreciate the comprehensive summary of reviewer 1.

Strengths:

This article demonstrates notable strengths in various aspects. Firstly, the clarity and excellent writing style contribute to the accessibility of the content. Secondly, the employed techniques are not only relevant but also complementary, enhancing the robustness of the study. The precision in their experimental design and the meticulous interpretation of results reflect the scientific rigor maintained throughout the study. Furthermore, the decision to create a second mouse model with the exact CYLC1 mutation found in humans adds significant qualitative value to the research. This approach not only validates the clinical relevance of the identified variant but also strengthens the translational impact of the findings.

We appreciate the positive comment of reviewer 1.

Weaknesses:

There are no obvious weaknesses. While a few minor refinements, as suggested in the recommendations to authors, could enhance the overall support for the data and the authors' messages, these suggested improvements in no way diminish the robustness of the already presented data.

In the recommendation for the authors, reviewer 1 mentioned a recent study (Schneider et al., eLife, 2023) showing that Cylc1-KO mice exhibits a reduced sperm count, an observation not noted in our current study. We would like to comment that that main and most important phenotype of Cylc1-KO mice in both studies is quite similar, including male subfertility and abnormal head morphology. We think the different targeting strategy and mouse strain may cause this discrepancy. In Schneider’s and our current studies, the total motility abnormality of Cylc1-KO mice are not observed. We appreciate the suggestion of reviewer 1 to further examine the detailed parameters of motility such as VCL, VSL, and ALH. Given that the head deformation is the most obvious phenotype of Cylc1-KO mice and the focus of our study, we feel sorry that this detailed analysis of sperm motility was not performed in the current stage. Reviewer 1 also asked whether Cylc1-KO female mice are fertile or not. Given that Cylc1 is an X chromosome gene and Cylc1-KO (Cylc1-/Y) mice are severely subfertile, we do not obtain enough Cylc1-KO female mice to examine their fecundity. We also would like to thank reviewer 1 to point out several inaccurate descriptions.

Reviewer #2 (Public Review):

Summary:

To verify the function of PT-associated protein CYLC1, the authors generated a Cylc1-KO mouse model and revealed that loss of cylicin-1 leads to severe male subfertility as a result of sperm head deformities and acrosome detachment. Then they also identified a CYLC1 variant by WES analysis from 19 infertile males with sperm head deformities. To prove the pathogenicity of the identified mutation site, they further generated Cylc1-mutant mice that carried a single amino acid change equivalent to the variant in human CYLC1. The Cylc1-mutant mice also exhibited male subfertility with detached acrosomes of sperm cells.

We appreciate the comprehensive summary of reviewer 2.

Strengths:

The phenotypes observed in the Cylc1-KO mice provide strong evidence for the function of CYLC1 as a PT-associated protein in spermatogenesis and male infertility. Further mechanistic studies indicate that loss of cylicin-1 in mice may disrupt the connections between the inner acrosomal membrane and acroplaxome, leading to detached acrosomes of sperm cells.

We appreciate the positive comment of reviewer 2.

Weaknesses:

The authors identified a missense mutation (c.1377G>T/p. K459N) from 19 infertile males with sperm head deformities. The information for the variant in Table 1 is insufficient to determine the pathogenicity and reliability of the mutation site. More information should be added, including all individuals in gnomAD, East Asians in gnomAD, 1000 Genomes Project for allele frequency in the human population; MutationTaster, M-CAP, FATHMM, and more other tools for function prediction. Then, the expression of CYLC1 in the spermatozoa from men with CYLC1 mutation should be explored by qPCR, Western blot, or IF staining analyses. Although 19 infertile males were found carrying the same missense mutation (c.1377G>T/p. K459N), their phenotypes are somewhat different. For example, sperm concentrations for individuals AAX765, BBA344, and 3086 are extremely low but this is not observed in other infertile males. Then, progressive motility for individuals AAT812, 3165, 3172, 3203, and 3209 are extremely low but this is also not observed in other infertile males. It is worth considering why different phenotypes are observed in probands carrying the same mutation.

We appreciate the suggestion of reviewer 2. First, Table 1 shows the information of the variant identified in CYLC1 gene, including allele frequency in gnomAD and functional prediction by SIFT, PolyPhen-2, and CADD. Given that mutant mice is a gold standard to confirm the pathogenicity of a variant, we generate Cylc1-mutant mice and Cylc1-mutant mice exhibit male subfertility with sperm acrosome detachment. The animal evidence is much more solid than bioinformatics prediction to confirm the pathogenicity of the identified variant in the CYLC1 gene. Second, the expression of CYLC1 in the spermatozoa from patients have been examined by IF staining (Fig. 5B). Unfortunately, the patients declined to continue in the project to donate more semen for qPCR and Western blot analyses. Third, the reviewer 2 asks why not all patients with CYLC1 gene mutation show the identical phenotype. Although some patients exhibit low sperm count or reduced motility, sperm head deformities are the shared phenotype of 19 patients. Many factors, such as way of life, may affect sperm quality. Perfectly identical phenotype of all 19 patients carrying the CYLC1 mutation is idealistic and will not always happen in clinical diagnosis. We also appreciate other suggestions from reviewer 2.

Author Response

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

We appreciate the insightful feedback provided by the editors and reviewers who have recognized the novelty of our study. We have mapped the spatial distribution of six endogenous somatic histone H1 variants within the nuclei of several human cell lines using specific antibodies, which strongly suggest functional differences between variants. We are submitting a revised version of the manuscript to accommodate the reviewers comments and recommendations.

Reviewer #1 (Recommendations For The Authors):

Minor Comments:

(1) In Figure 1C, since H1.4 is uniformly distributed among the four sections (A1-A4), its levels are not expected to be significant among the four sections as depicted. Even the violin plots shown do not seem to be significantly different from each other. This requires an explanation.

We agree with this reviewer that significant differences of H1.4 abundance within areas A1 to A4 seem to not exist, either looking at the images or the data violin plots, as discussed in the manuscript. Nonetheless, statistical testing gave this as significant, due to small differences and the elevated sample N of the analysis. It is clear that H1.4 does not show a relevant peripheral enrichment as shown for the other variants.

(2) At the end, it would be better to include a figure panel depicting chart/table/pictorial representation, depicting the summary of the work done with respect to all the histone variants, as there are several histone H1 variants studied under different conditions and contexts.

A table summarizing the location and characteristics of the different H1 variants has been included in the manuscript (Figure 6).

Reviewer #2 (Recommendations For The Authors):

(1) The authors may consider adding controls for the specificity of the antibodies used for the studies. While the antibodies used here are commercial, it does not guarantee the quality for immunofluorescence, especially considering their unreliability in the past. The authors may consider including peptide/ recombinant protein-based adsorption controls in addition to knockdown or knockout controls. Having these data will strengthen the exciting observations presented in this MS and significantly increase the impact of the presented findings.

We totally agree with the reviewers that the use of commercially available antibodies does not guarantee their quality and specificity. As this issue was crucial for our studies, we extensively assayed performance and specificity of the antibodies, using different approaches. The validations were shown in our previous publications where these antibodies where successfully used for ChIP-seq (Serna-Pujol et al. 2022 NAR 50:3892; Salinas-Pena et al. 2024 NAR doi 10.1093/nar/gkae014). In summary, performance of H1.0 (05-629l, Millipore), H1.2 (ab4086, abcam), H1.4 (702876; Invitrogen), H1.5 (711912, Invitrogen) and H1X (ab31972; abcam) antibodies was tested by Western-Blot, ChIP and proteomic analyses (all the results are included in Supplem. Figure 1 in Serna-Pujol et al. 2022 NAR 50:3892). Concretely, we tested specificity using inducible KDs for the depletion of each of the somatic H1 variants in T47D. We also checked that the antibodies did not recognize additional H1 variants using recombinant proteins or cell lines naturally lacking some of the variants. All the experiments confirmed that antibodies were variant-specific. In addition, when the corresponding epitope was absent, the antibodies did not gain new cross-reactivity with other variants. More recently, validation of the specificicity of the H1.3 antibody (ab203948) was performed following the same experimental approaches described for the rest of antibodies (Supplem. Figure 1 in Salinas-Pena et al. 2024 NAR doi 10.1093/nar/gkae014).

(2) Histone H1 is overexpressed in several cancers. While the authors do not use an overexpression strategy, the cells used in this study are all cancer cell lines. The study would benefit greatly if some of the findings- primarily regarding the spatial distribution of the H1 were to reproduce in non-tumorigenic, diploid cells.

We have also studied and discussed the spatial distribution of H1 variants in nontumorogenic cell lines 293T and IMR-90, and we have added this in the revised manuscript (Figure 5D and Figure 5-figure supplement 3). The nuclear radiality of H1.4 in 293T cells is also shown (Figure 5-figure supplement 4A).

Reviewer #3 (Recommendations For The Authors):

This is an interesting paper that provides convincing evidence of distinct distributions to individual histone H1 variants. There are several aspects of the study that leave me unconvinced that the study accurately captures histone H1 variant distributions.

(1) Antibody accessibility: (see PMID: 32505195). One means to address this is to express a fluorescent protein-tagged version of histone H1 and demonstrate that the antibody can detect that tagged version of histone H1 independent of its location in the nucleus. In general, these FP-tagged H1s show a much more even distribution than what is observed here. Of course, that could reflect artifacts related to the fusion or the expression of the exogenous construct. However, even if all of the above are true, this will test the ability of the antibodies to recognize their epitopes in different chromatin environments. The fluorescent protein tag enables unambiguous knowledge of the presence or absence of the H1 histone.

We have used cells expressing HA-tagged H1.0 variant and performed immunofluorescence with HA and H1.0 antibody to investigate co-localization, to test whether an H1 antibodiy recognize all the tagged protein in different chromatin environments or irrespective of its location in the nucleus. A very high correlation between the two antibodies has been found (Figure 1-figure supplement 1B).

(2) At high concentrations, the fluorescence signal intensity can be quenched. For example, this is common with high-affinity histone H3 serine 10 phosphorylation antibodies in late interphase/prophase nuclei. The artifact can be minimized by serial dilution of the antibody and identifying the minimum usable concentration for immunofluorescence. While I am not certain that this is taking place here, the rate and manner that the intensity drops off from the periphery in the peripheral H1 variant distribution are very similar in appearance. There are biological explanations related to constraints on diffusion that one could imagine also explaining the data so I'm not stating that this must be an artefact. However, I am concerned that it might be. An improved staining may reveal the same result but more convincingly.

We have performed immunofluorescence with serial dilutions of the H1.3 antibody to show that peripheral distribution was not due to fluorescence signal intensity quenching (Figure 1figure supplement 1A).

(3) Histone H1 is highly mobile and there is some concern that they could reorganize during the relatively long period of time that it takes to fully fix the cells for both ChIP and immunofluorescence. This should be acknowledged in the manuscript.

We have added this reviewer’ concern in the Discussion section.

(4) The paper would benefit from a more rigorous quantification of histone H1 subtypes. Mass spectrometry would be ideal but more classical techniques such as 2D AU-SDS PAGE, HPLC, etc...would be an improvement over immunoblotting. The authors did not explain the quantification of the immunoblots and the assignment of relative contributions of H1 subtypes to the individual coommassie bands in the Image J section of methods, which is referred to as the method of quantification in the immunoblotting methods.

We have further explained how the relative quantification of H1 variants in different cell lines was performed (Methods section). We agree that more sophisticated mass spectrometrybased quantification is desirable and we are collaborating to do this using internal H1 peptide controls (Parallel Reaction Monitoring), but this is out of the scope of this manuscript as the observed patterns of distribution of H1 variants do not depend on mild differences in variants abundance. Only the absence of H1.3 and H1.5 in some cell lines alters the distribution of other variants.

Additional author responses to the Public Review comments made by some Reviewer:

(1) Respect to the functional significance of the results presented here, we want to stress that as a consequence of the differential distribution and abundance of H1 variants among cell types, depletion of different variants has different consequences. For example, H1.2 depletion but not others has a great impact on chromatin compaction. Besides, cell lines lacking H1.3/H1.5 expression present a basal up-regulation of some Interferon stimulated genes (ISGs) and particular repetive elements, as it was previously described upon induced depletion of H1.2/H1.4 in a breast cancer cell line or in pancreatic adenocarcinomas with lower levels of replication-dependent H1 variants (Izquierdo et al. 2017 NAR 45:11622). So, our results reinforce the existing link between H1 content and immune signature. We have added this data in the revised manuscript (Figure 5-figure supplement 5).

Moreover, we also analyzed the chromatin structural changes upon combined depletion of H1.2 and H1.4. Combined H1.2/H1.4 depletion triggers a global chromatin decompaction, which supports previous observations from ATAC-Seq and Hi-C experiments in these cells (Izquierdo et al. 2017 NAR 45:11622; Serna-Pujol et al. 2022 NAR 50:3892). Although H1 content is more compromised in these cells (30% total H1 reduction) compared to single H1 KDs, the phenotype observed could not be recapitulated when other H1 KD combinations, in which total H1 content was reduced similarly, were investigated (Izquierdo et al. 2017 NAR 45:11622), supporting that the deleterious defects were due to the non-redundant role of H1.2 and H1.4 proteins. Indeed, this manuscript supports this notion, as H1.2 and H1.4 show a different genomewide and nuclear distribution.

(2) Our immunofluorescence data, together with ChIP-seq data, do not discard binding of H1 variants to a great variety of chromatin, but show enrichment or preferential binding to certain regions or chromatin types. Our data on the interphase nuclei does not suggest at all any type of quenching or saturation. Obviously, detection with antibodies depends on epitope accessibility, just like all immunofluorescence data ever published, and we have acknowledged that post-translational modifications of H1 may occlude antibody accessibility as some phospho-H1 antibodies give distribution patterns different than total/unmodified H1 antibodies. Thus, we cannot exclude that specific modified-H1s exhibit particular distribution patterns that are not being recapitulated in our data. This represents another layer of complexity in H1 diversity and we agree that exploration of the repertoire of H1 PTMs and their functional roles are an interesting matter of study that needs to be addressed. Still, our data is highly relevant as it demonstrates for the first time the unique distribution patterns of H1 variants among multiple cell lines and it does not use overexpression of tagged H1 variants that in our experience may produce mislocalization of H1s.

(3) We do have investigated co-localization of H1 variants with HP1alpha protein and we have added this data in the revised version of this manuscript (Figure 1-figure supplement 1C-D).

Author Response

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

eLife assessment:

The authors report a novel hepatic lncRNA FincoR regulating FXR with therapeutic implications in the treatment of MASH. The findings are important and use an appropriate methodology in line with the current state-of-the-art, with convincing support for the claims.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In the article titled "Hammerhead-type FXR agonists induce an eRNA FincoR that ameliorates nonalcoholic steatohepatitis in mice," the authors explore the role of the Farnesoid X Receptor (FXR) in treating metabolic disorders like NASH. They identify a new liver-specific long non-coding RNA (lncRNA), FincoR, regulated by FXR, notably induced by agonists such as tropifexor. The study shows that FincoR plays a significant role in enhancing the efficacy of tropifexor in mitigating liver fibrosis and inflammation associated with NASH, suggesting its potential as a novel therapeutic target. The study makes a promising contribution to understanding the role of FincoR in alleviating liver fibrosis in NASH, providing initial insights into the mechanisms involved. While it offers a valuable starting point, there is potential for further exploration into the functional roles of FincoR and their specific actions in human NASH cases. Building upon the current findings to elucidate more detailed mechanistic pathways through which FincoR exerts its therapeutic effects in liver disease would elevate the research's significance and potential impact in the field.

Strengths:

This study stands out for its comprehensive and unbiased approach to investigating the role of FincoR, a liver-specific lncRNA, in the treatment of NASH. Key strengths include: 1) The application of advanced sequencing methods like GRO-seq and RNA-seq offered a comprehensive and unbiased view of the transcriptional changes induced by tropifexor, particularly highlighting the role of FincoR. 2) Utilizing a genetic mouse model of FXR KO and a FincoR liver-specific knockdown (FincoR-LKD) mouse model provided a controlled and relevant environment for studying NASH, allowing for precise assessment of tropifexor's therapeutic effects. 3) The inclusion of tropifexor, an FDAapproved FXR agonist, adds significant clinical relevance to the study. It bridges the gap between experimental research and potential therapeutic application, providing a direct pathway for translating these findings into real-world clinical benefits for NASH patients. 4) The study's rigorous experimental design, incorporating both negative and positive controls, ensured that the results were specifically attributable to the action of FincoR and tropifexor.

Weaknesses:

The study presents several notable weaknesses that could be addressed to strengthen its findings and conclusions: 1) The authors focus on FincoR, but do not extensively test other lncRNAs identified in Figure 1A. A more comprehensive approach, such as rescue experiments with these lncRNAs, would provide a better understanding of whether similar roles are played by other lncRNAs in mitigating NASH. 2) FincoR was chosen for further study primarily because it is the most upregulated lncRNA induced by GW4064. Including another GW4064-induced lncRNA as a control in functional studies would strengthen the argument for FincoR's unique role in NASH. 3) The study does not conclusively demonstrate whether FincoR is specifically expressed in hepatocytes or other liver cell types. Conducting FincoR RNA-FISH with immunofluorescent experiments or RT-PCR, using markers for different liver cell types, would clarify its expression profile. 4) Understanding the absolute copy number of FincoR is crucial. Determining whether there are sufficient copies of FincoR to function as proposed would lend more credibility to its suggested role. 5) The manuscript, although technically proficient, does not thoroughly address the relevance of these findings to human NASH. Questions like the conservation of FincoR in humans and its potential role in human NASH should be discussed.

Reviewer #2 (Public Review):

Summary:

Nonalcoholic fatty liver disease (NASH), recently renamed as metabolic dysfunctionassociated steatohepatitis (MASH) is a leading cause of liver-related death. Farnesoid X receptor (FXR) is a promising drug target for treating NASH and several drugs targeting FXR are under clinical investigation for their efficacy in treating NASH. The authors intended to address whether FXR mediates its hepatic protective effects through the regulation of lncRNAs, which would provide novel insights into the pharmacological targeting of FXR for NASH treatment. The authors went from an unbiased transcriptomics profiling to identify a novel enhancer-derived lncRNA FincoR enriched in the liver and showed that the knockdown of FincoR in a murine NASH model attenuated part of the effect of tropifexor, an FXR agonist, namely inflammation and fibrosis, but not steatosis. This study provides a framework for how one can investigate the role of noncoding genes in pharmacological intervention targeting known protein-coding genes. Given that many disease-associated genetic variants are located in the non-coding regions, this study, together with others, may provide useful information for improved and individualized treatment for metabolic disorders.

Strengths:

The study leverages both transcriptional profile and epigenetic signatures to identify the top candidate eRNA for further study. The subsequent biochemical characterization of FincoR using FXR-KO mice combined with Gro-seq and Luciferase reporter assays convincingly demonstrates this eRNA as a FXR transcriptional target sensitive to FXR agonists. The use of in vitro culture cells and the in vivo mouse model of NASH provide multi-level evaluation of the context-dependent importance of the FincoR downstream of FXR in the regulation of functions related to liver dysfunction.

Weaknesses:

As discussed, future work to dissect the mechanisms by which FincoR facilitates the action of FXR and its agonists is warranted. It would be helpful if the authors could base this on the current understanding of eRNA modes of action and the observed biochemical features of FincoR to speculate potential molecular mechanisms explaining the observed functional phenotype. It is unclear if this eRNA is conserved in humans in any way, which will provide relevance to human disease. Additionally, the eRNA knockdown was achieved by deletion of an upstream region of the eRNA transcription. A more direct approach to alter eRNA levels, e.g., overexpression of FincoR in the liver would provide important data to interpret its functional regulation.

We thank the Editor and Reviewers for their constructive comments. We believe we have addressed all of the issues (detailed below) and the revisions have greatly strengthened the manuscript.

Reviewer 1:

The study presents several notable weaknesses that could be addressed to strengthen its findings and conclusions:

(1) The authors focus on FincoR, but do not extensively test other lncRNAs identified in Figure 1A. A more comprehensive approach, such as rescue experiments with these lncRNAs, would provide a better understanding of whether similar roles are played by other lncRNAs in mitigating NASH.

(2) FincoR was chosen for further study primarily because it is the most upregulated lncRNA induced by GW4064. Including another GW4064-induced lncRNA as a control in functional studies would strengthen the argument for FincoR's unique role in NASH.

(3) The study does not conclusively demonstrate whether FincoR is specifically expressed in hepatocytes or other liver cell types. Conducting FincoR RNA-FISH with immunofluorescent experiments or RT-PCR, using markers for different liver cell types, would clarify its expression profile.

(4) Understanding the absolute copy number of FincoR is crucial. Determining whether there are sufficient copies of FincoR to function as proposed would lend more credibility to its suggested role.

Response to 1 - 4): We thank Reviewer 1 for the positive comments on the strength of our work, including the open-ended approach, the novel eRNA FincoR and its strong relevance to liver disease. We also value the constructive feedback provided by the reviewer and agree that additional studies are important to fully understand the mechanisms of FincoR and the functional significance of other FXR-induced lncRNAs. In this manuscript we report the discovery and initial characterization of FincoR, as well as its potential function in FXR action in response to hammerhead agonists, but a number of interesting questions are raised. Future experiments, as suggested by reviewer, will be needed to examine the role of other FXR-induced lncRNAs, the potential role of FincoR induction by other nuclear receptors with binding sites at FincoR, whether FincoR is expressed in liver cell types in addition to hepatocytes, and the expression abundance of FincoR. These are all excellent suggestions for future experimentation which we feel are beyond the scope of the present report. For example, generating a genetic CRISPR/Cas9 of another lncRNA is not trial as it takes a significant amount of work with murine models. Also, we did not mean to exclude if other lncRNAs induced by FXR also bear functions. Technically, rescue experiment is not possible as FincoR RNA can be potentially very long (~10 kb if estimated by RNA-seq pattern in Fig.1C), and it is not feasible now to properly express it by exogenous vectors to ensure the expression levels are similar to endogenous ones. We therefore consider that these important questions are more suitable for future work to fully address. Our belief is that a comprehensive exploration of FXR-regulated lncRNAs holds the potential to unveil novel insights crucial for the development of therapies targeting NASH and other metabolic diseases. The study of FincoR is the beginning of this area of research.

(5) The manuscript, although technically proficient, does not thoroughly address the relevance of these findings to human NASH. Questions like the conservation of FincoR in humans and its potential role in human NASH should be discussed.

Response: These are important questions. To respond to the reviewer’s comment, new experiments are presented in our final revised manuscript in which we utilized mouse models of NAFLD/NASH and cholestatic liver injury to determine FincoR’s role in these diseases. Hepatic FincoR levels were significantly increased in mice fed with high fat diet (HFD) for 12 weeks (Supplementary Figure S1A) and in mice fed a HFD with high fructose (HFHF) in drinking water for 12 weeks (Supplementary Figure S1B). Elevated hepatic FincoR levels were also observed in mice treated with α-naphthylisothiocyanate (ANIT), a chemical inducer of liver cholestasis (Supplementary Figure S1C), and in mice with bile duct ligation (BDL), a surgical method to induce cholestatic liver injury (Supplementary Figure S1D).

In terms of the human relevance, we have provided additional information and figures showing that there is sequence similarity between mouse FincoR and a human loci. FincoR sequence is moderately conserved between mice and humans as displayed in the UCSC genome browser (Supplementary Figure S1E). Annotation of these conserved human sequences revealed that they overlap with a functionally uncharacterized human lncRNA XR_007061585.1 (Supplementary Figure S1F). Further, we conducted qRT-PCR experiment from human patient’s RNA samples, which demonstrated that hepatic lncRNA XR_007061585.1 levels are elevated in patients with NAFLD and PBC, but not in severe NASH-fibrosis patients (Supplementary Figure S1G, H). These results demonstrate that hepatic levels of a potential human analog of FincoR are elevated in NAFLD and PBC patients, which is consistent with FincoR’s upregulation in mouse models of chronic liver disease with hepatic inflammation and liver injury. Whether human lncRNA XR_007061585.1 is entirely analogous to mouse FincoR in terms of functions and mechanisms, and whether the elevation of this human lncRNA has a role in liver disease progression or is an adaptive response to liver injury remains to be determined.

Reviewer #2 (Recommendations For The Authors):

(1) In the introduction Line 96, "..., while the vast majority are transcribed into ncRNAs" may not be accurate. Please refer to Pointing and Haerty Annu Rev 2022 for a related discussion.

Response: We would like to thank the reviewer for pointing out this inaccurate information in the introduction. We have changed the content in the text, “While a significant portion of the genome was initially thought to be "junk DNA", it has been established that many non-coding regions give rise to functional non-coding RNAs.”

(2) Figure 5: the authors should provide a clear illustration demonstrating the sequence targeted by the sgRNA in relation to the transcriptional and epigenetic profile (i.e., RNAseq and H3K27ac ChIP-seq data).

Response: The illustration (Figure 5-figure supplement 1A, right panel) demonstrating the sequence targeted by the sgRNA has been updated as suggested by the reviewer.

In this model, the upstream of FincoR is deleted, leading to the inhibition of FincoR transcription. Does the deleted region include FXR binding sites? If so, would the phenotype be due to the deletion of these binding sequences, rather than the decreased FincoR transcripts? Accordingly, the limitation or alternative interpretation should be discussed.

Response: The reviewer made a good point. The deleted region includes FXR binding sites so that we cannot rule out decreased binding of FXR or decreased transcription of the region per se, in addition to the decreased levels of FincoR, to bear a role in the phenotypic changes we observed. In the final revision, we have added discussion of this alternative (6th paragraph in the revised discussion section).

(3) Figure 6C, the images should be accompanied by quantification. It appears the FincoR-KD shows a visible difference as compared to Tropifexor-treated control mice, which does not match entirely what is written in the results.

Response: The quantitation of Oil Red O staining has been done as suggested by the reviewer (Figure 6C). The result is consistent with the triglyceride result showing that tropifexor treatment markedly reduced neutral lipids determined by Oil Red O staining of liver sections (Figure 6C) and liver TG levels (Figure 6D) and these beneficial effects on reducing fatty liver were not altered by FincoR.

(4) Figure 7, does AST show the same pattern as ALT? As indicated from Line 335, "tropifexor treatment reduced mRNA levels of several genes that promote fibrosis (Col1a1, Col1a2, ...)". Fig. 7D does not seem to match the description of Col1a1. Authors may need to modify the results.

Response: AST has been measured and has the same pattern as ALT. The new data have been added to Figure 7B. Col1a1 expression has been re-measured and the results have been updated in Figure 7D.

(5) Is FincoR level reduced in NASH conditions?

Response: We thank the Reviewer for this question. We now added new data to examine the levels of FincoR in mouse liver disease models and also examined levels of a potential human analog of FincoR in human liver specimens from PBC, NAFLD, and NASH patients. Please see our new data and description above in the response to comment 5 by Reviewer 1 (most data now included in the new Supplementary Figure S1).

(6) Please provide information on the conservation of FincoR (DNA and RNA) in humans. This would be important to provide the human disease relevance.

Response: As described above in the response to comment 5 of reviewer 1, a human loci shows sequence similarity to mouse FincoR and this conserved region has an annotated uncharacterized human lncRNA. We also examined the levels of this human homolog in human diseased liver samples. Our new results demonstrate that hepatic levels of a potential human analog of FincoR are elevated in NAFLD and PBC patients, which is consistent with FincoR’s upregulation in mouse models of chronic liver disease with hepatic inflammation and liver injury. Whether human lncRNA XR_007061585.1 is entirely analogous to mouse FincoR in terms of functions and mechanisms, and whether the elevation of this human lncRNA has a role in liver disease progression or is an adaptive response to liver injury remains to be determined.

(7) Several discussion points for the authors' consideration:

(7.1) human-mouse conservation as alluded to in #6;

Response: Potential human-mouse conservation is discussed with new data in the last paragraph of the Results section.

(7.2) potential molecular mechanism involved in FincoR-regulated hepatocyte function;

Response: We thank Reviewer for this comment. We have added more discussion as shown below: “RNA inside the cells usually associates with different RNA-binding proteins (RBPs). To predict those potential binding proteins of FincoR. Additional bioinformatic analysis identified proteins that potentially binding FincoR, including KHDRBS1, RBM38, YBX2 and YBX3 (Supplemental Table S5). These findings and potential functions of the binding proteins are discussed in the 5th paragraph of the discussion section in the final revised manuscript. Whether these predicted RBPs interact with FincoR and the underlying mechanisms will need to be investigated in future experimentation to understand the mechanisms involved in FincoR-regulated hepatocyte function.”

(7.3) any disease-associated SNPs in the FincoR locus.

Response: No SNPs were noted in the annotation of the human loci with sequence similarity to mouse FincoR in the NCBI genome data viewer.

(7.4) the in vitro induction of FincoR is transient but in vivo this occurs after 12 days of drug treatment. How do the authors reconcile the differential induction patterns?

Response: To clarify, the induction of FincoR after a single dose of GW4064 in vivo was transient, peaked within 1 h and then declined gradually (Figure 1-figure Supplement 1C). In the tropifexor treatment protocol (also in vivo), the mice were treated daily with tropifexor for 12 days so that the multiple doses maintained FincoR induction. The beneficial effect of tropifexor by inducing FincoR, therefore, accumulated over the 12 days.

It is worthy to note that we failed to see induction of FincoR in isolated primary mouse hepatocytes treated with GW4064 in vitro. We can only detect FincoR in primary hepatocytes isolated from GW4064-treated mice liver. This may be due to the loss of key factors mediating FincoR induction in the cultured primary hepatocytes.

Author Response

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

eLife assessment

This manuscript describes valuable information on how the extraocular muscles (EOM) are preserved in a mouse model of familial Amyotrophic lateral sclerosis (ALS) that carries a G93A mutation in the Sod1 gene. The authors provide convincing evidence of how the integrity of neuromuscular junction is preserved in EOM but not in limb and diaphragm muscles of G93A mice. Overall, this interesting work provides new evidence regarding the etiopathogenesis of ALS and insights for the development of therapeutic targets to slow the loss of neuromuscular function in ALS.

Public Reviews:

Reviewer#1 (Public Review):

Summary:

The study explores the mechanisms that preserve satellite cell function in extraocular muscles (EOMs) in a mouse model of familial Amyotrophic lateral sclerosis (ALS) that carries the G93A mutation in the Sod1 gene. ALS is a fatal neuromuscular disorder driven by motor neuron degeneration, leading to progressive wasting of most skeletal muscles but not EOM. The study first established that integrity of neuromuscular junction (NMJ) is preserved in EOM but not in limb and diaphragm muscles of G93A mice, and sodium butyrate (NaBu) treatment partially improves NMJ integrity in limb and diaphragm muscles of G93A mice. They also found a loss of synaptic satellite cells and renewability of cultured myoblasts in hindlimb and diaphragm muscles of G93A mice, but not in EOM, and NaBu treatment restores myoblast renewability. Using RNA-seq analysis, they identify that exon guidance molecules, particularly Cxcl12, are highly expressed in EOM myoblasts, along with more sustainable renewability. Using a neuromuscular co-culture model, they convincingly show that AAV-mediated Cxcl12 expression in G93A myotubes enhances motor axon extension and innervation. Strikingly, NaBu-mediated preservation of NMJ in limb muscles of G93A mice is associated with elevated expression of Cxcl12 in satellite cells and improved renewability of myoblasts. These results together offer molecular insights into genes critical for maintaining satellite cell function and revealing a mechanism through which NaBu ameliorates ALS.

Strengths:

Combination of in vivo and cell culture models. Nice imaging of NMJ and associated satellite cells. Using motoneuron-myotube coculture to establish the mechanism. Tested and illustrated a mechanism through which a clinically used drug ameliorates ALS.

Weaknesses:

Data presentation could be improved (see details in the Recommendation for Authors).

It would have been nice to have included G93A motoneurons in the coculture study.

This is indeed a plan of our future study. In the revised version, we discussed the limitation of not including G93A motor neurons in the coculture assay. (Page 11, Line 445-448)

“However, it is possible that motor neurons carrying ALS mutations will respond differently to Cxcl12 mediated axon guidance than WT motor neurons. This is a limitation of the current study which will be investigated in future co-culture studies.”

Reviewer #2 (Public Review):

Summary:

The work is potentially interesting as it outlines the role of satellite cells in supporting the functional decline of skeletal muscle due to the denervation process. In this context the authors analyze the functional and molecular characteristics of satellite cells in different muscle types differently affected by the degenerative process in the ALS model.

Strengths:

The work illustrates a relevant aspect of the differences in stem cell potential in different skeletal muscles in a mouse model of the disease through a considerable amount of data and experimental models.

Weaknesses:

However, there are some criticisms of the structuring of the results:

It is not clear how many animals were used in each experimental group (Figs 1 and 2, Fig. 2-9). In particular, it is unclear whether the dots in the histograms represent biological or technical replicates. Furthermore, the gender used in experimental groups is never specified. This last point appears to be important considering the gender differences observed in the SOD1G93A mouse model.

The original quantification data and mouse gender specification were actually listed in the corresponding supplementary tables. We now added the gender specification and number of the mice used in all corresponding figure legends. The number of mice used for sorting SCs from different muscles were also specified in the Methods section in the revised manuscript. (Page 12, Line 489-493).

We also added one more supplementary figure (Figure 1-figure supplement 2) to compare the innervation status between male and female mice. The following description has been added in the updated manuscript (Page 3-4; Line 125-130):

“The data shown in Figure 1B has also been replotted to compare the innervation status between male and female mice (Figure 1- figure supplement 2). In terms of well- or partially- innervated ratios, there are no significant gender difference observed in our experimental condition, in which the muscle samples were collected at the end stage of the disease, although there is marginally lower “poorly innervated ratio” in the EDL muscle of G93A female mice compared to G93A male mice.”

However, we acknowledge that the current study has limitations to fully detect cross-gender differences in our experiments due to low “n” numbers per gender. We hope this is understandable as we have to split limited resource of ALS G93A mice between different kinds of experiments, including NMJ integrity assessment, peri-nuclear SC abundance assessment, whole muscle-qPCR, cell sorting for imaging, cell sorting for RNA-Seq, cell-sorting for qPCR, cell-sorting for neuromuscular co-culture, etc., in this pioneer study. However, we do intend to gradually build up “n” numbers for characterization of cross-gender difference in our ongoing studies.

As to what the dots in each plot represent, we have inserted the description in each relevant figure legend as detailed below:

For Fig 1, each dot represents quantification result from a single mouse. Please see Figure 1-figure supplement 1, Figure 1-figure supplement 2 and Figure 1-table supplement 1 for NMJs measured per muscle type per gender. Briefly, EDL, soleus and diaphragm muscles were from 4 male and 6 female mice per group; WT EOM group was from 4 male and 4 female mice; G93A EOM group was from 3 male and 4 female mice; G93A EOM with NaBu feeding group was from 6 female mice.

For Fig 2, each dot represents quantification result from a single mouse. Please see Figure 2-table supplement 1 for NMJs measured per muscle type per gender. Briefly, WT EDL group was from 2 male and 2 female mice; G93A EDL group was from 3 male and 3 female mice; G93A EDL with NaBu feeding group was from 2 male and 4 female mice; WT soleus group was from 2 male and 3 female mice; G93A soleus group was from 3 male and 2 female mice; G93A soleus with NaBu feeding group was from 1 male and 4 female mice; WT diaphragm group was from 1 male and 4 female mice; G93A diaphragm group was from 1 male and 4 female mice; G93A diaphragm with NaBu feeding group was from 4 female mice; WT EOM group was from 1 male and 3 female mice; G93A EOM group was from 5 female mice; G93A EOM with NaBu feeding group was from 1 male and 3 female mice.

For Fig 3, each dot in the box-and-dot plots represents result from one round of sorting. WT HL SCs were from 8 male and 6 female mice; G93A HL SCs were from 9 male and 5 female mice; WT diaphragm SCs were from 6 male and 3 female mice; G93A diaphragm SCs were from 12 male and 5 female mice. WT EOM SCs were from 6 batches of male and 1 batch of female mice (each batch contains 5-6 mice of the same gender). G93A EOM SCs were from 5 batches of male and 2 batches of female mice.

*Please note these results were from sorting in which the FACS profiles were recorded. Not all rounds of sorting were with FACS profile recorded.

For Fig 4A, each dot in the box-and-dot plots represents one image analyzed. For WT HL SCs, 94 images from 3 rounds of sorting; For WT Dia SCs, 107 images from 3 rounds of sorting; For WT EOM SCs, 75 images from 3 rounds of sorting; For G93A HL SCs, 96 images from 3 rounds of sorting; For G93A Dia SCs, 62 images from 3 rounds of sorting; For G93A EOM SCs, 79 images from 3 rounds of sorting. For the 3 rounds of sorting, 1 was from male and 2 were from female mice.

*Please note that the number of mice used for sorting SCs in different muscles were specified in the Method Section in the revised manuscript. (Page 12, Line 489-493)

For Fig 4B, each dot in the box-and-dot plots represents one image analyzed. For WT HL SCs, 52 images from 3 rounds of sorting; For WT Dia SCs, 51 images from 3 rounds of sorting; For WT EOM SCs, 51 images from 3 rounds of sorting; For G93A HL SCs, 52 images from 3 rounds of sorting; For G93A Dia SCs, 47 images from 3 rounds of sorting; For G93A EOM SCs, 56 images from 3 rounds of sorting. For the 3 rounds of sorting, 1 was from male and 2 were from female mice.

For Fig 5A, each dot in the box-and-dot plots represents one replicate of culture. HL SCs were from male mice.

For Fig 5B, each dot in the box-and-dot plots represents one image analyzed. For G93A HL SCs, 52 images from 3 rounds of sorting; 1-day NaBu treatment, 45 images from 3 rounds of sorting; 3-day NaBu treatment, 51 images from 3 rounds of sorting; For G93A Dia SCs, 47 images from 3 rounds of sorting; 1-day NaBu treatment, 60 images from 3 rounds of sorting; 3-day NaBu treatment, 57 images from 3 rounds of sorting. For the 3 rounds of sorting, 2 were from male and 1 was from female mice.

For Fig 6, all samples used for bulk RNA-Seq were from female mice.

For Fig 7C, each dot in the box-and-dot plots represents one replicate of culture. RNA samples were collected from 3-6 rounds of sorting and sorted cells were seeded into 3 dishes as replicates. WT HL SCs were from 3 male and 1 female mice. WT diaphragm SCs were from 2 male and 2 female mice; WT EOM SCs were from 3 male mice; G93A HL SCs were from 4 male and 2 female mice. G93A diaphragm SCs were from 1 male and 3 female mice; G93A EOM SCs were from 3 male mice.

For Fig 7D, each dot in the box-and-dot plots represents one replicate of culture. RNA samples were collected from 6 rounds of sorting and sorted cells were seeded into 3 dishes as replicates. G93A HL SCs were from 4 male and 2 female mice; G93A diaphragm SCs were from 2 male and 4 female mice.

For Fig 8D, each dot in the box-and-dot plot represents one neurite measured. HL and EOM SCs used for co-culture experiments were all from male mice.

For Fig 9D, each dot in the box-and-dot plot represents one image analyzed. HL and EOM SCs used for co-culture experiments were all from male mice.

For Figure 1-figure supplement 1, each dot in the box-and-dot plots represents quantification result from one mouse. Please also see Figure 1-table supplement 2. Briefly, muscles in WT and G93A groups were from 3 male and 3 female mice per group; G93A EDL with NaBu feeding group was from 3 male and 3 female mice. G93A soleus with NaBu feeding group was from 2 male and 3 female mice; G93A diaphragm with NaBu feeding group was from 2 male and 4 female mice; G93A EOM with NaBu feeding group was from 4 male and 2 female mice.

The first paragraph of the results lacks a functional analysis of the motor decline of the animals after the administration of sodium butyrate. The authors, in fact, administered NaBu around 90 days of age while in previous work the drug had been administered at a pre-symptomatic age. It would therefore be useful, to make the message more effective, to characterize the locomotor functions of the treated animals in parallel with the histological evidence of the integrity of the NMJ.

We are still in the process of collecting locomotor function data for G93A mice with and without NaBu treatment. We plan to report them in a future manuscript while this manuscript focuses on the molecular and histological aspect. Additionally, in the revised manuscript, we revised the rationale of the NaBu treatment starting after the disease onset. (Page 4, Line 131-134)

“In the previous study, NaBu treatment initiated at a pre-symptomatic age delayed disease progression in G93A mice. As treatment of ALS patients is initiated after symptoms appear, we further tested whether NaBu treatment started after disease onset (at the age of 3 months, 2% NaBu in water for 1 month) was effective in preserving NMJ integrity.”

Figure 5 should be completed with the administration of NaBu also to the satellite cells isolated from the WT mouse, the same for figure 9 where AAV-CMV-Cxcl12 transduction of WT myotubes is missing. We appreciate the reviewer’s suggestion of conducting the additional experiment with AAV-delivery of CXCL12 into the myotubes derived from the WT mice. Extensive studies by other investigators have been performed with butyrate on satellite cells derived from WT mice. To name a few here: Fiszman et al., 1980 (DOI: 10.1016/0014-4827(80)90467-X); Johnston et al., 1992 (DOI: 10.1128/mcb.12.11.5123-5130.1992); Lezzi et al., 2002 (DOI: 10.1073/pnas.112218599). To avoid performing redundant experiments, we focus on the effect of butyrate on the proliferation and differentiation of SCs derived from G93A mice. Thanks to the reviewer’s comment, we added additional discussion in the Results section (Page 6, line 216-217). Regarding the effect of Cxcl12, published studies have demonstrated its role in promoting axon growth. To name a few here: Negro et al., 2017 (DOI: 10.15252/emmm.201607257); Lieberam et al., 2005 (DOI: 10.1016/j.neuron.2005.08.011); Whitman et al., 2018 (DOI: 10.1167/iovs.18-25190). (Page 10, line 434, 440-442).

In the experiment illustrated in Figure 8, treatment of cell cultures with NaBu would improve the outcome as well as the interference of Cxcl12 expression in myotubes derived from G93A EOM SC (Fig.9) would strengthen the specificity of this protein in axon guidance in this NMJ typical of a spared muscle in ALS.

This is a great suggestion. Our study demonstrated the overexpression of CXCL12 in G93A myotube can enhance the axonal guidance and innervation of the co-cultured myotube/moto-neurons. We have also demonstrated the NaBu treatment can enhance the expression of CXCL12 and slow ALS progression. Combining NaBu treatment with CXCL12 overexpression may indeed have additive therapeutic benefits to slow ALS progression. We have added this statement in the revised Discussion. (Page 11, Line 466-468)

In the "materials and methods" section the paragraph relating to the methods used for statistical analysis is missing.

We have added it accordingly. (Page 15, Line 631-636)

Reviewer #3 (Public Review):

Summary:

In their paper, Li et al. investigate the transcriptome of satellite cells obtained from different muscle types including hindlimb, diaphragm, and extraocular muscles (EOM) from wild-type and G93A transgenic mice (end-stage ALS) in order to identify potential factors involved in the maintenance of the neuromuscular junction. The underlying hypothesis is that since EOMs are largely spared from this debilitating disease, they may secrete NMJ-protective factors. The results of their transcriptome analysis identified several axon guidance molecules including the chemokine Cxcl12, which are particularly enriched in EOM-derived satellite cells. Transduction of hindlimb-derived satellite cells with AAV encoding Cxcl12 reverted hindlimb-derived myotubes from the G93A mice into myotubes sharing phenotypic characteristics similar to those of EOM-derived satellite cells. Additionally, the authors were able to demonstrate that EOM-derived satellite cell myotube cultures are capable of enhancing axon extensions and innervation in co-culture experiments.

Strengths:

The strength of the paper is that the authors successfully isolated and purified different populations of satellite cells, compared their transcriptomes, identified specific factors released by EOM-derived satellite cells, overexpressed one of these factors (the chemokine Cxcl12) by AAV-mediated transduction of hindlimb-derived satellite cells. The transduced cells were then able to support axon guidance and NMJ integrity. They also show that administration of Na butyrate to mice decreased NMJ denervation and satellite cell depletion of hind limbs. Furthermore, the addition of Na Butyrate to hindlimb-derived satellite cell myotube cultures increased Cxcl12 expression. These are impressive results providing important insights for the development of therapeutic targets to slow the loss of neuromuscular function characterizing ALS.

Weaknesses:

Several important aspects have not been addressed by the authors, these include the following points which weaken the conclusions and interpretation of the results.

(a) Na Butyrate was shown to extend the survival of G93A mice by Zhang et al. Na butyrate has a variety of biological effects, for example, anti-inflammatory effects inhibit mitochondrial oxidative stress, positively influence mitochondrial function, is a class I / II HDAC inhibitor, etc. What is the mechanism underlying its beneficial effects both in the context of mouse muscle function in the ALS G93A mice and in the in vitro myotube assay? Cytokine quantification as well as histone acetylation/methylation can be assessed experimentally and this is an important point that has not been appropriately investigated.

Great suggestion by the reviewer.

Our previous publications (DOI: 10.3390/biom12020333; DOI: 10.3390/ijms22147412) have shown the beneficial roles of NaBu in ameliorating mitochondrial function in both motor neuron-like cells and adult muscle fibers. A focus of the current study is to test whether NaBu treatment also affect the SCs by regulating their gene transcription. Regarding the potential on HDAC/acetylation modification, there are previous studies by other investigators. We have added these references in the Discussion (Page 11, line 466-468).

(b) In the context of satellite cell characterization, on lines 151-152 the authors state that soleus muscles were excluded from further studies since they have a higher content of slow twitch fibers and are more similar to the diaphragm. This justification is not valid in the context of ALS as well as many other muscle disorders. Indeed, soleus and diaphragm muscles contain a high proportion of slow twitch fibers (up to 80% and 50% respectively) but soleus muscles are more spared than diaphragm muscles. What makes soleus muscles (and EOMs) more resistant to ALS NMJ injury? Satellite cells from soleus muscles need to be characterized in detail as well.

We agree with the reviewer’s comment that our original statement is misleading regarding the difference between soleus and diaphragm muscles in terms of the content of slow twitch fibers. Our histological studies revealed similar defects in denervation of diaphragm and soleus muscles derived from the G93A mice. Most importantly, the degree of NMJ degeneration and atrophy is less severe in soleus compared to other hindlimb muscles, such as EDL, during ALS progression. We have cited related studies such as Valdez et al., 2012 (DOI: 10.1371/journal.pone.0034640), Atkin et al., 2005 (DOI: 10.1016/j.nmd.2005.02.005). To avoid any confusion, we have removed the original statement and revised the paragraph (Page 4, line 159-162).

“The three groups were determined because they represent the most severely affected, moderately affected and least affected muscles by ALS progression, respectively. Soleus was not included in the hindlimb SCs pool because its less affected than other hindlimb muscles based on our study and others [6,42].”

Furthermore, EOMs are complex muscles, containing many types of fibers and expressing different myosin heavy chain isoforms and muscle proteins. The fact that in mice both the globular layer and orbital layers of EOMs express slow myosin heavy chain isoform as well as myosin heavy chain 2X, 2A, and 2B (Zhou et al., 2010 IOVIS 51:6355-6363) also indicates that the sparing is not directly linked to the fast or slow twitch nature of the muscle fiber. This needs to be considered.

We greatly appreciate your suggestions and have included these points in the revised Discussion. “It is known that EOMs are complex muscles. Besides the developmental myosin isoforms, EOMs also express both adult fast and slow myosin contractile elements (Zhou et al., 2010 IOVIS 51:6355-6363), suggesting that the sparing may not be solely linked to the fast or slow twitch nature of the muscle fiber, rather the changes in SCs may play a pivotal role in preserving the EOM function during the progression of ALS. ” (Page 9, line 389-392)

(c) In the context of myotube formation from cultured satellite cells on lines 178-179 the authors stained the myotubes for myosin heavy chain. Because of the diversity of myosin heavy chain isoforms and different muscle origins of the satellite cells investigated, the isoform of myosin heavy chain expressed by the myotubes needs to be tested and described. It is not sufficient to state anti-MYH.

We used the pan-anti-MYH antibody (MF20 from DSHB) for the immunostaining of myosin heavy chain for identification of the differentiated myotubes. As described in the commercial website: https://dshb.biology.uiowa.edu/MF-20), FM20 recognizes all myosin heavy chain isoforms. We are happy to examine whether specific myosin heavy chain isoforms may contribute to the differences observed in future studies.

(d) The original RNAseq results have not been deposited and while it is true that the authors have analyzed the results and described them in Figures 6 and 7 and relative supplements, the original data needs to be shown both as an xls list as a Volcano plots (q value versus log2 fold change). This will facilitate the independent interpretation of the results by the readers as some transcripts may not be listed. As presented it is rather difficult to identify which transcripts aside from Cxcl12 are commonly upregulated. Can the data be presented in a more visual way?

We have uploaded the Fastq files and the text files containing TPM values to the Gene Expression Omnibus (GEO) database and included the GEO access number GSE249484 in the revised text. Per recommendation of the reviewer, we have added supplementary tables for Figure 6, to list the top 20 differentially expressed genes (ranked by Log2FC, both the upregulated and downregulated) comparing 1) EOM SCs to their hindlimb and diaphragm counterparts (Figure 6-table supplement 1); 2) G93A SCs to WT SCs of the same muscle origin (Figure 6-table supplement 2); 3) G93A hindlimb and diaphragm SCs with 3 day-NaBu treatment to those without (Figure 6-table supplement 3). (Page 6, Line 237-257)

(e) There is no section describing the statistical analysis methods used. In many figures, more than 2 groups are compared so the authors need to use an ANOVA followed by a post hoc test.

Thank for the comments. We have added it accordingly. (Page 15, Line 631-636)

The authors have achieved their aim in showing that satellite cells derived from EOMs have a distinct transcriptome and that this may be the basis of their sparing in ALS. Furthermore, this work may help develop future therapeutic interventions for patients with ALS.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

The prevailing hypothesis of ALS is that motoneuron degeneration subsequently induces muscle atrophy and wasting. However, evidence also suggests that ALS is a muscle disease independent of motoneuron degeneration. The results from the current study support the latter. The RNA-seq data from cultured myoblasts (without innervation) suggest cell cell-autonomous effect of G93A on muscle cells. While the current analyses in this study identify axon guidance pathways in EOM satellite cells that may underlie their unique gene program that enhances motoneuron function, the powerfulness of the RNA-seq data is underutilized. I suggest that the authors explore the RNA-seq further by comparing genes and pathways altered by G93A in various muscles to better pinpoint how G93A influences satellite cell function.

Thanks for the comments and advice. Further analysis of the RNA-seq data is planned. As our original sequencing provider became unavailable to us since last year, we are currently negotiating with other sequencing providers. We have deposited the raw data files into the GEO database (GSE249484) to foster further analyses by other researcher teams.

To address the reviewer’s concern, we have added three more supplementary tables for Figure 6, which list the top 20 differentially expressed genes (DEG) (ranked by Log2FC, both the upregulated and downregulated) comparing 1) EOM SCs to their hindlimb and diaphragm counterparts (new Figure 6-table supplement 1); 2) G93A SCs to WT SCs of the same muscle origin (new Figure 6-table supplement 2); 3) G93A hindlimb and diaphragm SCs with and without 3 day-NaBu treatment (new Figure 6-table supplement 3). These three DEG lists are discussed in the results section of the revised manuscript as following (Page 6, Line 237-257).

Figure 4 presentation could be improved by adopting a similar comparison (WT vs G93A) as used in Figure 1-3. The current comparison is not straightforward. In addition, a magnified image of panel A would demonstrate the loss of myoblast homeostasis more clearly. (AKA Figure 2B)

The WT vs G93A comparison was presented in the supplementary figure of Figure 4 (Figure 4-figure supplement 1 in the previous version, and now in Figure 4-figure supplement 2 in the revised version).

As requested, we have added magnified single channel representative images of cultured SCs in the new Figure 4-figure supplement 1 in the revised manuscript.

Co-culture results in Figure 8 are very impressive. It would be nice if the data were quantified. The figure legend states that panel D is the quantification, but I don't see panel D. As the study used rat motoneurons (presumably SOD1 wildtype), it is unknown if G93A motoneurons would respond to muscle-derived CXCL12 similarly to the wildtype motoneurons. This information is crucial for understanding whether the SOD1 mutant ALS1 is a motoneuron disease or muscle disease or both. Some discussion should be provided to reflect the limitation (of not including G93A motoneurons in the coculture).

Panel D (the quantification data) was presented in the original figure setting (but may not be obvious). We have now revised Figure 8 to enlarge panel D to clearly present the quantification data.

We acknowledge the limitation of not including mutant G93A motor neurons in the coculture assay, and have added this important point (and our future plans to do so) in the discussion section of the revised manuscript: (Page 11, Line 445-448)

“However, it is possible that motor neurons carrying ALS mutations may respond differently to Cxcl12 mediated axon guidance than WT motor neurons. This is a limitation of the current study, which will be investigated in future co-culture studies.”

Reviewer #2 (Recommendations For The Authors):

Line 108. The sentence: "Z-stack scans of glycerol-cleared 109 whole muscles were obtained using a high working distance lens in a confocal microscope. The z-stacks were compacted into 2D images by maximal intensity projection" and should be moved to the material and methods section.

Removed from the Result section and added to the Method section as recommended (Page 13, Line 564-568).

Linea 113. The sentence: " In order to quantify the extent of denervation in a categorical manner, NMJs were arbitrarily defined as "well innervated" if SYP staining was present in >60% of the BTX positive area, "partially innervated" if between 60% and 30%, and "poorly innervated" if SYP staining corresponded to less than 30% of the BTX positive area" has already been written in the figure legend.

Thanks for the advice. We have rephrased the sentence to remove the redundant part.

In lines 445-7, it would be better to indicate the enzymatic units instead of the concentrations.

We included enzymatic units for the four enzymes in the Methods Section of revised manuscript (Page 12, Line 497-499).

Reviewer #3 (Recommendations for The Authors):

There are several points that need to be addressed by the authors including:

(a) The authors need to provide experimental evidence as to the mode of action of Na Butyrate and more specifically whether its beneficial effect is mediated by its anti-inflammatory action, inhibition of HDACs, or the combination of several mechanisms. Additionally, it should be clearer why Na Butyrate was administered. The sentence referring to reference 36 is not sufficient and some mechanistic insight needs to be provided in the results section.

Thanks for the great suggestion. We have revised the Results section accordingly to clarify the rationale for NaBu usage (please also see our detailed response to your suggestion above). (Page 4, line 131-134)

(b) Their reason for excluding soleus-derived-satellite cells from the analysis is not valid. Soleus muscles are "more" speared than diaphragm muscles and analysis may help shed light on this observation.

Please see our response to your question (b) in the above public review section.

(c) DATA AVAILABILITY: The RNAseq raw untransformed data has not been provided and Volcano plots are also not shown. I find it quite difficult to follow the results of the RNAseq experiments and this is central to the interpretation of the paper's results. Ideally, one should be able to look at the data and draw his/her own conclusions but as it stands this is difficult to do.

We have uploaded the raw FastQ files and the excel files containing TPM values to the GEO database with the access number GSE249484.

(d) A detailed description of all statistical tests that were used needs to be provided.

Yes, this has been added to the revised manuscript.

(e) Many figure legends are incomplete and some panels are not described appropriately, indicating that the authors need to thoroughly revise all aspects of the manuscript.

We have extensively edited the figure legends to address the issues raised by reviewers.

(f) Line 96-98: it is unlikely that muscles from ALS patients will be biopsied frequently. Furthermore, what biomarkers exactly could be followed in patients in response to therapy? This is unclear.

While it is true that it is not generally part of the diagnostic workup for ALS, muscle biopsy is increasingly being used pre- and post-treatment in ALS clinical trials to examine responses to potential new therapies. Muscle biopsy is also being explored in several ongoing studies as a potential ALS-relevant peripheral tissue amenable to biopsy (as opposed to brain or spinal cord) for predictive, pharmacodynamic, and prognostic biomarkers. This includes studies attempting to recapitulate pathophysiological patient clusters observed in CNS autopsy tissues and studies to detect aberrant TDP-43 aggregates in intramuscular nerve twigs, among others. Indeed, Dr. Ostrow’s clinical duties include performing muscle biopsies and interpreting muscle pathology, and he is involved in several ongoing studies attempting to correlate postmortem CNS and muscle analyses for these purposes.

To avoid potential controversy on the feasibility of multiple biopsies, we rephrased the sentence as follows (Page 3, Line 96-98)

“Characterizing the distinct EOM SC transcriptomic pattern could provide clues for identifying potential biomarkers in therapeutic trials in both ALS patients and animal models, in addition to identifying therapeutic targets.”

(g) Line 388-389. What do the authors mean by this sentence? It is not clear.

Thanks for the comment, we have expended the discussion to make it clearer in the revision. (Page 10, Line 428-431)

“It is possible that the more frequent self-renewal and spontaneous activation of EOM SCs contribute to higher rate of mitochondrial DNA replication, leading to accelerated spreading of mitochondrial DNA defects, resulting in higher proportion of COX-deficient myofibers than other muscles”.

(h) Were the experimenters blinded as to the results shown in Figures 2, 7, 8, and 9?

We endeavored to blind experiments whenever possible. Not all experiments were blinded due to logistic complexity and the clear difference in microscopic and gross appearances of wild-type and mutant muscle. The differences observed in Figures 2, 7, 8, 9 are qualitative (ie more than just quantitative), which should minimize the impact of possible human bias. Additionally, we employed multiple different experimental approaches to assess our hypotheses.

For Fig 2, the physical appearance is notably different between G93A and WT muscles. The different innervation status (Fig 2A) is also not amenable to blinding.

For Fig 7, the expression level of Hmga2, Notch3 and Cxcl12 detected by the qPCR assay are substantially greater in EOM derived SCs than counterparts from other muscles, and these results are also consistent with RNA-Seq, immunofluorescence assays. For Fig 8, the overexpression of Cxcl12 and the coculture with EOM SC derived myotubes not only increased the length of the longest neurites but also promoted axon branching, which can be easily observed.

For Fig 9, only the EOM SC derived myotubes were capable of aligning the neurites along with them on a global scale. This qualitative difference is easy to appreciate, even under low magnification.

(i) Line 64 -65 The authors refer to a very old paper by Fischer et al in 2002 for the expression profile of EOMs. There are more recent papers including that of Eckhardt et al. (eLife 2023, 12:e83618) showing the differences in proteome between EOMs and soleus and EOMs and EDL muscles. There are more than 2000 (and not 300!!) differentially expressed proteins.

Thank you for the newly published reference. We have revised the Introduction section to include this new proteomic study. (Page 2, Line 64-69)

(j) Figure 7 C. The Y axis is mislabeled as they should be log2 fold change and not the growth conditions.

Thank you for catching this. We have fixed it.

(k) In all figures, if each symbol represents the results obtained on 1 mouse, this needs to be clearly stated. What do the panels on the right of Figures 4 and 5B show?

Thanks for the comments. For Figure 1B and 2C, as well as Figure 1-figure supplement 1B, one dot in the box-and-dot plots represents result obtained from 1 mouse. For Figure 3B, one dot represents one round of sorting. Generally, one mouse was euthanized for each round of sorting for HL and diaphragm SCs. But the sorting of EOM SCs could take up to 6 mice (as the EOMs are much smaller). For Figure 4 and 5B, each dot represents one image analyzed. All images were collected from three rounds of sorting. For Figure 5A, each dot represents one replicate of culture. For Figure 5B, each dot represents one image analyzed. All images were collected from three rounds of sorting. We have indicated those details in the revision.

Please also see our response to the 1st question of Reviewer 2 in the public review section.

(l) Figure 6 Table supplement 3 does NOT show the FDR but only the log2 fold change. Please amend.

We have amended the supplementary table accordingly.

Author Response

We would like to thank the editors for giving us an opportunity to address the insightful comments made by the referees. In our response to the comments, we provide a guide to important information that may have been overlooked, and hope to elaborate on the context for better evaluating this study.

As mentioned in the introduction of our manuscript, mosquito-transmitted diseases cause nearly a million deaths every year and significant worldwide morbidity. Moreover, the geographical range of mosquito vectors is rapidly expanding due to climate change and mosquito-borne disease risks are emerging in new parts of the world. DEET was discovered in the 1940s and has remained the primary insect repellent for >70 years in the developed world. The US Environmental Protection Agency (EPA) regulates mosquito repellents, and DEET-based commercial products are typically assigned protection times that vary with concentration. Products with lower concentration need repeated applications, whereas those with higher concentrations feel oily and cost more.

We also mentioned that DEET inhibits mammalian cation channels and human acetylcholinesterase. The latter is a target of carbamate insecticides that are commonly used in disease-endemic areas, raising additional concerns about prolonged use of DEET. DEET is also a solvent and damages several forms of plastics, synthetic fabrics, and painted . Unfortunately, DEET has been of little value in disease control in Africa and Asia. Even in developed countries, a natural, cosmetically pleasant alternative could benefit millions of people who currently avoid repellents.

Innovation in finding new repellents has been slow due to limitations in current research approaches and high costs for EPA registration (specially for synthetic compounds). Since DEET only five additional actives have been approved by the EPA for repellent products. In the 20+ years since discovery of insect odorant receptors from genomes, not a single novel repellent compound has been identified registered by the EPA. Thus, there is a both a strong need for new approaches to find insect repellents and need for new active ingredients that are safe and strategically effective. In fact, this goal of finding new mosquito repellents has been the topic of multiple Gates Foundation Grand Challenge grants, and numerous NIH funded grants to many research groups around the world.

Reviewer #1 (Public Review):

Summary:

In this manuscript, the authors set up a pipeline to predict insect repellents that are pleasant and safe for humans. This is done by daisy-chaining a new classification model based on predicting repellents with a published model on predicting human perception. Models use a feature-engineered selection of chemical features to make their predictions. The predicted molecules are then validated against a proxy humanoid (heated brick) and its safety is tested by molecular assays of human cells. The humanistic approach to modeling these authors have taken (which considers cosmetic/aesthetic appeal and safety) is novel and a necessary step for consumer usage. However, the importance of pleasantness over effectiveness is still up for debate (DEET is unpleasant but still used often) and the generalization of safety tests is unknown and assumed. The effectiveness of the prediction models is also still warranted. They pass the authors' own behavioral tests, but their contribution to the field is unknown as both models (new and published) have not been rigorously benchmarked to previous models. Moreover, the author's breadth of literature in this field is sparse, ignoring directly related studies.

Strengths:

Humanistic approach to modeling considers pleasantness and safety. Chaining models can help limit the candidate odorants from the vastness of odor space.

Weaknesses:

The current models need to be bench-marked against leading models predicting similar outcomes. Similarly, many of these papers need to be addressed and discussed in the introduction. The authors might even consider their data sources for model training to increase performance and lexical categorization for interoperability. For instance, the Dravnikes data lexicon, currently used in the human perception lexicon, has been highly criticized for its overlapping and hard-to-interpret descriptive terms ("FRAGRANT", "AROMATIC").

Human Perception:

Khan, R. M., Luk, C. H., Flinker, A., Aggarwal, A., Lapid, H., Haddad, R., & Sobel, N. (2007). Predicting odor pleasantness from odorant structure: pleasantness as a reflection of the physical world. Journal of Neuroscience, 27(37), 10015-10023.

Keller, A., Gerkin, R. C., Guan, Y., Dhurandhar, A., Turu, G., Szalai, B., ... & Meyer, P. (2017). Predicting human olfactory perception from chemical features of odor molecules. Science, 355(6327), 820-826.

Gutiérrez, E. D., Dhurandhar, A., Keller, A., Meyer, P., & Cecchi, G. A. (2018). Predicting natural language descriptions of mono-molecular odorants. Nature communications, 9(1), 4979.

Lee, B. K., Mayhew, E. J., Sanchez-Lengeling, B., Wei, J. N., Qian, W. W., Little, K. A., ... & Wiltschko, A. B. (2023). A principal odor map unifies diverse tasks in olfactory perception. Science, 381(6661), 999-1006.

Author Response: The human perception predictions were performed using models that we had reported in two earlier publications: Kowalewski & Ray, iScience (2020b) and Kowalewski, Huynh & Ray, Chem. Senses (2021). Three of the four references pointed out by the referee were cited in these prior studies, which involved computational validation by predicting on a test set of the data which was left out of training (as typically done), and also predicting across different human studies with a high degree of success. A rigorous benchmarking of the odor perception models was done in Kowalewski, Huynh & Ray, Chem. Senses (2021) and a mini-review published in the same issue of the journal by Gerkin, Chem. Senses, (2021). This included a favorable comparison with the two references indicated by the referee: Keller et al. Science (2017) as well as the Gutiérrez et. al. Nat. Communication (2018). The 4th reference, Lee et al, Science (2023) describes a neural network approach and was published much after our mosquito behavior studies were completed. Although using an advanced Neural network model Lee et al. worked with 2-D structures of compounds in contrast to our 3-D approach. They also did not report cross-study validations or comparisons with Keller et al, 2017 or benchmark to past studies, so it is difficult to compare advances if any.

The intent of the current study was to move beyond testing approaches, of which there are many, and instead work on a practical use case. As we see it, it is not necessarily the prediction of fragrance character or quality alone that matters but overlap with other predicted bioactivities. From the perspective of human use, a molecule with a pleasing scent that also repels insects is likely to be far more useful than one with an unappealing scent. Accordingly, our task in this study was to select molecules that fit into specific use categories: display strong insect repellency, have pleasing scent profiles, are natural in origin and are potentially repurposed from flavors and fragrances.

Insect Repellents:

Wright, R. H. (1956). Physical basis of insect repellency. Nature, 178(4534), 638-638.

Katritzky, A. R., Wang, Z., Slavov, S., Tsikolia, M., Dobchev, D., Akhmedov, N. G., ... & Linthicum, K. J. (2008). Synthesis and bioassay of improved mosquito repellents predicted from chemical structure. Proceedings of the National Academy of Sciences, 105(21), 7359-7364.

Bernier, U. R., & Tsikolia, M. (2011). Development of Novel Repellents Using Structure− Activity Modeling of Compounds in the USDA Archival Database. In Recent Developments in Invertebrate Repellents (pp. 21-46). American Chemical Society.

Author response: The Katritzky et. al. PNAS (2008) paper is cited in our study, and we have indicated that the chemical analogs reported therein are part of the training data set in our study. We thank the reviewer for pointing us to the book chapter by Bernier & Tsikolia (2011), which reviews the QSAR approaches taken for repellent discovery and in large measure focuses on the Katritzky et. al. PNAS (2008) paper. We did cite two relevant studies by Uli Bernier, but agree that citation of the book chapter would make a nice addition.

The current study assumes that insect repellents repel via their odor valence to the insect, but this is not accurate. Insect repellents also mask the body odor of humans making them hard to locate. The authors need to consult the literature to understand the localization and landing mechanisms of insects to their hosts. Here, they will understand that heat alone is not the attractant as their behavioral assay would have you believe. I suggest the authors test other behaviour assays to show more convincing evidence of effectiveness. See the following studies:

De Obaldia, M. E., Morita, T., Dedmon, L. C., Boehmler, D. J., Jiang, C. S., Zeledon, E. V., ... & Vosshall, L. B. (2022). Differential mosquito attraction to humans is associated with skin-derived carboxylic acid levels. Cell, 185(22), 4099-4116.

McBride, C. S., Baier, F., Omondi, A. B., Spitzer, S. A., Lutomiah, J., Sang, R., ... & Vosshall, L. B. (2014). Evolution of mosquito preference for humans linked to an odorant receptor. Nature, 515(7526), 222-227.

Wei, J. N., Vlot, M., Sanchez-Lengeling, B., Lee, B. K., Berning, L., Vos, M. W., ... & Dechering, K. J. (2022). A deep learning and digital archaeology approach for mosquito repellent discovery. bioRxiv, 2022-09.

Author response: In this study we took an unbiased approach to compile the training data set, including several known insect repellents of varying chemical structures and volatility, for most of which there is no information on how they are sensed by insects. Not surprisingly, the repellents we identified are varied in structure and in functional groups, and are likely detected in more than one way by the mosquitoes, using olfactory and/or gustatory systems. We did not consider “masking” of skin attraction as a factor in the training data set in this study, which precluded the need to discuss the papers pointed out by the referee in any detail. In fact there is an extremely vast and rich body of literature regarding human skin odor, CO2 and breath emanations, which includes our own contributions of research and review articles that are not discussed in the current paper.

We did in fact conduct human arm-in-cage experiments with a few of the compounds reported in this study using female Aedes aegypti mosquitoes; a preprint describes the smaller scale analysis, the results of which show strong repellency, in Boyle et. al. bioRxiv (2016) https://doi.org/10.1101/060178 (Figure 4). However, heat offers a practical proxy for evaluating prospective repellents in a high-throughput manner. It would certainly be desirable to further evaluate additional candidates from the heat attraction assay with human subjects in the future.

We thank the reviewer for pointing out the preprint by Wei, et. al. bioRxiv (2022). Our approaches differ in that Wei et al do not consider properties such as fragrance and toxicity. We also cannot assume that their newer neural network model is superior because although the model uses a large training dataset, it does not use 3D chemical structures that are extremely relevant for biological activity. While very little information is available for the actives reported in Wei et. al., we independently evaluated their top compounds similar or better than DEET (CAS#3731-16-6, 4282-32-0, 2040-04-2, 32940-15-1 and 3446-90-0) and could not find information about toxicity, smell, or natural source. In contrast, the top repellents that we identify here as similar or better than DEET (N=8) are all classified as GRAS (Generally Regarded as Safe) compounds by the Flavor and Extract Manufacturers (FEMA), are all naturally occurring (plum, jasmin, mushroom, grapes, etc), and have pleasant smells. The Dermal toxicity values in rabbits are known for six of our compounds and are at the best possible levels (5000mg/kg).

Reviewer #2 (Public Review):

Summary:

This is an interesting study that seeks to identify novel mosquito repellents that smell attractive to humans.

Strengths:

The combination of standard machine learning methods with mosquito behavioral tests is a strength.

Weaknesses:

The study would be strengthened by describing how other modern ML approaches (RF, decision trees) would classify and identify other potential repellents.

Author response: The current approach already shows a success rate >85% for repellency coefficient >0.5 and identifies eight naturally occurring GRAS compounds with repellency as strong as or greater than DEET. This substantially expands the repertoire of strong natural repellents. Since the 1950s only six active ingredients have been registered by US EPA for use in topical repellents, of which only two are natural in origin (Oil of lemon eucalyptus and catmint oil) and they typically do not protect as well as DEET does. That being said, we have since explored other predictive algorithms, for instance Neural Networks. The experimental evaluation of these newer pipelines will take significant resources and time and will be the focus of future grants.

A comparison in the repellent activity between DEET and the top ten hits identified in this new study indicates little change in repellent activity (~3%), suggesting that DEET remains the gold standard. Without additional toxicity tests, the study is arguably incremental. The study's novelty should be better clarified.

Author response: There is an urgent need to find new insect repellents that have better chances of being adopted by people who avoid DEET, such as in Africa and Asia. Having more natural actives that are effective, expands the tools against disease transmitting mosquitoes. As mentioned above, the top repellents that we identified as similar to or better than DEET (N=8) are all classified as GRAS (Generally Regarded as Safe) compounds by the Flavor and Extract Manufacturers (FEMA), are all naturally occurring (plum, jasmin, mushroom, grapes), and have pleasant smells. The Dermal toxicity values in rabbits are known for six and they are of the best possible levels (5000mg/kg).

The Methods in the repellency tests are sparse, and more information would be useful. Testing the top repellents at low doses (<<1%) and for long periods (2-12 h) would strengthen the manuscript. Without this information, the manuscript is lacking in depth.

Author response: The US Environmental Protection Agency (EPA) regulates mosquito repellents, and DEET-based commercial products are typically assigned protection times that vary with concentration (10% ~2 hrs, 30% ~5hrs, 100% ~8hrs). These would be the relevant concentrations for testing protection times on human volunteers, not lower as suggested. Such studies fall within the realm of EPA registration efforts, involving extensive GLP-testing for safety, physical chemistry, and Human Subjects Board approvals. This is outside the scope of the current study and is typically accomplished during development efforts.

Testing human subjects on their olfactory perceptions of the repellents would also increase the depth and utility of the manuscript. Without additional experiments, the authors' conclusions lack support and have limited impact on the state-of-the-art.

This manuscript is a mix of different approaches, which makes it lack cohesion. There is the ML method for classifying new repellents that smell good, but no testing of the repellents on human volunteers. The repellents are not tested at realistic concentrations and durations. And the calcium mobilization test is strange and makes little sense in the context of the other experiments and framing of the manuscript.

Author response: The human olfaction validation that we present in this paper is consistent with most current publications in the field (for example, Keller et al, Gutiérrez et al.). More systematic validation of the human odor character prediction pipelines used was presented in two previous papers Kowalewski & Ray, iScience (2020b) and Kowalewski, Huynh & Ray, Chem. Senses (2021) and a mini-review published in the same issue of the journal by Gerkin, Chem. Senses, (2021).

Reviewer #3 (Public Review):

While I am not a specialist in this field, I do have some knowledge of the subject matter and the computational aspects involved. The authors employ simple machine learning techniques (such as SVM) for the following purposes:

(a) Prediction of aversive valence.

(b) Predicting anti-repellent chemicals.

(c) Predicting calcium mobilization.

The approach is commonplace in chemoinformatics literature.

Weaknesses:

• All the above models are presented discretely, making it difficult to discern experiment design principles and connectedness.

• The ML work is rudimentary, lacking adequate details. Chemoinformatics has reached great heights, and SVM does not seem contemporary.

• There is significant existing research on finding repellents.

Author response: In the current study, we aimed to showcase how computational research may be combined with basic science to create scalable pipelines that address real world problems, rather than to demonstrate methodological novelty of chemoinformatics approaches. Specifically we wanted to use different predictive models to identify compounds that display strong insect repellency, have pleasing scent profiles, are natural in origin and are potentially repurposed from flavors and fragrances. Unfortunately, there is very little existing research on insect repellents that have these types of properties, which would make them better candidates for EPA registration. Most tested compounds are synthetic, and are often analogs of known repellents like DEET, and necessitate substantial time and resources to register. Moreover the identities of chemosensory receptors that are responsible for repellency to DEET and other compounds, and that are conserved across Anopheles, Aedes and Culex mosquitoes are not known.

It is true that the field of cheminformatics has experimented with a variety of newer approaches, based in part on neural networks (e.g., Graph Neural Networks and graph embeddings to encode chemical structure rather than a more conventional Extended Connectivity Fingerprint (ECFP)). Importantly, however, novelty does not imply usefulness. The mosquito behavior experiments that we present show a very high success rate (>85%), validating our approach and identifying several excellent candidates already.

Strengths:

• Authors attempt to make a case for calcium mobilization in the context of repellency. This aspect sounds interesting but is not surprising.

• Behavioral profiling of repellents could be useful.

Author Comment: We thank the referee for this comment. We have indeed done behavioral profiling for several repellents that evoke calcium mobilization, but we do not see any clear correlation thus far.

Author Response

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

eLife assessment

This manuscript presents a valuable approach to exploring CD4+ T-cell response in mice across stimuli and tissues through the analysis of their T-cell receptor repertoires. The authors use a transgenic mouse model, in which the possible diversity of the T-cell receptor repertoire is reduced, such that each of a diverse set of immune exposures elicits more detectably consistent T-cell responses across different individuals. However, whereas the proposed experimental system could be utilized to study convergent T-cell responses, the analyses done in this manuscript are incomplete and do not support the claims due to limitations in the statistical analyses and lack of data/code access.

We worked to address the reviewers' concerns below, point-by-point.

All data on immune repertoires are deposited here: https://figshare.com/articles/dataset/Convergence_plasticity_and_tissue_residence_of_regulatory_and_effector_T_cell_response/22226155

We added the Data availability statement to the manuscript.

Public Reviews:

Reviewer #1 (Public Review):

The authors investigate the alpha chain TCR landscape in conventional vs regulatory CD4 T cells. Overall I think it is a very well thought out and executed study with interesting conclusions. The authors have investigated CDR3 alpha repertoires coupled with a transgenic fixed CDR3beta in a mouse system.

Strengths:

• One of a kind evidence and dataset.

• State-of-the-art analyses using tools that are well-accepted in the literature.

• Interesting conclusions on the breadth of immune response to challenges across different types of challenges (tumor, viral and parasitic).

Thank you for the positive view.

Weaknesses:

• Some conclusions regarding the eCD4->eTreg transition are not so strong using only the data.

The overlaps between the top-nucleotide clones in both LLC and PYMT challenges are prominently above the average, and this result is reproducible in lungs and skin, so we have no doubts based on these data. Further experiments with different methods, including tracking the clonal fates, should clarify and confirm/correct/disprove our findings.

• Some formatting issues.

We are working on the manuscript to correct minor errors and formatting.

Reviewer #2 (Public Review):

This study investigates T-cell repertoire responses in a mouse model with a transgenic beta chain, such that all T-cells in all mice share a fixed beta chain, and repertoire diversity is determined solely by alpha chain rearrangements. Each mouse is exposed to one of a few distinct immune challenges, sacrificed, and T-cells are sampled from multiple tissues. FACS is used to sort CD4 and Treg cell populations from each sample, and TCR repertoire sequencing from UMI-tagged cDNA is done.

Various analyses using repertoire diversity, overlap, and clustering are presented to support several principal findings: 1) TCR repertoires in this fixed beta system have highly distinct clonal compositions for each immune challenge and each cell type, 2) these are highly consistent across mice, so that mice with shared challenges have shared clones, and 3) induction of CD4-to-Treg cell type transitions is challenge-specific.

The beta chain used for this mouse model was previously isolated based on specificity for Ovalbumin. Because the beta chain is essential for determining TCR antigen specificity, and is highly diverse in wildtype mice, I found it surprising that these mice are reported to have robust and consistently focused clonal responses to very diverse immune challenges, for which a fixed OVA-specific beta chain is unlikely to be useful. The authors don't comment on this aspect of their findings, but I would think it is not expected a priori that this would work. If this does work as reported, it is a valuable model system: due to massively reduced diversity, the TCR repertoire response is much more stereotyped across individual samples, and it is much easier to detect challenge-specific TCRs via the statistics of convergent responses.

This was to some extent expected, since these mice live almost normally and have productive adaptive immune responses and protection. In real life, there are frequent TCR-pMHC interactions where the TCR-alpha chain dominates (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC5701794/; https://pubmed.ncbi.nlm.nih.gov/37047500/). On the fixed TCR-beta background this mechanics starts working full-fledged, essentially substituting TCR-beta diversity, at the extent of relatively simplified TCRab repertoire and probably higher cross-reactivity.

We agree that this is a valuable model, for sure, and indicated this in the last sentence of our Discussion. Now we are also adding this point to the abstract.

While the data and analyses present interesting signals, they are flawed in several ways that undermine the reported findings. I summarize below what I think are the most substantive data and analysis issues.

(1) There may be systematic inconsistencies in repertoire sampling depth that are not described in the manuscript. Looking at the supplementary tables (and making some plots), I found that the control samples (mice with mock challenge) have consistently much shallower sampling-in terms of both read count and UMI count-compared with the other challenge samples. There is also a strong pattern of lower counts for Treg vs CD4 cell samples within each challenge.

The immune response of control mice is less extensive, as it should be. Just like the fact that the number of Tregs in tissues is lower than CD4, this is normal. So this all follows the expectations. But please note that we were very accurate everywhere with appropriate data normalisation, using all our previous extensive experience (https://pubmed.ncbi.nlm.nih.gov/29080364/).

In particular (now adding more relevant details to Methods):

For diversity metrics calculations, we randomly sampled an equal number of 1000 UMI from each cloneset. Samples with UMI < 700 were excluded from analysis.

For amino acid overlap metrics calculations, we selected top-1000 largest clonotypes from each cloneset. Samples with clonotype counts < 700 were excluded from analysis.

For nucleotide overlaps metrics calculations (eCD4-eTreg), we selected top-100 clonotypes from each cloneset. Samples with clonotypes < 100 were excluded from analysis.

The top N clonotypes were selected as the top N clonotypes after randomly shuffling the sequences and aligning them in descending order. This was done in order to get rid of the alphabetical order for clonotypes with equal counts (e.g. count = 1 or 2).

Downsampling was carried out using software vdjtools v.1.2.1.

(2) FACS data are not reported. Although the graphical abstract shows a schematic FACS plot, there are no such plots in the manuscript. Related to the issue above, it would be important to know the FACS cell counts for each sample.

Yes, we agree that this is valuable information that should be provided. Unfortunately, this data has not been preserved.

(3) For diversity estimation, UMI-wise downsampling was performed to normalize samples to 1000 random UMIs, but this procedure is not validated (the optimal normalization would require downsampling cells). What is the influence of possible sampling depth discrepancies mentioned above on diversity estimation? All of the Treg control samples have fewer than 1000 total UMIs-doesn't that pose a problem for sampling 1000 random UMIs?

Indeed, I simulated this procedure and found systematic effects on diversity estimates when taking samples of different numbers of cells (each with a simulated UMI count) from the same underlying repertoire, even after normalizing to 1000 random UMIs. I don't think UMI downsampling corrects for cell sampling depth differences in diversity estimation, so it's not clear that the trends in Fig 1A are not artifactual-they would seem to show higher diversity for control samples, but these are the very same samples with an apparent systematic sampling depth bias.

We evaluated this approach through all our work, and summarised in the ref: https://pubmed.ncbi.nlm.nih.gov/29080364/. Altogether, normalising to the same count of randomly sampled UMI seems to be the best approach (although, preferably, the initial sequencing depth should be essentially higher for all samples than the sampling threshold used). Initial sorting of identical numbers of cells and ideally uniform library preparation and sequencing is generally not realistic and does not work in the real world, while UMI downsampling does the same work much better.

(4) The Figures may be inconsistent with the data. I downloaded the Supplementary Table corresponding to Fig 1 and made my own version of panels A-C. This looked quite different from the diversity estimations depicted in the manuscript. The data does not match the scale or trends shown in the manuscript figure.

There was a wrong column for Chao1, now correcting. Also, please note that we only used samples with > 700 UMI. Supplementary Table now corrected accordingly. Also, please note that Figure 1 shows the results for lung samples only.

(5) For the overlap analysis, a different kind of normalization was performed, but also not validated. Instead of sampling 1000 UMIs, the repertoires were reduced to their top 1000 most frequent clones. It is not made clear why a different normalization would be needed here. There are several samples (including all Treg control samples) with only a couple hundred clones. It's also likely that the noted systematic sampling depth differences may drive the separation seen in MDS1 between Treg and CD4 cell types. I also simulated this alternative downsampling procedure and found strong effects on MDS clustering due to sampling effects alone.

That’s right, for the overlap analysis (which values are mathematically proportional to the clonotype counts in both compared repertoires, so the difference in the counts causes major biases) the right way to do it is to choose the same number of clonotypes. See Ref. https://pubmed.ncbi.nlm.nih.gov/29080364/.

We kept only samples with > 700 for the overlap analyses. Some relatively poor samples are present in all challenges, while MDS1 localization has clear reproducible logic, so we are confident in these results.

It is not made clear how the overlap scores were converted to distances for MDS. It's hard to interpret this without seeing the overlap matrix.

This is a built-in feature in VDJtools software (https://pubmed.ncbi.nlm.nih.gov/26606115/). See also here: https://vdjtools-doc.readthedocs.io/en/master/overlap.html.

(6) The cluster analysis is superficial, and appears to have been cherry-picked. The clusters reported in the main text have illegibly small logo plots, and no information about V/J gene enrichments. More importantly, as the caption states they were chosen from the columns of a large (and messier-looking) cluster matrix in the supplementary figure based on association with each specific challenge. There's no detail about how this association was calculated, or how it controlled for multiple tests. I don't think it is legitimate to simply display a set of clusters that visually correlate; in a sufficiently wide random matrix you will find columns that seem to correlate with any given pattern across rows.

Particular CDR3 sequences and VJ segments do not mean much for the results of this manuscript. Logos are given just for visual explanation of how the consensus motifs of the clusters look like.

We now add two more Supplementary Tables and a Supplementary Figure with full information about clusters.

We disagree that the Supplementary Figure 1 (representing all the clusters) looks “messy”. Vice versa, it is surprisingly “digital”, showing the clear patterns of responses and homings. This becomes clear if you visually study it for a while. But yes, it is too big to let the reader focus on this or that aspect. That is why we need to select TCR clusters to illustrate this or that aspect discussed in the work, but they were selected from the overall already structured picture.

(7) The findings on differential plasticity and CD4 to Treg conversion are not supported. If CD4 cells are converting to Tregs, we expect more nucleotide-level overlap of clones. This intuition makes sense. But it seems that this section affirms the consequent: variation in nucleotide-level clone overlap is a readout of variation in CD4 to Treg conversion. It is claimed, based on elevated nucleotide-level overlap, that the LLC and PYMT challenges induce conversion more readily than the other challenges. It is not noted in the textual interpretations, but Fig 4 also shows that the control samples had a substantially elevated nucleotide-level overlap. There is no mention of a null hypothesis for what we'd expect if there was no induced conversion going on at all. This is a reduced-diversity mouse model, so convergent recombination is more likely than usual, and the challenges could be expected to differ in the parts of TCR sequence space they induce focus on. They use the top 100 clones for normalization in this case, but don't say why (this is the 3rd distinct normalization procedure).

Your point is absolutely correct: “This is a reduced-diversity mouse model, so convergent recombination is more likely than usual”. Distinct normalisation procedure was required to focus on the most expanded clonotypes to avoid the tail of (presumably cross-reactive) and identical TCRs present in all repertoires in these limited-repertoire mice. So we downsampled as strictly as possible to minimise this background signal of nucleotide overlap, and only this strict downsampling to the top-100 clonotypes allowed us to visualise the difference between the challenges. This is a sort of too complicated explanation that would overload the manuscript. But your comments and our answers will be available to the reader who wants to go into all the details.

The observed (at this strict downsampling) overlaps between the top-nucleotide clones in both LLC and PYMT challenges are prominently above the average, and this result is reproducible in lungs and skin, so we have no doubts in interpretations based on these data. Further experiments with different methods, including tracking the clonal fates, should clarify and confirm/correct/disprove our findings.

Although interpretations of the reported findings are limited due to the issues above, this is an interesting model system in which to explore convergent responses. Follow-up experimental work could validate some of the reported signals, and the data set may also be useful for other specific questions.

Yes, thank you for your really thorough analysis. We fully agree with your conclusion.

Reviewer #3 (Public Review):

Nakonechnaya et al present a valuable and comprehensive exploration of CD4+ T cell response in mice across stimuli and tissues through the analysis of their TCR-alpha repertoires.

The authors compare repertoires by looking at the relative overlap of shared clonotypes and observe that they sometimes cluster by tissue and sometimes by stimulus. They also compare different CD4+ subsets (conventional and Tregs) and find distinct yet convergent responses with occasional plasticity across subsets for some stimuli.

The observed lack of a general behaviour highlights the need for careful comparison of immune repertoires across cell subsets and tissues in order to better understand their role in the adaptive immune response.

In conclusion, this is an important paper to the community as it suggests several future directions of exploration.

Unfortunately, the lack of code and data availability does not allow the reproducibility of the results.

Thank you for your positive view.

All data on immune repertoires are deposited here: https://figshare.com/articles/dataset/Convergence_plasticity_and_tissue_residence_of_regulatory_and_effector_T_cell_response/22226155

We added the Data availability statement to the manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

• In the manuscript at "yielding 13,369 {plus minus} 1,255 UMI-labeled TCRα cDNA molecules and 3233 {plus minus} 310 TCRα CDR3 clonotypes per sample" I'm not sure how can there be fewer unique DNA molecules than clonotypes in each sample.

That was our mistake for sure, now corrected.

• In the manuscript at "This indicates that the amplitude and focused nature of the effector and regulatory T cell response in lungs is generally comparable."

I'm not sure it's possible to conclude that a drop in diversity in all conditions necessarily signals a focused nature. Since at this stage, the nature of the colotypes was not compared between conditions, it is not possible to claim a focused nature of the response.

We have softened the wording:

"This could indicate that the amplitude and focused nature of the effector and regulatory T cell response in lungs is generally comparable."

• What are your thoughts on why there is such a large overlap between Treg and Teff in the Lung in control? For some replicates it is almost as much as a post-LLC challenge!

There is some natural dispersion in the data, which is generally expectable. The overlaps between the top-nucleotide clones in both LLC and PYMT challenges are prominently above the average, and this result is reproducible in lungs and skin, so we have no doubts based on these data. Further experiments with different methods, including tracking the clonal fates, should clarify and confirm/correct/disprove our findings.

• In the manuscript at "These results indicate that distinct antigenic specificities are generally characteristic for eTreg cells that preferentially reside in particular lymphatic niches" I'm not sure we can conclude this from the Figure. Wouldn't you expect the samples to be grouped by color (the different challenges)? Maybe I'm not understanding the sentence!

This is a different story, about resident Tregs, irrespective of the challenge.

The whole explanation is here in the text:

“Global CDR3α cluster analysis revealed that characteristic eTreg TCR motifs were present in distinct lymphatic tissues, including spleen and thymus, irrespective of the applied challenge (Supplementary Fig. 1). To better illustrate this phenomenon, we performed MDS analysis of CDR3α repertoires for distinct lymphatic tissues, excluding the lungs due to their otherwise dominant response to the current challenge. This analysis demonstrated close proximity of eTreg repertoires obtained from the same lymphatic tissues upon all lung challenges and across all animals (Fig. 5a, b). These results indicate that distinct antigenic specificities are generally characteristic for eTreg cells that preferentially reside in particular lymphatic niches. Notably, the convergence of lymphatic tissue-resident TCR repertoires was less prominent for the eCD4 T cells (Fig. 5c, d).”

And in the abstract:

“Additionally, our TCRα repertoire analysis demonstrated that distinct antigenic specificities are characteristic for eTreg cells residing in particular lymphatic tissues, regardless of the challenge, revealing the homing-specific, antigen-specific resident Treg populations. ”

• In the manuscript at " Notably, the convergence of lymphatic tissue-resident TCR repertoires was less prominent for the eCD4 T cells ":

5b and 5d seem to have the same pattern: Spleen and MLN group together, AxLN and IgLN together and thymus is separate. Do you mean to say that the groups are more diffuse? I feel like the pattern really is the same and it's likely due to some noise in the data…

Yes, we just mean here that eTreg groups are less diffuse - means more convergent.

• I'm not sold on the eCD4 to eTreg conversion evidence. Why only limit to the top 100 clones? The top 1000 clones were used in previous analyses! Moreover, the authors claim that calculating relative overlap (via F2) of matching CDR3+V+J genes is evidence of a conversion between eCD4 and eTreg. I think to convince myself of a real conversion, I would track the cells between groups, unfortunately, I'm not sure how to track this.. Maybe looking at the thymus population? For example, what is the overlap in the thymus vs. after the challenge? I don't have an answer on how to verify but I feel that this conclusion is a bit on the weaker end.

Distinct normalisation procedure was required to focus on the most expanded clonotypes to avoid the tail of (presumably cross-reactive) and identical TCRs present in all repertoires in these limited-repertoire mice. So we downsampled as strictly as possible to minimise this background signal of nucleotide overlap, and only this strict downsampling to the top-100 clonotypes allowed us to visualise the difference between the challenges. This is a sort of too complicated explanation that would overload the manuscript. But your comments and our answers will be available to the reader who wants to go into all the details.

The observed (at this strict downsampling) overlaps between the top-nucleotide clones in both LLC and PYMT challenges are prominently above the average, and this result is reproducible in lungs and skin, so we have no doubts in interpretations based on these data. Further experiments with different methods, including tracking the clonal fates, should clarify and confirm/correct/disprove our findings.

• There is a nuance in the analysis between Figure 3 and Figure 5 which I think I am not grasping. Both Figures use the same method and the same data but what is different? I think the manuscript would benefit from making this crystal clear. The conclusions will likely be more evident as well!

As explained in the text and above, on Figure 5 “we performed MDS analysis of CDR3α repertoires for distinct lymphatic tissues, excluding the lungs due to their otherwise dominant response to the current challenge.”

The idea of this mini-chapter of the manuscript is to reveal tissue-resident Tregs, distinct for distinct tissues, resident there in all these mice, irrespectively of the challenge we applied. And they are really there (!).

• Do the authors plan to share their R scripts?

All calculations were performed in VDJtools. R was only used to build figures. Corrected this in Methods.

Minor typos and formatting issues to address:

• Typo in Figure 2a the category should read "worm" instead of "warm"

Corrected.

• Figure 2a heatmap is missing a color bar indicating the value ranges

The detailed information can be found in additional Supplementary materials.

• Figure 2f is never mentioned in the manuscript!

Corrected.

• "eTreg repertoire upon lung challenge is reflected in the draining lymph node" - the word upon is of a lower size

Corrected.

• The authors should make the spelling of eTreg uniform across the manuscript (reg in subscript vs just lower case letters. Same goes for CDR3a vs CDR3\alpha

Corrected.

• Figure 4a-d p-values annotations are not shown. Is it because they are not significant?

Corrected.

• The spelling of FACS buffer should be uniform (FACs vs FACS, see methods)

Corrected.

• In the gating strategy, I would make a uniform annotation for the cluster of differentiation, for example, "CD44 high" vs "CD44^{hi}", pos vs + etc.

Corrected.

• Citation for MIGEC software (if available) is missing from methods

Present in the text so probably sufficient.

Reviewer #2 (Recommendations For The Authors):

I noticed the data was made available via Figshare in the preprint, but there is no data availability statement in the current ms.

We provided Data availability statement.

The methods state that custom scripts were written to perform the various analyses. Those should be made available in a code repository, and linked in the ms.

All calculations were performed in VDJtools. R was only used to build figures. Corrected this in Methods.

The title mentioned "TCR repertoire prism", so I thought "prism" was the name of a new method or software. But then the word "prism" didn't appear anywhere in the ms.

We just mean viewing or understanding something from a different perspective or through a lens that reveals different aspects or nuances.

Figure 1D lacks an x-axis label.

Worked on the figures in general.

Reviewer #3 (Recommendations For The Authors):

• The paper is very concise, possibly a bit too much. It could use additional explanations to properly affirm its relevance, for example:

why the choice of fixing the CDR3beta background?

To make repertoire more similar across the mice, and to track all the features of repertoire using only one chain.

to what it is fixed?

As explained in Methods:

“C57BL/6J DO11.10 TCRβ transgenic mice (kindly provided by Philippa Marrack) and crossed to C57BL/6J Foxp3eGFP TCRa-/- mice.”

What do you expect to see and not to see in this specific system and why it is important?

As stated above: we expected repertoire to be more similar across the mice, and it is important to find antigen-specific TCR clusters across mice, and to be able to track all the features of the TCR repertoire using only one chain.

Does this system induce more convergent responses? If so, can we extrapolate the results from this system to the full alpha-beta response?

Such a model, compared to conventional mice, is much more powerful in terms of the ability of monitoring convergent TCR responses. At the same time, it behaves natural, mice live almost normally, so we believe it reflects natural behaviour of the full fledged alpha-beta T cell repertoire.

• Is the lack of similarity of other tissues to Lung/MLN due to a lack of a response?

As indicated in the title of the corresponding mini-chapter: “eTreg repertoire upon lung challenge is reflected in the draining lymph node”. And conclusion of this mini-chapter is that “these results demonstrate the selective tissue localization of the antigen-focused Treg response. ”

Can you do a dendrogram like 2a for the other tissues to better clarify what is going on there? There is space in the supplementary material.

We built lots of those, but in such single dimension mostly they are less informative compared to 2D MDS plots.

• Figure 5 seems a bit out of place as it looks more related to Figure 2. It could maybe be integrated there, sent to supplementary or become Figure 3?

This is a different story, about resident Tregs, irrespective of the challenge.

The whole explanation is here in the text:

“Global CDR3α cluster analysis revealed that characteristic eTreg TCR motifs were present in distinct lymphatic tissues, including spleen and thymus, irrespective of the applied challenge (Supplementary Fig. 1). To better illustrate this phenomenon, we performed MDS analysis of CDR3α repertoires for distinct lymphatic tissues, excluding the lungs due to their otherwise dominant response to the current challenge. This analysis demonstrated close proximity of eTreg repertoires obtained from the same lymphatic tissues upon all lung challenges and across all animals (Fig. 5a, b). These results indicate that distinct antigenic specificities are generally characteristic for eTreg cells that preferentially reside in particular lymphatic niches. Notably, the convergence of lymphatic tissue-resident TCR repertoires was less prominent for the eCD4 T cells (Fig. 5c, d).”

And in the abstract:

“Additionally, our TCRα repertoire analysis demonstrated that distinct antigenic specificities are characteristic for eTreg cells residing in particular lymphatic tissues, regardless of the challenge, revealing the homing-specific, antigen-specific resident Treg populations. ”

• Have you explored more systematically the role of individual variability? If you stratify by individual, do you observe any trend? If not this is also an interesting observation to highlight and discuss.

This is inside the calculations and figures/ one dot = 1 mice, so this natural variation is there inside.

• Regarding the MDS plots: why are 2 dimensions the right amount? Maybe with 3, you can see both tissue specificity and stimuli contributions. Can you do a stress vs # dimensions plot to check what should be the right amount of dimensions to more accurately reproduce the distance matrix?

Tissue specificity and stimuli contribution is hard to distinguish without focussing on appropriate samples, as we did on Fig. 3 and 5. The work is already not that simple as is, and attempting to analyse this in multidimensional space is far beyond our current abilities. But this is an interesting point for future work, thank you.

• Figure 2: A better resolution is needed in order to properly resolve the logo plots at the bottom.

Yes, we worked on Figures, and also provide new Supplementary Figure with all the logos.

• No code or data are made available. There is also a lack of supplementary figures that complement and expand the results presented in the main text.

We believe that the main text, although succinct, contains lots of information to analyse and conclusions (preliminary) to make. So we do not see it rational to overload it further.

Author Response

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

Reviewer #1 (Public Review):

The manuscript investigates the role of membrane contact sites (MCSs) and sphingolipid metabolism in regulating vacuolar morphology in the yeast Saccharomyces cerevisiae. The authors show that tricalbin (1-3) deletion leads to vacuolar fragmentation and the accumulation of the sphingolipid phytosphingosine (PHS). They propose that PHS triggers vacuole division through MCSs and the nuclear-vacuolar junction (NVJ). The study presents some solid data and proposes potential mechanisms underlying vacuolar fragmentation driven by this pathway. Although the manuscript is clear in what the data indicates and what is more hypothetical, the story would benefit from providing more conclusive evidence to support these hypothesis. Overall, the study provides valuable insights into the connection between MCSs, lipid metabolism, and vacuole dynamics.

We thank the positive review from the Reviewer #1. We hope that our hypotheses are supported by the "Author Response to Recommendations" and by further research in the future.

Reviewer #2 (Public Review):

This manuscript explores the mechanism underlying the accumulation of phytosphingosine (PHS) and its role in initiating vacuole fission. The study posits the involvement of membrane contact sites (MCSs) in two key stages of this process. Firstly, MCSs tethered by tricalbin between the endoplasmic reticulum (ER) and the plasma membrane (PM) or Golgi regulate the intracellular levels of PHS. Secondly, the amassed PHS triggers vacuole fission, most likely through the nuclear-vacuolar junction (NVJ). The authors propose that MCSs play a regulatory role in vacuole morphology via sphingolipid metabolism. While some results in the manuscript are intriguing, certain broad conclusions occasionally surpass the available data. Despite the authors' efforts to enhance the manuscript, certain aspects remain unclear. It is still uncertain whether subtle changes in PHS levels could induce such effects on vacuolar fission. Additionally, it is regrettable that the lipid measurements are not comparable with previous studies by the authors. Future advancements in methods for determining intracellular lipid transport and levels are anticipated to shed light on the remaining uncertainties in this study.

We thank the careful comment from Reviewer #2. As Reviewer #2 pointed out, the mechanism of how slight changes in PHS levels can induce the vacuolar fission event is still uncovered in this manuscript. We sincerely consider that this issue has to be resolved in further study.

Reviewer #3 (Public Review):

In this manuscript, the authors investigated the effects of deletion of the ER-plasma membrane/Golgi tethering proteins tricalbins (Tcb1-3) on vacuolar morphology to demonstrate the role of membrane contact sites (MCSs) in regulating vacuolar morphology in Saccharomyces cerevisiae. Their data show that tricalbin deletion causes vacuolar fragmentation possibly in parallel with TORC1 pathway. In addition, their data reveal that levels of various lipids including ceramides, long-chain base (LCB)-1P, and phytosphingosine (PHS) are increased in tricalbin-deleted cells. The authors find that exogenously added PHS can induce vacuole fragmentation and by performing analyses of genes involved in sphingolipid metabolism, they conclude that vacuolar fragmentation in tricalbin-deleted cells is due to the accumulated PHS in these cells. Importantly, exogenous PHS- or tricalbin deletion-induced vacuole fragmentation was suppressed by loss of the nucleus vacuole junction (NVJ), suggesting the possibility that PHS transported from the ER to vacuoles via the NVJ triggers vacuole fission. Of note, the authors find that hyperosmotic shock increases intracellular PHS levels, suggesting a general role of PHS in vacuole fission in response to physiological vacuolar division-inducing stimuli. This work provides valuable insights into the relationship between MCS-mediated sphingolipid metabolism and vacuole morphology. The conclusions of this paper are mostly supported by their results, but inclusion of direct evidence indicating increased transport of PHS from the ER to vacuoles via NVJ in response to vacuolar division-inducing stimuli would have strengthened this study. There is another weakness in their claim that the transmembrane domain of Tcb3 contributes to the formation of the tricalbin complex which is sufficient for tethering ER to the plasma membrane and the Golgi complex. Their claim is based only on the structural simulation, but not on by biochemical experiments such as co-immunoprecipitation and pull-down.

We appreciate the careful feedback from Reviewer #3. We have responded in the "Recommendations to Authors" section and hope it can partially support the weakness in our claim regarding the physical interaction between Tcb1, 2, and 3.

Reviewer #1 (Recommendations For The Authors):

I would suggest that the authors include some of the data (e.g., Tcb interactions) that they refer to in the response to the reviewers. I think that this could enhance the message in this manuscript. Also, maybe it's a typo and you were referring to some other image panel, but in the rebuttal letter a "Fig. S3B" is mentioned, but I could not find it.

Following the suggestions of reviewers #1 and #3, we have added the data of co-immunoprecipitation which confirmed that Tcb3 binds to both Tcb1 and Tcb2 as Supplemental Figure 2. With this change, the person (Ms. Saku Sasaki) who performed this analysis was also added as a co-author.

Also, we appreciate the careful remark and apologize for the mistake. In the previous Author's response, we mentioned the vacuole observation using SD medium, but this data was Fig 5C, not Fig S3B.

Reviewer #3 (Recommendations For The Authors):

I would recommend that the authors include the IP data mentioned in their rebuttal letter to show the interactions among Tcb1-3. Also, the authors should quantify all lipid species in Fig 5B, as shown in Fig 3A.

Following the suggestions of reviewers #1 and #3, we have added the co-immunoprecipitation data (Fig S2). In a further study, we would like to test if the transmembrane domain of Tcb3 is sufficient for the interaction among Tcb1-3. Also, we quantified all lipid species and replaced the data in Fig 5B.

Minor points:

(1) The function of vps4 is not mentioned in the manuscript.

(2) The function of Sur2p is not mentioned in the manuscript. It should be clearly mentioned that DHS is converted to PHS by Sur2p.

(1) We have added text sections which mention that VPS4 is needed for normal ESCRT function, and its deletion is an example for inhibition of GFP-Cps1p transport into the vacuole.

(2) We have added the text in the manuscript that states Sur2p is the hydroxylase that catalysis the conversion of DHS to PHS.

Author Response

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

Overall, the magnitude of the effect size due to FNDC5 deficiency in both male and female mice is rather modest. Looking at the data from a qualitative perspective, it is clear that knockout females still lose bone during lactation and on the low calcium diet (LCD). It is difficult to assess the physiologic consequence of the modest quantitative 'protection' seen in FNDC5 mutants since the mutants still show clear and robust effects of lactation and LCD on all parameters measured. Similarly, the magnitude of the 'increased' cortical bone loss in FNDC5 mutant males is also modest and perhaps could be related to the fact that these mice are starting with slightly more cortical bone. Since the authors do not provide a convincing molecular explanation for why FNDC5 deficiency causes these somewhat subtle changes, I would like to offer a suggestion for the authors to consider (below, point #2) which might de-emphasize the focus of the manuscript on FNDC5. If the authors chose not to follow this suggestion, the manuscript could be strengthened by addressing the consequences of the modest changes observed in WT versus FNDC5 KO mice.

Response: We agree that the magnitude of the effect size due to FNDC5 deficiency is modest with regards to the quantitative cortical bone parameters. However, if one examines the changes in osteocyte lacunar size and the mechanical properties of these bones, the differences are greater. As shown in Figure 3 E, the lacunar area of the WT females on a low calcium diet increases by over 30% and the KO by less than 20%, while in the males it is approximately 38% in WT compared to 46% in KO mice. According to Sims and Buenzli (PMID: 25708054) a potential total loss of ~16,000 mm3 (16 mL) of bone occurs through lactation in the human skeleton. This was based on our measurements in lactation-induced murine osteocytic osteolysis (Qing et al PMID: 22308018). They used our 2D section of tibiae from lactating mice showing an increase in lacunar size from 38 to 46 um2. In that paper we also showed that canalicular width is increased with lactation. Therefore, this would suggest a dramatic decrease in intracortical porosity due to the osteocyte lacunocanalicular system in female KO on a low calcium diet compared to WT females and a dramatic increase in KO males compared to WT males. Also, PTH was higher in the serum of female WT compared to female KO mice on a low calcium diet, the opposite for males in order to maintain normal calcium levels (See Table 1). Based on this data, using the FNDC5 null animals, we would speculate that the product of FNDC5, irisin, is having a highly significant effect on the ultrastructure of bone in both males and females challenged with a low calcium diet.

(2) The bone RNA-seq findings reported in Figures 4-6 are quite interesting. Although Youlten et al previously reported that the osteocyte transcriptome is sex-dependent, the work here certainly advances that notion to a considerable degree and likely will be of high interest to investigators studying skeletal biology and sexual dimorphism in general. To this end, one direction for the authors to consider might be to refocus their manuscript toward sexually-dimorphic gene expression patterns in osteocytes and the different effects of LCD on male versus female mice. This would allow the authors to better emphasize these major findings, and to then use FNDC5 deficiency as an illustrative example of how sexually-dimorphic osteocytic gene expression patterns might be affected by deletion of an osteocyte-acting endocrine factor. Ideally, the authors would confirm RNA-seq data comparing male versus female mice in osteocytes using in situ hybridization or immunostaining.

Response: Thank you for this suggestion. We have compared the different effects of LCD on male versus female mice in our revised version and have added a figure containing this information.

(3) Along the lines of point #2 (above), the presentation of the RNA-seq studies in Figures 4-6 is somewhat confusing in that the volcano plot titles seem to be reversed. For example, Figure 4A is titled "WT M: WT F", but the genes in the upper right quadrant appear to be up-regulated in female cortical bone RNA samples. Should this plot instead be titled "WT F: WT M"? If so, then all other volcano plots should be re-titled as well.

Response: We have now insured that the plots are appropriately labeled.

(4) Have the authors compared male versus female transcriptomes of LCD mice?

Response: We have now compared the male vs female transcriptomes of LCD mice and added an additional figure.

(5) It would be appreciated if the authors could provide additional serum parameters (if possible) to clarify incomplete data in both lactation and low-calcium diet models: RANKL/OPG ratio, Ctx, PTHrP, and 1,25-dihydroxyvitamin D levels.

Response: It is not possible to quantitate each of these as the serum has been exhausted. We have checked the RANKL/OPG ratio in the RNA seq and qPCR data using osteocyte enriched bone chips and found no difference.

(6) Lastly, the data that overexpressing irisin improved bone properties in Fig 2G was somewhat confusing. Based on Kim et al.'s (2018) work, irisin injection increased sclerostin gene expression and serum levels, thus reducing bone formation. Were sclerostin levels affected by irisin overexpression in this study? Was irisin's role in modulating sclerostin levels attenuated with additional calcium deficiency?

Response: We have not observed any differences in the osteocyte Sost mRNA expression between WT and KO normal and low-calcium-diet male and female mice in our RNAseq and qPCR data. As such, we did not check the Sost levels for the 2G experiment.

Reviewer #2 (Public Review):

Summary:

The goal of this study was to examine the role of FNDC5 in the response of the murine skeleton to either lactation or a calcium-deficient diet. The authors find that female FNDC5 KO mice are somewhat protected from bone loss and osteocyte lacunar enlargement caused by either lactation or a calcium-deficient diet. In contrast, male FNDC5 KO mice lose more bone and have a greater enlargement of osteocyte lacunae than their wild-type controls. Based on these results, the authors conclude that in males irisin protects bone from calcium deficiency but that in females it promotes calcium removal from bone for lactation.

While some of the conclusions of this study are supported by the results, it is not clear that the modest effects of FNDC5 deletion have an impact on calcium homeostasis or milk production.

Specific comments:

(1) The authors sometimes refer to FNDC5 and other times to irisin when describing causes for a particular outcome. Because irisin was not measured in any of the experiments, the authors should not conclude that lack of irisin is responsible. Along these lines, is there any evidence that either lactation or a calcium-deficient diet increases the production of irisin in mice?

therefore we have extrapolated that the observed effects are due to a lack of circulating irisin. However, this does not rule out that Fndc5 itself could have a function, but this would have to be most likely in muscle and not in the osteocyte as we do not detect significant levels of irisin in either primary osteoblasts nor primary osteocytes compared to muscle and C2C12 cells. As such, we concluded that the phenotypical differences we saw in our experiments are due to a lack of irisin. We now address the reviewer’s point in the discussion. The measurement of irisin in the circulation with lactation or with low calcium diet of normal mice has not been performed.

(2) The results of the irisin-rescue experiment shown in figure 2G cannot be appropriately interpreted without normal diet controls. In addition, some evidence that the AAV8-irisin virus actually increased irisin levels in the mice would strengthen the conclusion.

Response: We do not have the normal diet controls at this time. We have quantitate tagged irisin in other AAV experiments and found highly significant expression

(3) There is insufficient evidence to support the idea that the effect of FNDC5 on bone resorption and osteocytic osteolysis is important for the transfer of calcium from bone to milk. Previous studies by others have shown that bone resorption is not required to maintain milk or serum calcium when dietary calcium is sufficient but is critical if dietary calcium is low (Endo. 156:2762-73, 2015). To support the conclusions of the current study, it would be necessary to determine whether FNDC5 is required to maintain calcium levels when lactating mice lack sufficient dietary calcium.

Response: We agree that it would be important to measure calcium levels in the milk to test the hypothesis that FNDC5 is important to maintain calcium levels in milk. However, as the calcium levels are normal in the serum, we are assuming they are normal in milk. This would require future experiments.

(4) The amount of cortical bone loss due to lactation is very similar in both WT and FNDC5 KO mice. The results of the statistical analysis of the data presented in figure 1B are surprising given the very similar effect size of lactation. The key result from the 2-way ANOVA is whether there is an effect of genotype on the effect size of lactation (genotype-lactation interaction). The interaction terms were not provided. Similar concerns are noted for the results shown in figure 1G and H.

Response: We agree, thanks. We will now add the interaction terms in the figure legends.

(5) It is not clear what justifies the term 'primed' or 'activated' for resorption. Is there evidence that a certain level of TRAP expression lowers the threshold for osteocytic osteolysis in response to a stimulus?

Response: The number of TRAP positive osteocytes in female KO mice are lower than in female WT. The number of TRAP positive osteocytes are lower in WT males compared to WT females. We propose that irisin plays a role in the number of TRAP positive osteocytes in normal, WT females by readying or preparing these cells to rapidly respond to low calcium. We will use the term ‘primed’ and will not use the term ‘activated’. We are open to any terminology or description as to why this is observed and what irisin could be doing to the osteocyte.

Reviewer #3 (Public Review):

Summary:

Irisin has previously been demonstrated to be a muscle-secreted factor that affects skeletal homeostasis. Through the use of different experimental approaches, such as genetic knockout models, recombinant Irisin treatment, or different cell lines, the role of Irisin on skeletal homeostasis has been revealed to be more complex than previously thought and this warrants further examination of its role. Therefore, the current study sought to rigorously examine the effects of global Irisin knockout (KO) in male and female mouse bone. Authors demonstrated that in calcium-demanding settings, such as lactation or low-calcium diet, female Irisin KO mice lose less bone compared to wild-type (WT) female mice. Interestingly male Irisin KO mice exhibited worse skeletal deterioration compared to WT male mice when fed a low-calcium diet. When examined for transcriptomic profiles of osteocyte-enriched cortical bone, authors found that Irisin KO altered the expression of osteocytic osteolysis genes as well as steroid and fatty acid metabolism genes in males but not in females. These data support the authors' conclusion that Irisin regulates skeletal homeostasis in sex-dependent manner.

Strengths:

The major strength of the study is the rigorous examination of the effects of Irisin deletion in the settings of skeletal maturity and increased calcium demands in female and male mice. Since many of the common musculoskeletal disorders are dependent on sex, examining both sexes in the preclinical setting is crucial. Had the investigators only examined females or males in this study, the conclusions from each sex would have contradicted each other regarding the role of Irisin on bone. Also, the approaches are thorough and comprehensive that assess the functional (mechanical testing), morphological (microCT, BSEM, and histology), and cellular (RNA-seq) properties of bone.

Weaknesses: One of the weaknesses of this study is a lack of detailed mechanistic analysis of why Irisin has a sex-dependent role on skeletal homeostasis. This absence is particularly notable in the osteocyte transcriptomic results where such data could have been used to further probe potential candidate pathways between LC females vs. LC males.

Response: Our future studies will focus on understanding the molecular mechanism behind the sex-dependent effects of irisin. Our RNA seq data shows a significant difference in the lipid, steroid, and fat metabolism pathways between male and female mice, as well as between WT and KO mice. Future studies will focus on these pathways.

Another weakness is authors did not present data that convincingly demonstrate that Irisin secretion is altered in the skeletal muscle between female vs. male WT mice in response to calcium restriction. The supplement skeletal muscle data only present functional and electrophysiolgical outcomes. Since Itgav or Itgb5 were not different in any of the experimental groups, it is assumed that the changes in the level of Irisin is responsible for the phenotypes observed in WT mice. Assessing Irisin expression will further strengthen the conclusion based on observing skeletal changes that occur in Irisin KO male and female mice.

Response: The problem is that the commercial assays for irisin are not dependable, and results can differ widely across and beyond the physiologic range of 1-10 ng/ml. In part this is due to the nature of the polyclonal antibodies used and the resultant cross reactivity with other proteins. It was shown in Islam et al, 2021 (Nature Metabolism) that the commercial ELISAs were completely unreliable in mice and the only reliable method of measuring circulating irisin is mass spectrometry.

Reviewer #1 (Recommendations For The Authors):

Minor comments:

(1) Were there any low calcium diet food intake or body weight alterations between littermates and FDNC5 KO mice?

Response: Yes, and we can now include the body weight data and the food intake data in the supplement. We do not observe any significant difference between the groups.

(2) In Fig 1, ideally the authors would provide the osteocyte lacunar density along with the lacunar area.

Response: We do not observe any difference in osteocyte density in any of the groups. There is not sufficient time within 2 weeks to see a change in osteocyte density because there is no new bone formation.

(3) What is the author's comment on the involvement of irisin on TGF-B signaling since the authors observed peri lacunar remodeling in FDNC5 KO mice? Authors should also include this in the discussion section regarding the Irisin-TGF-B signaling in terms of observed increased matrix-related signals.

Response: Perilacunar modeling is the removal followed by the replacement of the perilacunar and pericanilucular matrix as occurs with lactation (Qing et al 2012). Osteocytic osteolysis is the first half of that process where the matrix is removed. Alliston and colleagues generated transgenic mice with reduced expression of the TGFb Type II receptor in mice by using the Dmp1-Cre (PMID: 32282961). They clearly found a significant difference in bone parameters, the appearance of the osteocyte lacunocanalicular network, and markers of the osteocyte perilacunar remodeling between the sexes, however they did not compare the lacunar remodeling process in males as compared to females. The females were subjected to lactation and were found to be resistant to osteocytic osteolysis. To compare males and females, they would have had to challenge both sexes to a high calcium demanding condition such as low calcium diet as performed in the current study. Their study does suggest that TGF is involved in the osteocytic osteolysis that occurs with lactation. However, as the null males showed an abnormal lacunocanlicular network compared to wildtype males, this does not necessarily indicate a defect in perilacunar remodeling. It is more likely that the defect occurred during bone formation when osteoblasts were differentiating into osteocytes. Therefore, we will reference this paper regarding the role of TGF in osteocytic osteolysis in females with lactation but not in the comparison of males to females. We have examined the normalized expression of TGF1, 2, and 3 in the present study and found no significant differences in TGF1 or 2 in any of the groups, but did find significantly higher expression of TGF3 in females compared to males for WT (fdr < 0.05), LCD WT (fdr < 0.05), and Control KO (p value < 0.01). Perhaps this isoform is playing a major role in osteocytic osteolysis that occurs with lactation.

(4) Did the authors compare the transcriptomic dataset between lactated female WT vs. KO groups? Or were the RNA-seq studies only performed on LCD study samples?

Response: We have examined RNA sequence on the LCD study samples, and not in the lactating females.

Reviewer #2 (Recommendations For The Authors):

Line 401 on page 14 states that the sexes respond differently to calcium deficiency. Lacunar area increases in both sexes, so the response is very similar. What appears to be different between the sexes is the role of FNDC5 in this process.

Response: Female WT mice have higher osteocyte lacunar area at baseline with normal diet compared to WT males. With the low calcium diet, lacunar area increases in both sexes, with female WTs having a greater increase. We agree that what appears to be different between the sexes is the role of FNDC5 when challenged with high calcium demand.

Reviewer #3 (Recommendations For The Authors):

• The authors state in the abstract and discussion that 'We propose Irisin ensures the survival of offspring by targeting the osteocytes...'. However, this appears to be over interpretation of their findings as they have not assessed the number of offspring surviving to weaning or their growth rate between WT and KO breeders.

Response: That was a proposal and we agree that it could be an over interpretation. However we would like to keep this as a speculation that could be tested in future studies.

• Figures 1 and 2 should include cortical Total Area (and maybe Marrow Cavity data from Supp as well). These data will help readers to assess whether the thinning of the cortex is driven by impaired periosteal expansion or accelerated endosteal resorption (or both). Marrow cavity area data seem to suggest increased endosteal resorption (Supp. Table 2), but unclear if periosteal expansion is altered.

Response: The data are included in the supplementary tables. We do not observe any difference in the periosteal area between the groups.

• To further support the author's statement that male KO mice exhibit different material properties of bone compared to WT mice, estimated elastic modulus should be calculated from the stiffness data (see https://doi.org/10.1002/jbmr.2539).

Response: We looked at the elastic modulus and it requires a stress strain curve instead of the force displacement we used in our calculations, therefore we were not able to get the estimated elastic modulus from the raw data we have.

• In Figure 3 there is no legend indicating females or males. Based on the data and results texts it is assumed that red is Female and blue is Male. However, please confirm in the figure legend.

Response: This is now added in the figure legends.

• Transcriptomic data should be deposited to NCBI GEO data repository. Also, please indicate whether cutoff p-value for DEG analysis was adjusted or not.

Response: We have submitted our data to the GEO data repository: GSE242445. Significant genes were defined as genes with p-value less than 0.01 and absolute log2 fold change larger than 1. The p-value is not adjusted. This information is now added.

• The statistical analysis section indicates that a two-way repeated-measure ANOVA was used. However, the data presented in the study are from independent groups, in which case repeated-measure statistical approaches should not be used. Please clarify the statistical tests that were used.

Response: We now use regular ANOVA instead of repeated-measure ANOVA. Repeated-measure ANOVA is used for paired tests. The data remain significant.

In summary, we thank the reviewers for their very useful and thoughtful suggestions for improving our manuscript.

Author Response

Reviewer #1 (Public Review):

Response to reviewer 1 comments on “weaknesses”:

“A weakness in the approach is the use of genetic models that do not offer complete deletion of the prolactin receptor from targeted neuronal populations...”

We acknowledge that neither model used provided a complete deletion of the prolactin receptor (Prlr) from the targeted neuronal populations. We suspect that incomplete deletion of targeted genes is not uncommon in these sort of studies, but this remains the best approach to addressing our question, and we believe we have been thorough and transparent in reporting the degree of deletion observed. We thought we had appropriately discussed the implications of the low proportion of Kiss1 cells still expressing Prlr, but will certainly revisit to ensure it is discussed thoroughly. This does not detract, however, from the key conclusion that prolactin action is necessary for full suppression of fertility in lactation in the mouse.

“Results showing no impact of progesterone on LH secretion during lactation are surprising, given the effectiveness of progesterone-containing birth control in lactating women...”

We think that this comment misrepresents what has been done in our study. We did not report a lack of impact of progesterone, as exogenous progesterone was never administered to mice. We did, however, give mifepristone as a progesterone receptor antagonist to determine whether endogenous progesterone contributed to the suppression of kisspeptin neuronal activity. We found that mifepristone, at levels sufficient to terminate pregnancy, had no effect on pulsatile LH secretion in lactating mice. This is consistent with our prior observation that progesterone levels are low in mouse lactation, suggesting that progesterone does not contribute significantly to the suppression of kisspeptin neuronal activity during lactation in the mouse. We agree with the reviewer that if we had given exogenous progesterone, it likely would result in suppression of pulsatile LH secretion (as it does in women). Indeed, in other work, we have found that progesterone administration profoundly suppresses activity of the kisspeptin neurons in mice (https://doi.org/10.1210/en.2019-00193). But this was not the point of the present experiment. We will review how we have described this experiment to ensure that this is absolutely clear.

“While the authors assert their findings may reflect an important role for prolactin in lactational infertility in other mammalian species, that remains to be seen….”

We acknowledge that our study cannot address whether prolactin is necessary for the suppression of lactation in other mammalian species. We hope our data may stimulate a re-examination of this question in other species, however, as some of the prior methodology (such as using pharmacological suppression of prolactin) may have had off target effects that confound interpretation. We thought that this point was discussed appropriately in the manuscript but we will certainly check and make sure this is addressed suitably.

Author Response

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

eLife assessment

This important study used Voltage Sensitive Dye Imaging (VSDI) to measure neural activity in the primary visual cortex of monkeys trained to detect an oriented grating target that was presented either alone or against an oriented mask. The authors show convincingly that the initial effect of the mask ran counter to the behavioral effects of the mask, a pattern that reversed in the latter phase of the response. They interpret these results in terms of influences from the receptive field center, and although an alternative view that emphasizes the role of the receptive field surround also seems reasonable, this study stands as an interesting and important contribution to our understanding of mechanisms of visual perception.

Public Reviews:

Reviewer #1 (Public Review):

This is a clear account of some interesting work. The experiments and analyses seem well done and the data are useful. It is nice to see that VSDI results square well with those from prior extracellular recordings.

The authors have done a good job responding to the main points of my previous review. One important question remains, as stated in that review:

"My reading is that this is primarily a study of surround suppression with results that follow pretty directly from what we already know from that literature, and although they engage with some of the literature they do not directly mention surround suppression in the text. Their major effect - what they repeatedly describe as a "paradoxical" result in which the responses initially show a stronger response to matched targets and backgrounds and then reverse - seems to pretty clearly match the expected outcome of a stimulus that initially evokes additional excitation due to increased center contrast followed by slightly delayed surround suppression tuned to the same peak orientation. Their dynamics result seems entirely consistent with previous work, e.g. Henry at al 2020, particularly their Fig. 3 https://elifesciences.org/articles/54264, so it seems like a major oversight to not engage with that work at all, and to explain what exactly is new here."

Their rebuttal of my first review is not convincing -- I still believe that surround influences are important and perhaps predominant in determining the outcome of the experiments. This is particularly clear for the "paradoxical" dynamics that they observe, which seem exactly to reflect the behavior of the surround.

The authors' arguments to the contrary are based on three main points. First, their stimuli cover the center and surround, unlike those of many previous experiments, so they argue that this somehow diminishes the impact of the surround. But the argument is not accompanied by data showing the effects of center stimuli alone or surround stimuli alone. Second, their model -- a normalization model -- does not need surround influences to account for the masking effect. Third, they cite human psychophysical masking results from their collaborators (Sebastian et al 2017), but do not cite an equally convincing demonstration that surround contrast creates potent orientation selective masking when presented alone (Petrov et al 2005, https://doi.org/10.1523/JNEUROSCI.2871-05.2005).

At the end of the day, these issues will be resolved by further experiments, not argumentation. The paper stands as an excellent contribution, but it might be wise for the authors to be less doctrinaire in their interpretations.

We thank the reviewer for their positive comments and constructive criticism. In general, we agree with the reviewer’s comments. Importantly, we do not claim that there is no effect from the surround. What we say in the discussion is:

“Because our targets are added to the background rather than occluding it, it is likely that a significant portion of the behavioral and neural masking effects that we observe come from target-mask interactions at the target location rather than from the effect of the mask in the surround.”

We still stand by this assessment. We also make the point that, at least within the framework of our delayed normalization model, there is no need for the normalization mechanism to extend beyond the center mechanism to account for our results, and even if the normalization mechanism is somewhat larger than the center, the overlap region at the center would still have a large contribution to the modulations. Overall, we agree that these issues will be need to be resolved by future experiments.

For the reasons discussed in our previous reply, we disagree with the reviewers’ statement “…this is primarily a study of surround suppression with results that follow pretty directly from what we already know from that literature”. For similar reasons we disagree with the statement “It is nice to see that VSDI results square well with those from prior extracellular recordings”.

Reviewer #2 (Public Review):

Summary

In this experiment, Voltage Sensitive Dye Imaging (VSDI) was used to measure neural activity in macaque primary visual cortex in monkeys trained to detect an oriented grating target that was presented either alone or against an oriented mask. Monkeys' ability to detect the target (indicated by a saccade to its location) was impaired by the mask, with the greatest impairment observed when the mask was matched in orientation to the target, as is also the case in human observers. VSDI signals were examined to test the hypothesis that the target-evoked response would be maximally suppressed by the mask when it matched the orientation of the target. In each recording session, fixation trials were used to map out the spatial response profile and orientation domains that would then be used to decode the responses on detection trials. VSDI signals were analyzed at two different scales: a coarse scale of the retinotopic response to the target and a finer scale of orientation domains within the stimulus-evoked response. Responses were recorded in three conditions: target alone, mask alone, and target presented with mask. Analyses were focused on the target evoked response in the presence of the mask, defined to be the difference in response evoked by the mask with target (target present) versus the mask alone (target absent). These were computed across five 50 msec bins (total, 250 msec, which was the duration of the mask (target present trials, 50% of trials) / mask + target (target present trials, 50% of trials). Analyses revealed that in an initial (transient) phase the target evoked response increased with similarity between target and mask orientation. As the authors note, this is surprising given that this was the condition where the mask maximally impaired detection of the target in behavior. Target evoked responses in a later ('sustained') phase fell off with orientation similarity, consistent with the behavioral effect. When analyzed at the coarser scale the target evoked response, integrated over the full 250 msec period showed a very modest dependence on mask orientation. The same pattern held when the data were analyzed on the finer orientation domain scale, with the effect of the mask in the transient phase running counter to the perceptual effect of the mask and the sustained response correlating the perceptual effect. The effect of the mask was more pronounced when analyzed at the scale.

Strengths

The work is on the whole very strong. The experiments are thoughtfully designed, the data collection methods are good, and the results are interesting. The separate analyses of data at a coarse scale that aggregates across orientation domains and a more local scale of orientation domains is a strength and it is reassuring that the effects at the more localized scale are more clearly related to behavior, as one would hope and expect. The results are strengthened by modeling work shown in Figure 8, which provides a sensible account of the population dynamics. The analyses of the relationship between VSDI data and behavior are well thought out and the apparent paradox of the anti-correlation between VSDI and behavior in the initial period of response, followed by a positive correlation in the sustained response period is intriguing.

We thank the reviewer for their positive comments.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

None, except perhaps for a more balanced representation of the "surround" possibility in the Discussion. The Petrov et al paper (https://doi.org/10.1523/JNEUROSCI.2871-05.2005) should be considered and cited.

As discussed above, we believe that our discussion of possible contribution from the surround is balanced. While the paper by Petrov et al is interesting, the stimuli used to study the surround effects are quite different (e.g., gap between center and surround, and the sharp edge of the surround inner boundary) so direct comparison with our results is not possible.

Reviewer #2 (Recommendations For The Authors):

The authors have addressed the questions/suggestions I raised in my review.

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

We thank the reviewers for their helpful comments and suggestions.

eLife assessment

This is an important contribution that extends earlier single-unit work on orientation-specific center-surround interactions to the domain of population responses measured with Voltage Sensitive Dye (VSD) imaging and the first to relate these interactions to orientation-specific perceptual effects of masking. The authors provide convincing evidence of a pattern of results in which the initial effect of the mask seems to run counter to the behavioral effects of the mask, a pattern that reversed in the latter phase of the response. It seems likely that the physiological effects of masking reported here can be attributed to previously described signals from the receptive field surround.

We thank the reviewers for bringing up the relation of our results to findings from previous orientation-specific center-surround interactions studies. In our final manuscript, we added a paragraph discussing this important issue. Briefly, for multiple reasons, we believe that the orientation-dependent behavioral and neural masking effects that we observe are unlikely to depend on previously described center-surround interactions in V1. First, in human subjects, perceptual similarity masking effects are almost entirely accounted for by target-mask interactions at the target location and are recapitulated when the mask has the same size and location as the target (Sebastian et al 2017). Second, in our computational model, the effect of mask orientation on the dynamics of the response are qualitatively the same if the mask is restricted to the size and location of the target while mask contrast is increased (Fig. 8 – figure supplement 3). Third, in our model, the results are qualitatively the same when the spatial pooling region for the normalization signal is the same as that for the excitation signal (Fig. 8 – figure supplement figure 1). These considerations suggest that center-surround interactions may not be necessary for neural and behavioral similarity masking effects with additive targets.

We would also like to point out some key differences between the stimuli that we use and the ones used in most previous center-surround studies. First, in our experiments, the target and the mask were additive, while in most previous center-surround studies the target occludes the background. Such studies therefore restrict the mask effect to the surround, while in our study we allow target-mask interactions at the center. Second, most center-surround studies have a sharp-edged target/surround, while in our experiments no sharp edges were present. Unpublished results from our lab suggest that such sharp edges have a large impact on V1 population responses. A third key difference is that our stimuli were flashed for a short interval of 250 ms corresponding to a typical duration of a fixation in natural vision, while most previous center-surround studies used either longer-duration drifting stimuli or very short-duration random-order stimuli for reverse-correlation analysis.

In addition, we would like to emphasize that our results go beyond previous studies in two important ways. First, we study the effect of similarity masking in behaving animals and quantitatively compare the effect of similarity masking on behavior and physiology in the same subjects and at the same time. Second, VSD imaging allows us to capture the dynamics of superficial V1 population responses over the entire population of millions of neurons activated by the target at two important spatial scales. Such results therefore complement electrophysiological studies that examine the activity of a very small subset of the active neurons.

Public Reviews:

Reviewer #1 (Public Review):

This is a clear account of some interesting work. The experiments and analyses seem well done and the data are useful. It is nice to see that VSDI results square well with those from prior extracellular recordings. But the work may be less original than the authors propose, and their overall framing strikes me as odd. Some additional clarifications could make the contribution more clear.

Please see our reply above regarding the agreement with previous studies and framing.

My reading is that this is primarily a study of surround suppression with results that follow pretty directly from what we already know from that literature, and although they engage with some of the literature they do not directly mention surround suppression in the text. Their major effect - what they repeatedly describe as a "paradoxical" result in which the responses initially show a stronger response to matched targets and backgrounds and then reverse - seems to pretty clearly match the expected outcome of a stimulus that initially evokes additional excitation due to increased center contrast followed by slightly delayed surround suppression tuned to the same peak orientation. Their dynamics result seems entirely consistent with previous work, e.g. Henry et al 2020, particularly their Fig. 3 https://elifesciences.org/articles/54264, so it seems like a major oversight to not engage with that work at all, and to explain what exactly is new here.

We thank the reviewer for the pointing out this previous work which we now cite in the final version of the manuscript. For the reasons discussed above, while this study is interesting and related to our work, we believe that our results are quite distinct.

• In the discussion (lines 315-316), they state "in order to account for the reduced neural sensitivity with target-background similarity in the second phase of the response, the divisive normalization signal has to be orientation selective." I wonder whether they observed this in their modeling. That is, how robust were the normalization model results to the values of sigma_e and sigma_n? It would be useful to know how critical their various model parameters were for replicating the experimental effects, rather than just showing that a good account is possible.

Thank you for this suggestion. In the final manuscript we include a supplementary figure that shows how the model’s predictions are affected by the orientation tuning and spatial extent of the normalization signal, and by the size and contrast of the mask (Fig. 8 – figure supplement 1-4).

• The majority of their target/background contrast conditions were collected only in one animal. This is a minor limitation for work of this kind, but it might be an issue for some.

We agree that this is a limitation of the current study. These are challenging experiments and we were unable to collect all target/background contrast combinations from both monkeys. However, in the common conditions, the results appear similar in the two animals, and the key results seem to be robust to the contrast combination in the animal in which a wider range of contrast combinations was tested. We added these points to the discussion in the final manuscript.

• The authors point out (line 193-195) that "Because the first phase of the response is shorter than the second phase, when V1 response is integrated over both phases, the overall response is positively correlated with the behavioral masking effect." I wonder if this could be explored a bit more at the behavioral level - i.e. does the "similarity masking" they are trying to explain show sensitivity to presentation time?

We agree that testing the effect of stimulus duration on similarity masking is interesting, but unfortunately, it is beyond the scope of the current study. We would also like to point out that the duration of the presentation was selected to match the typical time of fixation during natural behaviors, so much shorter or much longer stimulus durations would be less relevant for natural vision.

• From Fig. 3 it looks like the imaging ROI may include some opercular V2. If so, it's plausible that something about the retinotopic or columnar windowing they used in analysis may remove V2 signals, but they don't comment. Maybe they could tell us how they ensured they only included V1?

We thank the reviewer for this comment. As part of our experiments, we extract a detailed retinotopic map for each chamber, so we were able to ensure that the area used for the decoding analysis lays entirely within V1. We now incorporate this information in the final manuscript (Fig. 3 – figure supplement 1).

• In the discussion (lines 278-283) they say "The positive correlation between the neural and behavioral masking effects occurred earlier and was more robust at the columnar scale than at the retinotopic scale, suggesting that behavioral performance in our task is dominated by columnar scale signals in the second phase of the response. To the best of our knowledge, this is the first demonstration of such decoupling between V1 responses at the retinotopic and columnar scales, and the first demonstration that columnar scale signals are a better predictor of behavioral performance in a detection task." I am having trouble finding where exactly they demonstrate this in the results. Is this just by comparison of Figs. 4E,K and 5E,K? I may just be missing something here, but the argument needs to be made more clearly since much of their claim to originality rests on it.

We thank the reviewer for this comment. In the final manuscript we are more explicit when we discuss this point and refer to the relevant panels in Figs. 4, 5 and their figure supplements. To substantiate this key claim, we also report the timing of the transition between the two phases in all temporal correlation panels and report the neural-behavioral correlation for the integration period.

Reviewer #2 (Public Review):

Summary

In this experiment, Voltage Sensitive Dye Imaging (VSDI) was used to measure neural activity in macaque primary visual cortex in monkeys trained to detect an oriented grating target that was presented either alone or against an oriented mask. Monkeys' ability to detect the target (indicated by a saccade to its location) was impaired by the mask, with the greatest impairment observed when the mask was matched in orientation to the target, as is also the case in human observers. VSDI signals were examined to test the hypothesis that the target-evoked response would be maximally suppressed by the mask when it matched the orientation of the target. In each recording session, fixation trials were used to map out the spatial response profile and orientation domains that would then be used to decode the responses on detection trials. VSDI signals were analyzed at two different scales: a coarse scale of the retinotopic response to the target and a finer scale of orientation domains within the stimulus-evoked response. Responses were recorded in three conditions: target alone, mask alone, and target presented with mask. Analyses were focused on the target evoked response in the presence of the mask, defined to be the difference in response evoked by the mask with target (target present) versus the mask alone (target absent). These were computed across five 50 msec bins (total, 250 msec, which was the duration of the mask (target present trials, 50% of trials) / mask + target (target present trials, 50% of trials). Analyses revealed that in an initial (transient) phase the target evoked response increased with similarity between target and mask orientation. As the authors note, this is surprising given that this was the condition where the mask maximally impaired detection of the target in behavior. Target evoked responses in a later ('sustained') phase fell off with orientation similarity, consistent with the behavioral effect. When analyzed at the coarser scale the target evoked response, integrated over the full 250 msec period showed a very modest dependence on mask orientation. The same pattern held when the data were analyzed on the finer orientation domain scale, with the effect of the mask in the transient phase running counter to the perceptual effect of the mask and the sustained response correlating the perceptual effect. The effect of the mask was more pronounced when analyzed at the scale.

Strengths

The work is on the whole very strong. The experiments are thoughtfully designed, the data collection methods are good, and the results are interesting. The separate analyses of data at a coarse scale that aggregates across orientation domains and a more local scale of orientation domains is a strength and it is reassuring that the effects at the more localized scale are more clearly related to behavior, as one would hope and expect. The results are strengthened by modeling work shown in Figure 8, which provides a sensible account of the population dynamics. The analyses of the relationship between VSDI data and behavior are well thought out and the apparent paradox of the anti-correlation between VSDI and behavior in the initial period of response, followed by a positive correlation in the sustained response period is intriguing.

Points to Consider / Possible Improvements

The biphasic nature of the relationship between neural and behavioral modulation by the mask and the surprising finding that the two are anticorrelated in the initial phase are left as a mystery. The paper would be more impactful if this mystery could be resolved.

We thank the reviewer for the positive comments. In our view, while our results are surprising, there may not be a remaining mystery that needs to be resolved. As our model shows, the biphasic nature of V1’s response can be explained by a delayed orientation-tuned gain control. Our results are consistent with the hypothesis that perception is based on columnar-scale V1 signals that are integrated over an approximately 200 ms long period that incorporates both the early and the late phase of the response, since such decoded V1 signals are positively correlated with the behavioral similarity masking effect (Fig. 5D, J; Fig. 5 – figure supplement 1). We now explain this more clearly in the discussion of our final manuscript.

The finding is based on analyses of the correlation between behavior and neural responses. This appears in the main body of the manuscript and is detailed in Figures S1 and S2, which show the correlation over time between behavior and target response for the retinotopic and columnar scale.

One possible way of thinking of this transition from anti- to positive correlation with behavior is that it might reflect the dynamics of a competitive interaction between mask and target, with the initial phase reflecting predominantly the mask response, with the target emerging, on some trials, in the latter phase. On trials when the mask response is stronger, the probability of the target emerging in the latter phase, and triggering a hit, might be lower, potentially explaining the anticorrelation in the initial phase. The sustained response may be a mixture of trials on which the target response is or is not strong enough to overcome the effect of the mask sufficiently to trigger target detection.

It would, I think, be worth examining this by testing whether target dynamics may vary, depending on whether the monkey detected the target (hit trials) or failed to detect the target (miss trials). Unless I missed it I do not think this analysis was done. Consistent with this possibility, the authors do note (lines 226-229) that "The trajectories in the target plus mask conditions are more complex. For example, when mask orientation is at +/- 45 deg to the target, the population response is initially dominated by the mask, but then in mid-flight, the population response changes direction and turns toward the direction of the target orientation." This suggests (to this reviewer, at least) that the emergence of a positive correlation between behavioral and neural effects in the latter phase of the response could reflect either a perceptual decision that the target is present or perhaps deployment of attention to the location of the target.

It may be that this transition reflected detection, in which it might be more likely on hit trials than miss trials. Given the SNR it would presumably be difficult to do this analysis on a trial-by-trial basis, but the hit and miss trials (which make each make up about 1/2 of all trials) could be averaged separately to see if the mid-flight transition is more prominent on hit trials. If this is so for the +/- 45 degree case it would be good to see the same analysis for other combinations of target and mask. It would also be interesting to separate correct reject trials from false alarms, to determine whether the mid-flight transition tends to occur on false alarm trials.

If these analyses do not reveal the predicted pattern, they might still merit a supplemental figure, for the sake of completeness.

We thank the reviewer for suggesting this interesting possibility. The original analysis in the manuscript was based on both correct and incorrect trials, raising the possibility that our results reflect some contribution from decision- and/or attention-related signals rather than from low-level nonlinear encoding mechanisms in V1 that we postulate in our model (Fig. 8). To explore this possibility, we re-examined our results while excluding error trials. We found that our key results from Figs 4 and 5 – namely that there is an early transient phase in which the neural and behavioral similarity effects are anti-correlated, and a later sustained phase in which they are positively correlated – hold even for the subset of correct trials, reducing the possibility that decision/attention-related signals play a major role in explaning our results. We now include the results of this analysis as a supplementary figure in the final manuscript (Fig. 4 – figure supplement 2). While there may be some interesting differences in the response dynamics between correct and incorrect trials, the current study was not designed to address this question and the large number of conditions and small number of repeats that it necessitated make this data set suboptimal for examining these phenomena.

References

Sebastian S, Abrams J, Geisler WS. 2017. Constrained sampling experiments reveal principles of detection in natural scenes. Proc Natl Acad Sci U S A 114: E5731-e40

Author Response

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

We would like to express our sincere appreciation for the invaluable comments provided by the reviewers and their constructive suggestions to enhance the quality of our manuscript. In response to their feedback, we have diligently revised and resubmitted our paper as an article, introducing five primary figures, seven supplementary figures, and two supplementary data files. Importantly, this work represents a noteworthy contribution to the field, presenting novel findings for the first time without any prior publication.

Within the enclosed document, we have provided a comprehensive response to the reviewer comments, addressing each point in a meticulous and specific manner. We extend our sincere gratitude to the reviewers for their diligent examination of our manuscript and for offering insightful recommendations.

In our latest revision, we have taken great care to respond to every reviewer's comment, ensuring that we clarify the manuscript and provide robust evidence where required. The primary focus of these revisions was to provide additional context regarding the cooperative role between PR-Set-7 and PARP-1 in the repression of metabolic genes, accompanied by a thorough description of the current state of the field. Substantial modifications and new analyses, presented in the supplemental figures, have been included to comprehensively address this concern.

Another concern raised was regarding the interaction between PARP-1 and mono-methylated active histone marks, which was not adequately described in the previous version of our manuscript. In this revised version, we have updated our Fig. 1 and Supplemental Fig. S1 and introduced Supplemental Fig. S2 to properly demonstrate that PARP-1 binds to all mono-methylated active histone marks tested. Furthermore, we extensively revised the Discussion section of our manuscript to discuss the implications of this discovery and how it fits into the broader context of PARP-1 research.

Addressing another reviewer's concern about the potential indirect regulation of transcription by PARP1 and PR-SET7, we revised the discussion section and incorporated findings from our recent study. These findings clearly demonstrate PARP1's binding to the loci of misregulated genes, suggesting a direct involvement in their regulation.

Furthermore, we have improved the description of the reagents and Drosophila lines used in this study to provide a more comprehensive understanding for readers. Finally, we conducted a comprehensive revision of the entire manuscript to rectify the identified typos and grammatical errors.

Enclosed, you will find a detailed, point-by-point response to each of the reviewer's comments, showcasing our commitment to addressing their concerns with precision.

We firmly believe that our revisions successfully resolve all the concerns raised by the reviewers, and we are confident that this improved version of our manuscript contributes significantly to the scientific discourse.

Reviewer #1:

The study investigates the role of PARP-1 in transcriptional regulation. Biochemical and ChIP-seq analyses demonstrate specific binding of PARP-1 to active histone marks, particularly H4K20me, in polytene chromosomes of Drosophila third instar larvae. Under heat stress conditions, PARP-1's dynamic repositioning from the Hsp70 promoter to its gene body is observed, facilitating gene activation. PARP-1, in conjunction with PR-Set7, plays a crucial role in the activation of Hsp70 and a subset of heat shock genes, coinciding with an increase in H4K20me1 levels at these gene loci. This study proposes that H4K20me1 is a key facilitator of PARP-1 binding and gene regulation. However, there are several critical concerns that are yet to be addressed. The experimental validation and demonstration of results in the main manuscript are scant. Recent developments in the area are omitted, as an important publication hasn't been discussed anywhere in the work (PMID: 36434141). The proposed mechanism operates quite selectively, and any extrapolations require intensive scientific evidence.

Major Comments:

(1) PARP1 hypomorphic mutant validation data must be provided at RNA levels as the authors have mentioned about its global reduction in RNA levels.

We sincerely appreciate Reviewer 1 for their meticulous review of our manuscript and for providing valuable insights. In response to the raised concern, we would like to highlight that the validation data for the PARP1 hypomorphic mutant at the RNA level has been previously documented in our study (PMID: 20371698), where we found that PARP1 RNA level was deeply impacted in parp1C03256. To enhance clarity, we have made corresponding modifications to the Materials and Methods section to explicitly articulate this aspect: parp-1C03256 significantly lowers the level of PARP-1 RNA and protein level (14) but also significantly diminishes the level of pADPr (11).

We hope these revisions effectively address the reviewer's suggestion and contribute to a more comprehensive understanding of our findings.

(2) The authors should provide immunoblot data for global Poly (ADP) ribosylation levels in PARP1 hypomorphic mutant condition as compared to the control. They must also provide the complete details of the mouse anti-pADPr antibody used in their immunoblot in Figure 5B.

We extend our gratitude to Reviewer 1 for drawing attention to aspects requiring further clarification. In response to the inquiry about global Poly (ADP) ribosylation levels in the PARP1 hypomorphic mutant condition, we want to emphasize that our study extensively reported on the diminished levels of pADPr in comparison to the wildtype, as documented in our previous work (PMID: 21444826). To address this, we have incorporated pertinent details in the Materials and Methods section, providing a comprehensive account of our findings. parp-1C03256 significantly lowers the level of PARP-1 RNA and protein level (14) but also significantly diminishes the level of pADPr (11).

Furthermore, in addressing the request for complete details of the mouse anti-pADPr antibody (10H) used in Figure 5B, we have taken steps to enhance transparency. The Materials and Methods section has been revised to incorporate more comprehensive information about the antibody, ensuring a clearer understanding of our experimental procedures. anti-pADPr (Mouse monoclonal, 1:500, 10H - sc-56198, Santa Cruz).

We appreciate the reviewer's diligence in ensuring the robustness of our methodology, and we believe these modifications strengthen the overall quality and transparency of our study.

(3) PR-Set7 mutant validation results should be provided in the main manuscript, as done by the authors using qRT-PCR. Also, immunoblot data for the PR-set7 null condition should be supplemented in the main manuscript as the authors have already mentioned their anti-PR-Set7 (Rabbit, 1:1000, Novus Biologicals, 44710002) antibody in the materials and methods section.

We appreciate Reviewer 1's thorough examination of our manuscript and their constructive feedback. The pr-set7 null mutant has been rigorously characterized in a study conducted by Dr. Ruth Steward's laboratory (PMID: 15681608). Additionally, we employed our PR-SET7 antibody to validate the mutant, and the corresponding data can be found in Supplemental Figure 3. To enhance clarity, we have made necessary modifications to both the results and Materials and Methods sections, providing explicit details on the validation process. Result section: To validate our hypothesis, we initially confirmed that the pr-set720 mutant not only eliminated PR-SET7 RNA and protein but also abrogated H4K20me1 modification (Supplemental Fig.S3).

Material and methods section: The pr-set720 null mutant was validated in (15) and we confirmed that this mutant abolishes PR-SET7 RNA and protein level but also leads to the absence of H4K20me1 (Supplemental Fig. S3).

We believe these revisions address the reviewer's concerns and contribute to a more comprehensive presentation of our study.

(4) The authors have probably missed out on a very important recent report (PMID: 36434141), suggesting the antagonistic nature of the PARP1 and PR-SET7 association. In light of these important observations, the authors must check for the levels of PR-SET7 in PARP1 hypomorphic conditions.

We appreciate the insightful comment from Reviewer 1, drawing our attention to the recent study by Estève et al. (PMID: 36434141) highlighting the potential antagonistic relationship between PARP1 and PR-SET7. To address this important point, we have carefully examined the levels of PR-SET7 in PARP1 hypomorphic conditions.

In response to this concern, we have added two new supplemental figures, Supplemental Fig. S4 and S5, which specifically address the impact of PARP1 deficiency on PR-Set7 expression. These figures clearly demonstrate that there were no significant changes observed in PR-SET7 RNA (Fig. S4) or protein levels (Fig. S5) in the absence of Parp1. This finding supports the conclusion that Parp1 is not directly involved in the regulation of PR-SET7 in Drosophila.

Furthermore, we have updated the Results section to explicitly mention this observation:

Interestingly, in the absence of PARP-1, neither PR-SET7 RNA nor protein levels were affected (Supplemental Fig. S4-5), indicating that PARP-1 is not directly implicated in the regulation of PR-SET7.

Additionally, we have included information about the anti-H3 antibody used in Supplemental Fig. S4 in the Materials and Methods section: anti-H3 (Rabbit polyclonal, 1/1000, FL-136 sc-10809 Santa Cruz).

We believe that these modifications effectively address the raised concern and provide a more comprehensive understanding of the relationship between PARP1 and PR-SET7 in our study. We hope these clarifications enhance the overall robustness and clarity of our findings.

(5) Also, the results of the aforementioned study should be adequately discussed in the present study along with its implications in the same.

We appreciate Reviewer 1's valuable suggestion to discuss the implications of the study by Estève et al. (PMID: 36434141) within the context of our own findings. Estève et al. reported a potential antagonistic relationship between PARP1 and PR-SET7, showing that a decrease in PARP1 proteins leads to an increase in PR-SET7 protein levels. In our investigation, however, we did not observe significant changes in PR-SET7 RNA and protein levels in the parp1C03256 mutant, as demonstrated in the newly added Supplemental Fig. S3 and S4.

We acknowledge the discrepancy between our results and those of Estève et al., and we propose that this difference may be due to distinct experimental approach: Estève et al.'s study focused on mammalian cell populations and in vitro experiments, whereas our investigation employed Drosophila third-instar larvae as the whole organism model. It is plausible that regulatory mechanisms governing PR-SET7 differ between mammals and Drosophila. Another possibility is that PARP-1 may cooperate with PR-SET7 in the context of Drosophila development but could exhibit antagonistic roles against PR-SET7 in specific cell lines and under certain biological or developmental conditions.

In the Discussion section, we have incorporated this information, stating: A recent study demonstrated that in human cells overexpressing PARP-1, PR-SET7/SET8 is degraded (33). This implies that the absence of PARP-1 might lead to increased levels of PR-SET7. However, in our study involving parp-1 mutant in Drosophila third-instar larvae, we observed a slightly different scenario: we detected a minor but not significant reduction in both PR-SET7 RNA and protein levels (Supplemental Fig.S4 and S5). This outcome stands in stark contrast to the previous study's findings. The discrepancy could be due to the distinct experimental approaches used: the previous research focused on mammalian cells and in vitro experiments, whereas our study examined the functions of PARP-1 in whole Drosophila third-instar larvae during development. Consequently, while PARP-1 may cooperate with PR-SET7 in the context of Drosophila development, it could exhibit antagonistic roles against PR-SET7 in specific cell lines and under certain biological or developmental conditions.

We believe these modifications provide a comprehensive discussion of the observed discrepancies and enhance the overall interpretation of our findings. We hope that these clarifications satisfactorily address the concerns raised by Reviewer 1.

(6) Gene transcriptional activation requires open chromatin and RNA polymerase II binding to the promoter. Since, differentially expressed genes in both PR-Set7 null and PARP1 hypomorph mutants, co-enriched with PARP-1 and H4K20me1 were mainly upregulated, the authors should provide RNA polymerase II occupancy data of these genes via RNA-Pol II ChIP-seq to further attest their claims.

We appreciate the insightful comment from Reviewer 1 regarding the necessity for RNA-polymerase II (PolII) occupancy data to further support our claims on gene transcriptional activation. To address this concern, we conducted an analysis of PolII occupancy around genes co-enriched with PARP-1 and H4K20me1 that are upregulated in both pr-set720 and parp-1C03256 mutants during the third instar larvae stage. The results of this analysis have been included in the newly added supplemental Fig. S5.

Our findings reveal that these upregulated genes exhibit higher PolII occupancy compared to other genes, both at their promoter regions and gene bodies, suggesting heightened activity during third instar larval stage in wild type animals (Supplemental Fig. S6). To further validate these results, we cross-referenced publicly available RNA-seq data at the same developmental stage, confirming that, on average, these upregulated genes display a 40% higher expression compared to other genes (supplemental Fig. S6B).

Moreover, we would like to highlight the consistency of our current findings with our previous study (PMID: 38012002), where we reported the critical involvement of PARP-1 in tempering the expression of active metabolic genes at the end of the third instar larvae. The current data, suggesting a role for PR-SET7 in this regulatory process, adds another layer to our understanding of the nuanced control exerted by PARP-1 on the expression of active metabolic genes during this critical developmental transition.

In light of these results, we have modified the Results section to emphasize these findings: Intriguingly, under wild-type conditions, these genes displayed expression levels approximately 40% higher than the average and demonstrated increased RNA-Polymerase II occupancy both at their promoter regions and gene bodies compared to other genes (supplemental Fig.S6), indicating their high activity in wild type context.

Additionally, we have incorporated this information into the Discussion section to underscore the cooperative role of PARP-1 and PR-SET7 in repressing the expression of active metabolic genes: Notably, genes co-enriched with PARP-1 and H4K20me1, and are upregulated in both parp-1C03256 and pr-set720 mutants, are predominantly metabolic genes exhibiting high expression levels under wild-type conditions and a high occupancy of polymerase II both at their promoter region and gene body (Supplemental Fig. S6). In our previous study, we discovered that PARP-1 plays a crucial role in repressing highly active metabolic genes during the development of Drosophila by binding directly to their loci (34). Also, PARP-1 is required for maintaining optimum glucose and ATP levels at the third-instar larval stage (34). During Drosophila development, repression of metabolic genes is crucial for larval to pupal transition (35, 36). This repression is linked to the reduced energy requirements as the organism prepares for its sedentary pupal stage (35, 37). Notably, we observed that PARP-1 shows a high affinity for binding to the gene bodies of these metabolic genes (34).

Our data indicates that in both parp-1 and pr-set7 mutant animals, there was a preferential repression of metabolic genes at sites where PARP-1 and H4K20me1 are co-bound (Fig.3E), while these metabolic genes are highly active during third-instar larval stage (Supplemental Fig.S6). Thus, we propose that the presence of H4K20me1 may be essential for the binding of PARP-1 at these gene bodies, contributing to their repression. Importantly, this mechanism of gene repression has broader developmental implications. As earlier stated, mutant animals lacking functional PARP-1 and PR-SET7 undergo developmental arrest during larval to pupal transition. This arrest could be directly linked to the disruption of the normal metabolic gene repression during development. Without the repressive action of PARP-1 and PR-SET7, key metabolic processes might remain unchecked, leading to metabolic imbalances that are incompatible with the normal progression to the pupal stage.

Finaly, we have updated the Materials and Methods section to include information about the RNA-seq and PolII ChIP-seq datasets used: GSE15292 (RNA-polymerase II). In addition, we used the Developmental time-course RNA-seq dataset (54), SRP001065.

We believe that these modifications comprehensively address Reviewer 1's concern and provide a more robust foundation for our claims regarding the role of PARP-1 and PR-SET7 in the transcriptional regulation of co-enriched genes during the critical developmental transition.

(7) As discussed in Figure 4, the authors found transcriptional activation of group B genes even after a significant reduction of H3K20me1 in their gene body after heat shock. Given the dynamic equilibrium shift in epigenetic marks that regulate gene expression and their locus-specific transcriptional regulation, the authors should further look for the enrichment of other epigenetic marks and even H4K20me1 specific demethylases such as PHF8 (PMID: 20622854), and their cross-talk with PARP1 to further bridge the missing links of this tale. This will add more depth to this work.

We appreciate the thoughtful input provided by Reviewer 1 and acknowledge the importance of exploring additional epigenetic marks and potential cross-talk association with PARP1 to enhance the depth of our study. Our investigation has primarily focused on the interplay between PR-SET7/H4K20me1 and PARP-1, as evidenced by the colocalization and robust binding affinity observed between PARP-1 and H4K20me1 (Fig 1C, 2B, and 3A). This interaction is particularly noteworthy in the context of regulating specific heat shock genes, as highlighted in Figure 4A. While we recognize the potential significance of examining a broader spectrum of epigenetic marks and considering the involvement of specific demethylases, such as PHF8 (PMID: 20622854), in this regulatory network, our research strategy is intentionally tailored to leverage the unique characteristics of the PR-SET7/H4K20me1 and PARP-1 interplay in Drosophila. A key consideration is the technical advantage afforded by the fact that PR-SET7 is the exclusive methylase responsible for H4K20 in Drosophila (PMID: 15681608), allowing for specific depletion of H4K20me1 without the confounding influence of other methyltransferases.

This specificity is pivotal, especially given the similar developmental arrest patterns observed in both PR-SET7 and PARP-1 mutants. Such parallel phenotypes provide a distinct opportunity to delve deeply into the intricacies of their interaction during organismal development and in response to heat stress. Additionally, the identity of the demethylase for H4K20me1 in Drosophila remains unknown, further underscoring the rationale for our focused approach.

While we acknowledge the broader implications of exploring additional epigenetic marks, we believe that our deliberate focus on the PR-SET7/H4K20me1 and PARP-1 pathway provides a unique and valuable perspective on the regulation of gene expression in Drosophila. We hope that this clarification addresses the concerns raised by Reviewer 1 and conveys the rationale behind our chosen research strategy.

Reviewer #2:

Summary:

This study from Bamgbose et al. identifies a new and important interaction between H4K20me and Parp1 that regulates inducible genes during development and heat stress. The authors present convincing experiments that form a mostly complete manuscript that significantly contributes to our understanding of how Parp1 associates with target genes to regulate their expression.

Strengths:

The authors present 3 compelling experiments to support the interaction between Parp1 and H4K20me, including:

(1) PR-Set7 mutants remove all K4K20me and phenocopy Parp mutant developmental arrest and defective heat shock protein induction.

(2) PR-Set7 mutants have dramatically reduced Parp1 association with chromatin and reduced poly-ADP ribosylation.

(3) Parp1 directly binds H4K20me in vitro.

Weaknesses:

(1) The histone array experiment in Fig1 strongly suggests that PARP binds to all mono-methylated histone residues (including H3K27, which is not discussed). Phosphorylation of nearby residues sometimes blocks this binding (S10 and T11 modifications block binding to K9me1, and S28P blocks binding to K27me1). However, H3S3P did not block H3K4me1, which may be worth highlighting. The H3K9me2/3 "blocking effect" is not nearly as strong as some of these other modifications, yet the authors chose to focus on it. Rather than focusing on subtle effects and the possibility that PARP "reads" a "histone code," the authors should consider focusing on the simple but dramatic observation that PARP binds pretty much all mono-methylated histone residues. This result is interesting because nucleosome mono-methylation is normally found on nucleosomes with high turnover rates (Chory et al. Mol Cell 2019)- which mostly occurs at promoters and highly transcribed genes. The author's binding experiments could help to partially explain this correlation because PARP could both bind mono-methylated nucleosomes and then further promote their turnover and lower methylation state.

We appreciate the comprehensive review and valuable insights provided. In response to the comments, we have made substantial revisions to address the concerns and enhance the clarity of our findings. In Figure 1B, C, D, F, and G, we have expanded our data presentation to demonstrate PARP-1's binding affinity for H3K27me1. This addition is now incorporated into the revised results section. Additionally, we have updated Supplemental Fig.S1 and introduced new supplemental data (Supplemental Fig.S2) to illustrate the inhibition of PARP-1 binding by H3S10P, H3S28P, and H3T11P. The comprehensive exploration of PARP-1's interaction with mono-methylated histones, as suggested by the reviewer, is now more robustly documented in our revised figures and supplementary materials.

Our Discussion section has been refined to articulate more clearly how PARP-1 may be selectively recruited to active chromatin domains through its interaction with mono-methylated histone marks. We have proposed a model where PARP-1 actively participates in the turnover process, contributing to the maintenance of an active chromatin environment. This proposed mechanism involves PARP-1 selectively binding to mono-methylated active histone marks associated with highly transcribed genes. Upon activation, PARP-1 undergoes automodification, leading to its release from chromatin and facilitating the reassembly of nucleosomes carrying the mono-methylated marks. The enzymatic action of Poly(ADP)-ribose glycohydrolase (PARG) subsequently cleaves pADPr, allowing for the restoration of PARP-1's binding affinity to mono-methylated active histone marks. This proposed hypothesis is consistent with existing research across various model organisms and aligns with the known association of PARP-1 with highly expressed genes, as well as its role in mediating nucleosome dynamics and assembly.

Our Discussion section is modified a followed: Finaly, highly transcribed genes have been reported to present a high turnover of mono-methylated modifications, maintaining a state of low methylation (50). Then, our findings suggest that PARP-1 might actively participate in the turnover process to uphold an active chromatin environment. The proposed mechanism unfolds as follows: 1) PARP-1 selectively binds to mono-methylated active histone marks associated with highly transcribed genes. 2) Upon activation, PARP-1 undergoes automodification and is subsequently released from chromatin, facilitating the reassembly of nucleosomes carrying the mono-methylated marks. 3) The enzymatic action of Poly(ADP)-ribose glycohydrolase (PARG) cleaves pADPr, allowing for the restoration of PARP-1's binding affinity to mono-methylated active histone marks. This proposed hypothesis aligns cohesively with existing research conducted across various model organisms, including mice, Drosophila, and Humans (7, 23, 29, 51-53). Notably, previous studies have consistently demonstrated that PARP-1 predominantly associates with highly expressed genes and plays a crucial role in mediating nucleosome dynamics and assembly. Thus, our proposed model provides a molecular framework that may contribute to understanding the relationship between PARP-1 and the epigenetic regulation of gene expression. Further experimental validation is warranted to elucidate the precise details of this proposed mechanism and its implications in the broader context of chromatin dynamics and transcriptional control.

We hope that these revisions address the reviewer's concerns and contribute to the overall strength and clarity of our manuscript.

(2) The RNAseq analysis of Parp1/PR-Set7 mutants is reasonable, but there is a caveat to the author's conclusion (Line 251): "our results indicate H4K20me1 may be required for PARP-1 binding to preferentially repress metabolic genes and activate genes involved in neuron development at co-enriched genes." An alternative possibility is that many of the gene expression changes are indirect consequences of altered development induced by Parp1 or PR-Set7 mutants. For example, Parp1 could activate a transcription factor that represses the metabolic genes that they mention. The authors should consider discussing this possibility.

We hope that these revisions address the reviewer's concerns and contribute to the overall strength and clarity of our manuscript.

We extend our gratitude to Reviewer 2 for their thoughtful consideration of our manuscript and the insightful suggestion. In response to the raised concern regarding the conclusion on Line 251, where we proposed that "our results indicate H4K20me1 may be required for PARP-1 binding to preferentially repress metabolic genes and activate genes involved in neuron development at co-enriched genes," we acknowledge the alternative possibility suggested by the reviewer. It is plausible that many of the observed gene expression changes are indirect consequences of altered development induced in parp-1 or pr-set7 mutants. For example, PARP-1 could activates a transcription factor that represses the mentioned metabolic genes.

To address this concern, we have revisited our data and incorporated relevant findings from one of our recent studies that utilized a ChIP-seq approach. The results from this study suggest a direct binding of PARP-1 to the loci of metabolic genes, providing support for the notion that PARP-1 may indeed directly regulate their expression (PMID: 37347109). We have updated the Discussion section to reflect this information, aiming to provide a more comprehensive perspective on the potential mechanisms underlying the observed gene expression changes: In our previous study, we discovered that PARP-1 plays a crucial role in repressing highly active metabolic genes during the development of Drosophila by binding directly to their loci (34). Also, PARP-1 is required for maintaining optimum glucose and ATP levels at the third-instar larval stage (34). During Drosophila development, repression of metabolic genes is crucial for larval to pupal transition (35, 36). This repression is linked to the reduced energy requirements as the organism prepares for its sedentary pupal stage (35, 37). Notably, we observed that PARP-1 shows a high affinity for binding to the gene bodies of these metabolic genes (34).

We believe these modifications contribute to a more informed interpretation of our findings.

(3) The section on the inducibility of heat shock genes is interesting but missing an important control that might significantly alter the author's conclusions. Hsp23 and Hsp83 (group B genes) are transcribed without heat shock, which likely explains why they have H4K20me without heat shock. The authors made the reasonable hypothesis that this H4K20me would recruit Parp-1 upon heat shock (line 270). However, they observed a decrease of H4K20me upon heat shock, which led them to conclude that "H4K20me may not be necessary for Parp1 binding/activation" (line 275). However, their RNA expression data (Fig4A) argues that both Parp1 and H40K20me are important for activation. An alternative possibility is that group B genes indeed recruit Parp1 (through H4K20me) upon heat shock, but then Parp1 promotes H3/H4 dissociation from group B genes. If Parp1 depletes H4, it will also deplete H4K20me1. To address this possibility, the authors should also do a ChIP for total H4 and plot both the raw signal of H4K20me1 and total H4 as well as the ratio of these signals. The authors could also note that Group A genes may similarly recruit Parp1 and deplete H3/H4 but with different kinetics than Group B genes because their basal state lacks H4K20me/Parp1. To test this possibility, the authors could measure Parp association, H4K20methylation, and H4 depletion at more time points after heat shock at both classes of genes.

We thank Reviewer 2 for their valuable comment on our manuscript. We acknowledge your hypothesis suggesting that PARP-1 may induce H3/H4 dissociation from group B genes, potentially leading to a reduction in H4K20me1. However, our findings support a different interpretation.

Our data indicate that while H4K20me1 is present under normal conditions at group B genes, its reduction following heat shock does not appear to hinder PARP-1's role in transcriptional activation (Fig 4A, C and E). We propose that the observed decrease in H4K20me1 might reflect a regulatory shift in chromatin structure that is conducive to transcriptional activation during heat shock, facilitated by PARP-1 independently of sustained H4K20me1 levels at group B genes. Additionally, the literature suggests a dual role for H4K20me1 in gene regulation, from facilitating transcriptional elongation in certain contexts to acting as a repressor in others.

Unlike in group A genes which had low enrichment of H4K20me1 before heat shock (Fig 4B and D), the high enrichment of H4K20me1 in group B genes (Fig 4C and E) could imply a repressive role for this mark prior to heat stress. Thus, in the context of group B genes, it's conceivable that the removal of H4K20me1 might be necessary for their activation during heat stress. Thus, PR-SET7 may possess functions beyond its role as a histone methylase, which are crucial for activating group B genes under heat stress conditions. These functions could include methylation of non-histone substrates and non-catalytic activities.

Furthermore, our analysis of gene expression in pr-set720 and parp-1C03256 mutants indicates that while PARP-1 and H4K20me1 interaction may have overlapping roles in gene regulation, they also possess distinct functions in the modulation of gene expression (Fig 3E). Thus, we propose that the relationship between PR-SET7 and PARP-1 in transcriptional regulation involves a complex regulatory mechanism that extends beyond the presence of H4K20me1.

We modified the discussion section to address this point: Another plausible explanation could be that the recruitment of PARP-1 to group B genes loci promotes H4 dissociation and then leads to a reduction of H4K20me1. However, our findings suggest an alternative interpretation: the decrease in H4K20me1 at group B genes during heat shock does not seem to impede PARP-1's role in transcriptional activation, (Fig.4A, C and E). Rather than disrupting PARP-1 function, we propose that this reduction in H4K20me1 may signify a regulatory shift in chromatin structure, priming these genes for transcriptional activation during heat shock, with PARP-1 playing an independent facilitating role. Moreover, existing studies have highlighted the dual role of H4K20me1, acting as a promoter of transcription elongation in certain contexts and as a repressor in others (13, 25, 38, 39, 41-45). The elevated enrichment of H4K20me1 in group B genes under normal conditions may indicate a repressive state that requires alleviation for transcriptional activation. Additionally, we cannot discount the possibility of unique regulatory functions associated with PR-SET7, extending beyond its recognized role as a histone methylase. Non-catalytic activities and potential interactions with non-histone substrates might contribute to the nuanced control exerted by PR-SET7 on group B genes during heat stress (46, 47). Furthermore, our exploration of pr-set720 and ParpC03256 mutants reveals distinct roles for PARP-1 and H4K20me1 in modulating gene expression (Fig 3E). This reinforces the notion that the interplay between PR-SET7 and PARP-1 involves a multifaceted regulatory mechanism. Understanding the intricate relationship between these molecular players is crucial for elucidating the complexities of gene expression modulation under heat stress conditions.

We hope that this modification will adequately address Reviewer 2 concerns and enhance the clarity of our conclusions.

Reviewer #1 (Recommendations For The Authors):

(1) Please check the entire manuscript for grammatical errors and typos. PR-set7 has been wrongly written as PR-ste7 in quite a few places in the manuscript. Poly (ADP)-ribosylation has been written as poly(ADP-ribosyl)ation in the last result heading. There are more such errors. Please rectify them.

We express our sincere appreciation to Reviewer 1 for their meticulous review of our manuscript, and we acknowledge the importance of ensuring grammatical accuracy and clarity. We have taken your feedback seriously and conducted a comprehensive revision of the entire manuscript to rectify the identified typos and grammatical errors. We hope that these revisions contribute to an improved overall presentation of our research, and we appreciate the reviewer's diligence in ensuring the accuracy of the manuscript.

(2) The authors can also look up publicly available mammalian ChIP-seq data for H4K20me1 and PARP1, in order to further ossify their findings and increase the breadth of their work.

We appreciate the suggestion from Reviewer 1 and have taken steps to further validate and broaden the scope of our findings. Specifically, we compared the distribution of PARP1 and H4K20me1 in Human K562 cells. The results of this analysis revealed a correlation in their distribution, supporting the idea that the observed correlation between PARP-1 and H4K20me1 is not limited to fruit flies. We have incorporated these findings into the Results section and added a new Supplemental Fig. S6 to visually highlight this correlation: Finally, to extend the generalizability of our observations beyond Drosophila, we compared the distribution of PARP1 and H4K20me1 in Human K562 cells. Strikingly, we observed a correlation in their distribution, suggesting that the interplay between PARP-1 and H4K20me1 is not limited to fruit flies (Supplemental Fig. S6).

We believe that this modification addresses Reviewer 1's suggestion by providing additional evidence that supports the broader relevance of our findings beyond the Drosophila model system.

(3) Please discuss in greater detail how the PARP1-H4K20me1 axis orchestrates the repression program (metabolic pathways in this case) with proper references.

We appreciate Reviewer 1's continued engagement with our manuscript and have adjusted the discussion section to provide a more detailed insight into how the PARP1-H4K20me1 axis orchestrates the repression program, particularly focusing on metabolic pathways. The modified discussion section now reads: In our previous study, we discovered that PARP-1 plays a crucial role in repressing highly active metabolic genes during the development of Drosophila by binding directly to their loci (34). Also, PARP-1 is required for maintaining optimum glucose and ATP levels at the third-instar larval stage (34). During Drosophila development, repression of metabolic genes is crucial for larval to pupal transition (35, 36). This repression is linked to the reduced energy requirements as the organism prepares for its sedentary pupal stage (35, 37). Notably, we observed that PARP-1 shows a high affinity for binding to the gene bodies of these metabolic genes (34). Our data indicates that in both parp-1 and pr-set7 mutant animals, there was a preferential repression of metabolic genes at sites where PARP-1 and H4K20me1 are co-bound (Fig.3E), while these metabolic genes are highly active during third-instar larval stage (Supplemental Fig.S6). Thus, we propose that the presence of H4K20me1 may be essential for the binding of PARP-1 at these gene bodies, contributing to their repression. Importantly, this mechanism of gene repression has broader developmental implications. As earlier stated, mutant animals lacking functional PARP-1 and PR-SET7 undergo developmental arrest during larval to pupal transition. This arrest could be directly linked to the disruption of the normal metabolic gene repression during development. Without the repressive action of PARP-1 and PR-SET7, key metabolic processes might remain unchecked, leading to metabolic imbalances that are incompatible with the normal progression to the pupal stage.

We hope these modifications provide a more comprehensive discussion on how the PARP1-H4K20me1 axis influences the repression program, particularly within metabolic pathways, and how this mechanism contributes to the broader context of Drosophila development.

Author Response

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

eLife assessment

This study presents a useful inventory of immune signatures that are correlated with cancer treatment-related pneumonitis. The data were collected and analysed using solid and validated methodology and can be used as a starting point for further functional studies.

We sincerely thank the editor for their encouraging comments regarding our study. As rightly pointed out, this study indeed serves as a pivotal starting point for subsequent functional studies.

Reviewer #2 (Recommendations For The Authors):

I greatly appreciate the authors diligence in addressing all the suggested points. The paper now presents significantly stronger evidence to support the findings.

I do have one final question: Could you clarify how the correlation presented in Supplementary Figure 3 was calculated? Is it a Pearson correlation of CTCAE grade directly to marker expression? Additionally, could you explain how the significance was determined? The authors mention a significant correlation for CCR7, but the heatmap displays similarly high values for CD7 and CD57. Finally, I'm curious about the absence of CD16 in the heatmap.

Thank you for your insightful query. To clarify, the correlation shown in Supplementary Figure 3 was indeed calculated using the Pearson correlation coefficient. This involved correlating the CTCAE grade directly with the mean expression levels of each marker. The computations were conducted using GraphPad Prism version 9. Regarding the statistical significance, we defined a threshold of P < 0.05 as significant. Specifically, the P-values for CCR7, CD7, and CD57 were found to be 0.009, 0.035, and 0.039, respectively. Hence, while CCR7 showed a significant correlation, CD7 and CD57 also exhibited relatively high values, as correctly observed. We have added CD7 and CD57 along with CCR7 in the discussion section, though not to mention much for better focusing on CD16.

CD16 was initially omitted from Supplementary Figure 3 to prevent redundancy and preserve data clarity. Nonetheless, in light of your query, we have included CD16 in the correlation matrix to provide a comprehensive view of its association with other markers.

We hope this adequately addresses your question and further clarifies our findings.

Reviewer #3 (Recommendations For The Authors):

General suggestions for presentation in the future:

It is essential to concretely define the numbers presented in all figures and plots. For example, in Figure 6 (I), what does it mean by "percentage representation of FCGR3A (CD16)"? Percentage of what? How did you calculate that? It is also important to show more statistics in general, for example, in dot plots like Figure 6 (H), where are the means and p-values? Little things like that completely change the impact of the figures. For the narrative of this paper, it is OK, but in the future, fine-tuning the presentation would massively improve the impact of the work which the contents deserve.

Thank you for your insightful feedback. Addressing your concerns, I have revised Figure 6H and Figure 6I to provide a more precise and informative presentation of our data. In Figure 6H, the violin plots illustrate the expression intensity of FCGR3A (CD16) on CD4+ and CD8+ T cells. Each dot represents an individual cell within the BALF from both healthy controls (HC) and COVID-19 patients. This data was derived from the single-cell RNA-seq dataset GSE145926. To enhance clarity and statistical robustness, I have now included p-values directly in Figure 6H. Additionally, for a more comprehensive understanding, the means ± standard deviation (SD) have been incorporated into the main text of the manuscript.

Regarding Figure 6I, it depicts the proportion of FCGR3A (CD16)-positive cells within the CD4+ and CD8+ T cell populations in BALF from HC and COVID-19 patients. The threshold for FCGR3A expression was set at 0.5. Upon further review and in response to your feedback, I realized an error in the calculation of the proportion of FCGR3A-positive cells among CD4+ and CD8+ T cells. Initially, the proportion of FCGR3A-positive CD4+ T cells was calculated in relation to the entire CD4+ T cell population, without differentiation between the groups. This has now been corrected, and the adjusted figures are presented in Figure 6I.

I am grateful for the opportunity to refine these figures, as your suggestions have not only helped to correct the error but have also significantly enhanced the impact and clarity of our work. Your guidance has been instrumental in improving the overall quality and presentation of our research, ensuring that the findings are communicated effectively and accurately.

Author Response

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

eLife assessment

This study presents valuable findings on diabetogenic risk from colorectal cancer (CRC) treatment. The authors claim that postoperative screening for type 2 diabetes should be prioritized in CRC survivors with overweight/obesity, irrespective of the oncological treatment received. The evidence supporting the claims is solid but requires confirmation in different populations. These results have theoretical or practical implications and will be of interest to endocrinologists, oncologists, general practitioners, gastrointestinal surgeons, and policymakers working on CRC and diabetes.

Author response: We thank you for taking the time to provide constructive feedback on our manuscript and for the useful suggestions. We have provided a point-by-point response to each of the reviewers’ comments with clearly marked changes to the manuscript.

Public reviews

Reviewer #1 (Public Review):

Summary:

In this study, the authors set out to determine whether colorectal cancer surgery site (right, left, rectal) and chemotherapy impact the subsequent risk of developing T2DM in the Danish national health register.

Strengths:

• The research question is conceptually interesting

• The Danish national health register is a comprehensive health database

• The data analysis was thorough and appropriate

• The findings are interesting, and a little surprising that there was no impact of chemotherapy on the development of T2DM

Weaknesses:

This is not a weakness as such, but in the discussion, I would consider adding some brief comment on the international generalizability of the findings - e.g. demographic make up of the Danish population health register and background rates of DM and obesity in this population with CRC compared to countries on other continents.

Author response: We agree that this information would be valuable. It has now been added in the Discussion section.

Changes in manuscript: "In Denmark, the overall T2D prevalence is 6.9%25, lower than the global average in 2021 (10.5%) and also falls below the estimate of high-income countries (11.1%).26 Similarly, the obesity rate of 20% aligns with other Scandinavian countries and is below that of most high-income nations.27” (Page 8, line 256-258)

A little more information would be helpful regarding how T2DM was diagnosed in the registry.

Author response: We have now added a more thorough explanation of how T2D was diagnosed in the Methods section.

Changes in manuscript: “Diabetes is defined as the second occurrence of any event across three types of inclusion events: 1) Diabetes diagnosed during hospitalisation 2) diabetes-specific services received at podiatrist 3) purchases of glucose lowering. Thus, if a patient developed transient T2D during chemotherapy treatment, it will only be an inclusion event if they purchase glucose lowering drugs. Individuals were classified as having T1D if they had received prescriptions for insulin combined with a diagnosis of type 1 from a medical hospital department. Otherwise, diabetes was classified as type 2.22” (Page 5, line 154-160)

If someone did develop transient hyperglycemia requiring DM medications during chemotherapy, would the investigators have been able to identify these people?

Author response: Yes, we have added a sentence in the Methods section.

Changes in manuscript: “Thus, if a patient developed transient T2D during chemotherapy treatment, it will only be an inclusion event if they purchase glucose lowering drugs.” (Page 5, line 156-158)

Would they have been classified as T2DM based on filling a prescription for DM meds for a period of time? Also, did the authors have information regarding time to development of T2DM after surgery?

Author response: Yes, if they have 2 (or more) prescriptions of oral glucose lowering drugs. Yes, we have information regarding time to development of T2DM after surgery and found no difference between the groups.

Changes in manuscript: Information on mean time to develop T2D post-surgery has now been added to Table 2.

In the adjusted Models, the authors did not adjust for cancer stage, even though cancer stage appears to be very different between the chemo and no chemo groups. It would be interesting to know if it affects the results if the model adjusted for cancer stage

Author response: We agree that adjustment for cancer stage would be a valuable information and we have performed the analysis and added a sentence in the Result section.

Changes in manuscript: An adjusted analysis of cancer stage now appears in the Supplementary table 1.

“Moreover, adjusting for cancer stage did not affect the results (Supplementary table 1).” (Page 7, line 219-220)

It would be worthwhile to report if mortality rates were different between the groups during follow up, and if the authors investigated whether perhaps differences in mortality rates led to specific groups living longer, and therefore having more time to develop DM

Author response: This situation is accounted for in the analysis by using Cox-regression analysis. This method accounts for the potential competing effect of mortality.

Changes in manuscript: None.

Overall, the authors achieved their aims, and the conclusions are supported by their results as reported.

The results are unlikely to significantly change patient treatment or T2DM screening in this population. With some additional information, as described above, the results would be of interest to the community.

Reviewer #2 (Public Review):

Summary:

The study showed the impact of cancer treatment on new onset of diabetes among patients with colorectal cancer using the national database. Findings reported that individuals with rectal cancer without chemotherapy were less likely to develop diabetes but among other groups, treatment didn't show any impact on the development of diabetes. BMI still played a significant role in developing diabetes regardless of treatment types.

Strengths:

One of the strengths of this study is innovative findings about the prognosis of colorectal cancer treatment stratified by treatment types. Especially, as it examined the impact of treatment on the risk of new chronic disease after diagnosis, it became significant evidence that suggests practical insights in developing a proper monitoring system for patients with colorectal cancer and their outcomes after treatment and diagnosis. It is imperative for providers to guide patients and caregivers to prevent adverse outcomes like new onset of chronic disease based on BMI and types of treatment. The next strength is the national database. As the study used the national database, the generalizability is validated.

Weaknesses:

Even though the study attempted to examine the impact of each treatment option, the dosage of chemotherapy and the types of chemotherapy were not able to be examined due to the data source.

Author response: No unfortunately not. We agree that this would have been valuable information. This is stated in the original manuscript as a limitation. Please refer to page 10 line 305-306.

Changes in manuscript: None.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Minor things:

There are minor inconsistencies in the methods and results regarding BMI. In the methods, the authors state that BMI <18.5 and >/=40 were excluded, but these groups are included in Table 2.

Author response: This has been corrected

Changes in manuscript: BMI groups <18.5 and >/=40 are now excluded in Table 2. (Page 18)

Line 204, I believe should be BMI 18.5-24.9, not 20-24.9.

Author response: This has been corrected

Changes in manuscript: “For each group (type of surgery ± chemotherapy), the HR for developing T2D depending on BMI subgroups was calculated by using Cox regression analysis adjusted for age, sex, year of surgery, and ASA score using normal weight (BMI:18.5-24.9) as the reference group.” (Page 6, line 184-186)

Rather than showing the BMI mean in Table 1, it would be interesting to see the BMI breakdown by category.

Author response: Yes, we agree. This analysis has now been added to Table 1

Changes in manuscript: Please refer to Table 1

Re line 215, I would consider rewriting to remove the multiple negatives -e.g. Radiation therapy in rectal resected had did not impact the incidence rate of T2D in the Rectal-No-Chemo group or Rectal-Chemo group

Author response: This has been corrected. Please refer to the Result section.

Changes in manuscript: “Radiation therapy in the rectal resected groups had no impact on the incidence rate of T2D (Table 2); and the unadjusted/adjusted HR of developing T2D was non-significant when comparing Rectal-No-Radiation patients with Rectal-Radiation patients (Table 3).” (Page 7, 223-225)

Consider changing some of the "didn't"s in the discussion to "did not"

Author response: This has been corrected.

Changes in manuscript: Revised and corrected throughout the discussion.

Reviewer #2 (Recommendations For The Authors):

Some points need to be clarified and improved.

In the method, patients with Type 1 Diabetes were excluded in the baseline but some patients were diagnosed with Type 1 diabetes after treatment and they were included in your analysis. It is interesting to identify Type 1 Diabetes after the treatment as an outcome, do you think that this diagnosis is caused by the treatment? And incidence rate or other HRs did not seem to include Type 1 Diabetes as stated in the methods. Did you exclude every Type 1 diabetes? If not, It needs to give further explanation about this outcome since the mechanism of Type 1 Diabetes and Type 2 Diabetes is different.

Author response: This matter has now been clarified in the Methods section.

Changes in manuscript: “Additionally, individuals diagnosed with Type 1 diabetes (T1D) either before or after surgery were excluded, along with those diagnosed with T2D preoperatively or within the first 2 weeks postoperatively, as the last group probably represents patients with preoperatively unknown pre-existing prediabetes or diabetes.22” (Page 4, line: 125-128)

Despite limited existing findings, some studies actually reported the incidence rates of Type 2 Diabetes among patients with CRC (Singh S, Earle CC, Bae SJ, et al. Incidence of Diabetes in Colorectal Cancer Survivors. J Natl Cancer Inst. 2016;108(6):djv402. Published 2016 Feb 2. doi:10.1093/jnci/djv402; Khan NF, Mant D, Carpenter L, Forman D, Rose PW. Long-term health outcomes in a British cohort of breast, colorectal and prostate cancer survivors: a database study. Br J Cancer. 2011;105 Suppl 1(Suppl 1):S29-S37. doi:10.1038/bjc.2011.420; Jo A, Scarton L, O'Neal LJ, et al. New onset of type 2 diabetes as a complication after cancer diagnosis: A systematic review. Cancer Med. 2021;10(2):439-446. doi:10.1002/cam4.3666) whereas your study examined the impact of the different types of treatments.

Author response: Our findings of T2D rate among CRC patients are now commented on in discussion section, and the abovementioned studies are included as references.

Changes in manuscript: “This national cohort study demonstrated an IR of developing T2D after CRC surgery similar to previous studies.5,11” (Page 8, line 237-238)

To strengthen the presentation, some places should be revised.

• Line 216: it says that Table 1 showed no impact of radiation therapy on the incidence rate of T2D. However, either the interpretation or the table number seems wrong. Table 1 does not have this information. Correct this statement.

• Line 239: There are typo and incomplete sentence. Check the sentence and correct the sentence.

• Line 257-261: It may be a systematic issue to separate these two paragraphs. But two paragraphs seem related so make them one paragraph.

Author response: These suggested changes have been made. Regarding line 216 the paragraph has been adjusted to the following:

Changes in manuscript: “Radiation therapy in the rectal resected groups had no impact on the incidence rate of T2D (Table 2); and the unadjusted/adjusted HR of developing T2D was non-significant when comparing Rectal-No-Radiation patients with Rectal-Radiation patients (Table 3).” (Page 7, 223-225)

Reference

(1) Araghi M, Soerjomataram I, Jenkins M, et al. Global trends in colorectal cancer mortality: projections to the year 2035. Int J Cancer. 2019;144(12):2992-3000. doi:10.1002/ijc.32055

(2) Arnold M, Sierra MS, Laversanne M, Soerjomataram I, Jemal A, Bray F. Global patterns and trends in colorectal cancer incidence and mortality. Gut. 2017;66(4):683-691. doi:10.1136/gutjnl-2015-310912

(3) González N, Prieto I, del Puerto-Nevado L, et al. 2017 Update on the Relationship between Diabetes and Colorectal Cancer: Epidemiology, Potential Molecular Mechanisms and Therapeutic Implications. Vol 8.; 2017. www.impactjournals.com/oncotarget

(4) Mills KT, Bellows CF, Hoffman AE, Kelly TN, Gagliardi G. Diabetes mellitus and colorectal cancer prognosis: A meta-analysis. Dis Colon Rectum. 2013;56(11):1304-1319. doi:10.1097/DCR.0b013e3182a479f9

(5) Singh S, Earle CC, Bae SJ, et al. Incidence of Diabetes in Colorectal Cancer Survivors. J Natl Cancer Inst. 2016;108(6). doi:10.1093/jnci/djv402

(6) Xiao Y, Wang H, Tang Y, et al. Increased risk of diabetes in cancer survivors: a pooled analysis of 13 population-based cohort studies. ESMO Open. 2021;6(4). doi:10.1016/j.esmoop.2021.100218

(7) Colorectal D, Nordcan 2019. 5-Year Age-Standardised Relative Survival (%), Males and Females. Accessed September 12, 2022. “https://nordcan.iarc.fr/en/dataviz/survival?cancers=520&set_scale=0&sexes=1_2&populations=208”" has been copied into your clipboard

(8) Nano J, Dhana K, Asllanaj E, et al. Trajectories of BMI Before Diagnosis of Type 2 Diabetes: The Rotterdam Study. Obesity. 2020;28(6):1149-1156. doi:10.1002/oby.22802

(9) Maddatu J, Anderson-Baucum E, Evans-Molina C. Smoking and the risk of type 2 diabetes. Translational Research. 2017;184:101-107. doi:10.1016/j.trsl.2017.02.004

(10) Lega IC, Lipscombe LL. Review: Diabetes, Obesity, and Cancer-Pathophysiology and Clinical Implications. Endocr Rev. 2020;41(1). doi:10.1210/endrev/bnz014 (11) Jo A, Scarton L, O’Neal LTJ, et al. New onset of type 2 diabetes as a complication after cancer diagnosis: A systematic review. Cancer Med. 2021;10(2):439-446. doi:10.1002/cam4.3666

(12) Feng JP, Yuan XL, Li M, et al. Secondary diabetes associated with 5-fluorouracil-based chemotherapy regimens in non-diabetic patients with colorectal cancer: Results from a single-centre cohort study. Colorectal Disease. 2013;15(1):27-33. doi:10.1111/j.1463-1318.2012.03097.x

(13) Lee EK, Koo B, Hwangbo Y, et al. Incidence and disease course of new-onset diabetes mellitus in breast and colorectal cancer patients undergoing chemotherapy: A prospective multicenter cohort study. Diabetes Res Clin Pract. 2021;174. doi:10.1016/j.diabres.2021.108751

Author Response

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

We would like to thank the reviewer for the constructive comments. We have revised the papers to address the concerns. In summary, here is what we included in the revised version.

• Statistical analysis using biological replicate datasets for WT and K40R doublet microtubule.

• Addition figures for statistical analysis and MIP decorations in MEC17-KO and K40R.

• Revised texts and figures to reflect the new changes, cite proper references and fix small errors throughout the text.

Reviewer #1 (Public Review):

Summary:

The study "Effect of alpha-tubulin acetylation on the doublet microtubule structure" by S. Yang et al employs a multi-disciplinary approach, including cryo-electron microscopy (cryo-EM), molecular dynamics, and mass spectrometry, to investigate the impact of α-tubulin acetylation at the lysine 40 residue (αK40) on the structure and stability of doublet microtubules in cilia. The work reveals that αK40 acetylation exerts a small-scale, but significant, effect by influencing the lateral rotational angle of the microtubules, thereby affecting their stability. Additionally, the study provided an explanation of the relationship between αK40 acetylation and phosphorylation within cilia, despite that the details still remain elusive. Overall, these findings contribute to our understanding of how post-translational modifications can influence the structure, composition, stability, and functional properties of important cellular components like cilia.

Strengths:

(1) Multi-Disciplinary Approach: The study employs a robust combination of cryo-electron microscopy (cryo-EM), molecular dynamics, and mass spectrometry, providing a comprehensive analysis of the subject matter.

(2) Significant Findings: The paper successfully demonstrates the impact of αK40 acetylation on the lateral rotational angles between protofilaments (inter-PF angles) of doublet microtubules in cilia, thereby affecting their stability. This adds valuable insights into the role of post-translational modifications in cellular components.

(3) Exploration of Acetylation-Phosphorylation Relationship: The study also delves into the relationship between αK40 acetylation and phosphorylation within cilia, contributing to a broader understanding of post-translational modifications.

(4) High-quality data: The authors are cryo-EM experts in the field and the data quality presented in the manuscript is excellent.

(5) Depth of analysis: The authors analyzed the effects of αK40 acetylation in excellent depth which significantly improved our understanding of this system.

Thank you for highlighting the strength of our paper.

Weaknesses:

I have no major concerns about this paper, but would recommend that a few minor issues be addressed.

(1) Lack of Statistical Details: The review points out that the paper could benefit from providing more statistical details, such as the number of particles and maps used for analysis, randomization methods, and dataset splitting for statistical analyses.

To address this, we analyzed the true biological replicate datasets (different cultures, cryo-EM vitrification and data collection) from WT and K40R. Since the MEC17-KO was collected as only one dataset, we decided to not divide the MEC-17 using randomization since the division does not lead to independent sets, which tends to yield identical results in the case of cryo-EM. The biological replicates help us to see how consistent is our structure data for interpretation. The information about the replicate dataset is now included in Table 1. The description of the analysis is highlighted in the manuscript and included in the Materials & Methods and Fig. S4.

In summary, the biological replicate between the WT data indicates that the inter-PF rotation angles are significantly consistent between two biological replicates. On the other hand, there are variations in the inter-PF angles between two replicates of K40R data in the B-tubule (Fig. S4B).

Overall, when pooling the data together ( 6 + 6 measurement points for WT dataset 1 & 2 and 6 + 6 measurement points for K40R dataset 1 & 2 and 6 measurement points for MEC17-KO) (Fig. S4), our analysis yields the same statistical significance as the average of all datasets (6 measurement points of the total averages for WT, K40R and MEC17-KO) (Fig. 3).

In addition, the variation in inter-PF rotation angles between certain PF pairs within the K40R replicates (B7B8 and B9B10) is similar to the variation to MEC17-KO. This suggests that the deacetylation induces variation in inter-PF angles while the inter-PF angles are maintained consistently in WT.

(2) Questionable Conclusion Regarding MIPs: The reviewer suggests caution in the paper's conclusion that "Acetylation of αK40 does not affect tubulin and MIPs." The reviewer recommends that this conclusion be more specific or supported by additional evidence to exclude all other possibilities.

We now revised the text to make sure we do not overclaim that “Acetylation of αK40 does not affect tubulin and MIPs.” We now describe more specifically as “Lack acetylation of αK40 does not significantly affect tubulin and MIP interactions”. Also the text was edited to make the statement more specific.

(3) Need for Additional Visual Data: The reviewer recommends that an enlarged local density map along with fitted PDB models be provided in a supplementary figure, such as Figure 4.

We now include the density maps and fitted PDB models in Fig. 4 and Fig. S5. We also include more snapshots of the MIP in K40R and MEC17-KO in Figure S3.

Overall, the paper is strong in its scientific approach and findings but could benefit from additional statistical rigor and clarification of certain conclusions.

Page 11, Line 226: "cluster consists of only ~ acetylated", lacks the percentage. Please correct this.

We corrected it.

Author Response

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

Reviewer #1 (Recommendations For The Authors):

(1) V2 epitopes exhibit properties of CD4i epitopes in that they are largely absent from the native Env surface, probably by glycan-occlusion, but become more exposed upon CD4 binding. Although the V2-scaffolds were produced in GnTi- cells to produce highmannose proteins, it appears that no systematic analysis of glycan content or structure was carried out save for enzymatic deglycosylation of the constructs to sharpen bands on SDS-PAGE gels. It would be helpful if the authors could comment on how the lack of this information might impact their conclusions.

We thank the reviewer for this comment.

The lack of native glycan structures is a common phenomenon in all HIV studies involving in vitro cell culture-expressed envelope proteins.

As the reviewer mentioned, it is clear that our V1V2 scaffolds produced in GnTi-cells contain the expected high-mannose glycans, as evident from a significant shift and sharpening of the protein bands on the SDS-PAGE gel upon deglycosylation with the PNGase enzyme.

In our previously published studies by Chand et al.,2017* (ref. below), the V1V2 scaffolds were shown to bind to glycan-dependent PG9 antibody suggesting that the conformation of the PG9 epitope is retained in the high-mannose V1V2 scaffold. This information has also been added to the “Hypothesis and Experimental Design” section of the Results in the revised manuscript.

Additionally, as shown in Results, the human antibodies elicited in study participants against native glycosylated envelope protein due to natural HIV-1 infection distinguished the H173 and Y 173 epitopes in the high-mannose scaffolds, which was also recapitulated in our mouse studies using the GnTi-expressed high-mannose V1V2 scaffolds as antigens.

Therefore, it does not seem likely that differences in glycans per se majorly affected the binding or the conclusions from our studies.

*Chand S, Messina EL, AlSalmi W, Ananthaswamy N, Gao G, Uritskiy G, Padilla-Sanchez V, Mahalingam M, Peachman KK, Robb ML, Rao M, Rao VB. Glycosylation and oligomeric state of the envelope protein might influence HIV-1 virion capture by α4β7 integrin. Virology. 2017 Aug;508:199-212. doi: 10.1016/j.virol.2017.05.016. Epub 2017 May 31. PMID: 28577856; PMCID: PMC5526109.

(2) Similarly, the MD simulations appear to be performed without taking glycan structure/occupancy.

We were unable to perform glycan-dependent MD simulation studies because of the high computational demands and also the technical limitations that existed at the time of the study several years ago. Therefore, we focused on the protein backbone of the short C-strand in the V2 region that lacks glycan sites and in previous published studies has been demonstrated as conformationally polymorphic.

Since this C-strand epitope is the binding site for many V2-directed antibodies identified previously, we hypothesized that it is relevant to explore this small immunogenic epitope for its propensity to change conformation due to an escape mutation discovered at residue 173 in a natural HIV-1 infection. How might this epitope behave in MD simulations in the presence of different glycans requires further investigation.

Author Response

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

Public Reviews:

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. Additionally, the authors generated novel knock-in HA-SMAD1 and PA-SMAD5 tagged mice to combat antibody issues facing the field, generating a novel model to advance the study of BMP signaling in the female reproductive tract. During decidualization in a murine model, SMAD1/5 are bound to many genomic sites of genes important in decidualization and pregnancy and coregulated responses with progesterone receptor signaling.

Strengths

The authors utilized powerful next generation sequencing and identified important transcriptional mechanisms of SMAD1/5 and PGR during decidualization in vivo.

Weaknesses<br /> None.

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.

We thank you for the summary and consideration.

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. Overall the present manuscript is an excellent resource paper for the field of reproductive biology.

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 an outdated method on inferring the cell type composition. Evidence was provided for potential associations between SMAD1/5 and other major transcription factors. However, causal effects of SMAD1/5 on the genome occupancy of other major uterine transcription factors were discussed but not experimentally examined in the present manuscript, which is understandable.

For data in Figure 2B, the current manuscript fails to elaborate the common and distinct features between clusters 1 and 3 as well as the biological significance of having two separate clusters for SMAD1. In addition, Figure S1A shows overlapping genome occupancy between SMAD1 and SMAD5, which is not clearly demonstrated in Figure 2B.

Thank you for the comments. We’ve added additional interpretations in Lines 281-283, addressing the clustering results mentioned in Figure 2B as suggested. We do appreciate the overlapping genome occupancy in Cluster 1, although the signal intensities may differ between two groups.

Lines 281-283:

“Peaks in cluster 1 exhibit a shared enrichment for both SMAD1 and SMAD5, whereas clusters 2 and 3 demonstrate preferential enrichment for SMAD5 and SMAD1, respectively.”

For data in Figure 5A, the result description does not provide adequate information to guide readers to full understanding of the data. The biological meaning behind the three PR clusters is not stated nor speculated. Moreover, Figure 5A and Figure S1B are inherently connected but fail to be adequately described in the main text.

Thank you for the comments. We’ve added additional interpretations in Lines 415-421 discussing the clustering results mentioned in Figure 5A, together with Supplement Figure 1C (Former Supplement Figure 1B) as suggested.

Lines 415-421:

“Based on the k-means clustering results of the peaks, we demonstrated clusters with shared occupancy between SMAD1/5 and PR (cluster 1), preferential deposition in the SMAD1 (cluster 2), SMAD5 (cluster 4) and PR (clusters 3,5), respectively. Interestingly, between clusters 3 and 5, although the primary enrichment is for PR, overall, the signal intensities for SMAD5 are higher in cluster 5. Together with previous analysis on genes uniquely or commonly bound by SMAD1/5 (Supplement Figure 1A), we speculate such observation can be attributed to a subset of the genes that are potentially co-regulated by SMAD5 and PR.”

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. Additionally, 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 comments. We recognized this limitation and discussed future options regarding this in Lines 578-583.

Lines 578-583:

“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. Further work is needed to delineate binding and transcriptional activation of SMAD1/5 and the progesterone receptor in the uterine compartments.

We thank the reviewer for the insightful comment. Given the multifaceted roles of SMAD1/5 play the female reproductive tract, we concur that future studies will benefit from a more compartmentalized approach, as discussed in Lines 526-538.

Lines 526-538:

“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 coregulatory 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 validations using single-cell sequencing 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. Further investigation is needed to understand the meaning of these differences and as they relate to the entire SMAD transcriptome.

Thank you for the comments. In the current study, we used human endometrial stromal cells as a model to validate our findings functionally, aiming to mimic the specific time point during decidualization. We acknowledge the similarities and differences between the mouse and human cell models, and this information needs to be considered when evaluating genome-wide effects on the transcriptome. This point is discussed ins Lines 589-597.

Lines 589-597:

“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.”

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

The inference on the cell type composition could use updated bioinformatic tools, which are purely computational without costly and time-consuming wet-lab resources. Perhaps this part of the description could be streamlined if the authors chose to use the method in the current version.

We thank the reviewer for the suggestion. We added the analysis of the cell type composition using the updated tool CIBERSORTx (PMID:31061481) and included the results and discussion regarding the cell type composition changes in Supplement Figure 1B and Lines 392-407.

Lines 392-407

“To explore the major cell types regulated by SMAD1/5, first, we used CIBERSORTx to analyze and depict changes in the cell populations upon SMAD1/5 depletion in the mouse uterus during early pregnancy. By imputing the bulk uterine gene expression profiles to previously published mouse uterine single-cell datasets using CIBERSORTx, we were able to compare changes across both samples and cell types upon the SMAD1/5 perturbation in the mouse uterus. We highlight the proportional increase in the epithelial cells, as well as the decrease in the decidual stromal cells and smooth muscle cells in mice lacking uterine SMAD1/5 during the periimplantation phase (Supplement Figure 1B). Such cell populational changes are in line with the phenotypical observations of decidualization failure and excessive proliferation in the epithelial compartment. In addition, to explore the expression patterns of SMAD1/5 direct targets in human, we profiled the expression levels of the key “up-targets” and “down-targets” in the different cell types of the human endometrium. Using previously published single-cell RNA seq data of human endometrium, we visualized the expression patterns of suppressive targets and activating targets of SMAD1/5 (Figure 4E). Apart from the major epithelial and stromal compartments, SMAD1/5 target genes are also widely expressed in the immune cell populations. Such observations reinforced the importance of the BMP signaling pathways in establishing an immune-privileged environment at the maternal-fetal interface.”

Author Response

Reviewer #1 (Public Review):

Reviewer 1: The structural part of this work is interesting, as it is the first structure of Pin1 with a ligand that bridges both domains. They might want to underline this - all other structures in the PDB have a single domain complex, but never both domains by a single longer peptide.

Done. We have highlighted the novelty of the structure in the abstract, introduction (page 5); and discussion (section “The Pin1-PKC interface is described by a novel bivalent interaction mode”, page 24).

Reviewer 1: I would however question the static representation of this structure - the 90{degree sign} kink in the peptide when complexed is probably one single snapshot, but I hardly believe the PPIase/WW domain orientation to be static. Unless the authors have additional information to stand by this static structure, this point merits being commented on in the manuscript.

Done. Following the reviewer’s suggestion and to avoid the impression of “static” structure, we have added sentences that highlight the dynamic aspects of the complex evident from the entire ensemble representation of Figure 5-figure supplement 2:

Page 15 (Results):

“Of note, the linker region connecting the two domains retains its flexibility in the complex and confers some variability onto the relative positions of the WW and PPIase domains, as is evident from the ensemble representation of Figure 5-figure supplement 2. The complex exhibits novel structural features that distinguish it from all other structures of Pin1 complexes known to date. These features are highlighted in Fig. 6 using the lowest-energy structure of the ensemble.”

Page 24 (Discussion): “Moreover, the retention of linker flexibility in the Pin1::pV5bII complex suggests that Pin1 can potentially adopt minor “extended” states that would not be readily detectable by ensemble-averaged methods such as solution NMR.”

Also, in describing specific interactions in the section “Structural basis of the Pin1-PKCII C-term bivalent recognition mode”, we now note how many structures of the Pin1-pV5bII ensemble have those interactions.

Reviewer 1: I would like to point out to literature that described for example the non-canonical binding (Yeh ES, Lew BO & Means AR (2006) The loss of PIN1 deregulates cyclin E and sensitizes mouse embryo fibroblasts to genomic instability. J Biol Chem 281, 241-251. Pin1 recognizes cyclin E via a noncanonical pThr384- Gly385 motif [33] rather than the pThr380-Pro381 motif.). They mention briefly the absence of isomerase activity in similar TPP motifs, but this information might already come in the Results section.

Done. We have incorporated this information in the Discussion section, page 25 (last paragraph).

Reviewer 1: The expression levels of Pin1 and PKCa are amazingly linear (Fig 7A), but when they overexpress WT Pin1 in a KO line, with 3-4 times higher overexpression, the PKCa levels are hardly higher than in the original WT cell line.

We thank Reviewer 1 for raising this interesting point. Our simple interpretation of the data is that physiological expression of Pin1 in the cell model we use is a limiting factor in the stimulated PKCa degradation pathway, but that Pin1 is no longer a limiting factor at higher expression levels. We now include this point in the Discussion, page 26.

Reviewer 1: Also, the levels in the W34A/R68A/R69A (abolishing both WW and PPIase binding functions) are surprising, why would PKCa levels rise above the level found in the Pin1 KO cells?

This result remains a puzzle but, as we are including all independent biological replicates in the analysis, the data are the data. Moreover, by assessing the functional complementation data to the KO by two-tailed t-test (see last point below), this effect does not reach statistical significance. Nonetheless, as the result is reproducible, we now comment on this effect in the Results, page 21. One speculation is this triple mutant has dominant negative properties imposed on some limiting factor in PKCa degradation that are revealed in the absence of WT Pin1. Considerably more work needs to be done to settle this issue. However, in light of the fact that this result does not conflict with the structural/biochemical data (rather, it is consistent with it), we hope this positive response satisfies the Reviewer.

Reviewer 1: Finally, if even slight overexpression of the C113S catalytically inactive mutant leads to more efficient PKCa degradation than overexpression of the WT Pin1 (Figure 7C), it is hard to interpret. The conclusion that Pin1-mediated regulation of PKCa requires a bivalent interaction mode of Pin1 with PKCa independent of its catalytic activity do depend on these data, so they merit further analysis.

We certainly had no intention of concluding that the C113S catalytically inactive mutant is more efficient with regard to promoting PKCa degradation than overexpression of the WT Pin1. That overstates the data. We concede that our organization of the Pin1 rescue data in the original Fig 7C confused the issue, and that the original text also invited conclusions that overstate the result. To correct this problem, we reorganized Fig. 7C to simplify the presentation by comparing the complementation data to the KO. All statistical comparisons are now to the KO cell line (not to WT as before) and we employ the two-tailed t-test to compare the data. Statistical significance is attained only for reconstituted WT and C113S Pin1 expression. The text is also appropriately revised to describe the results clearly. We trust the Reviewer agrees that the C113S data are compelling and are consistent with a noncanonical (noncatalytic) mode of PKCa regulation by Pin1. This is a major point of Fig 7C as it links the structural/biochemical data to a cellular context.

Author Response

eLife assessment

This computational study is a valuable empirical investigation into the common trait of neurons in brains and artificial neural networks: responding effectively to both objects and their mirror im- ages and it focuses on uncovering conditions that lead to mirror symmetry in visual networks and the evidence convincingly demonstrates that learning contributes to expanding mirror symmetry tuning, given its presence in the data. Additionally, the paper delves into the transformation of face patches in primate visual hierarchy, shifting from view specificity to mirror symmetry to view invariance. It empirically analyzes factors behind similar effects in two network architec- tures, and key claims highlight the emergence of invariances in architectures with spatial pooling, driven by learning bilateral symmetry discrimination and importantly, these effects extend be- yond faces, suggesting broader relevance. Despite strong experiments, some interpretations lack explicit support, and the paper overlooks pre-training emergence of mirror symmetry.

As detailed above, we have now analyzed several convolutional architectures and made a direct link between the artificial neural networks and neuronal data to further support our claims (refer to Figure 6, S10- 13).

To address the concern about pre-training emergence of mirror symmetry, we conducted a new analysis inspecting unit-level response profile, following Baek and colleagues (2021). This analysis is described in detail below (response to R3). In brief, we found that the first fully connected layer in trained networks exhibits twice the number of mirror symmetric units found before training. In addition to our population-level observations (Fig. S2) and explicit training- dataset manipulations (Fig. 4), this finding supports the interpretation of training to discriminate among mirror- symmetric object categories as a major factor behind the emergence of mirror symmetric viewpoint tuning.

Reviewer 1 (Public Review):

By using deep convolutional neural networks (CNNs) as model for the visual system, this study aims at understanding and explaining the emergence of mirror-symmetric viewpoint tuning in the brain.

Major strengths of the methods and results:

1) The paper presents comprehensive, insightful and detailed analyses investigating how mirror- symmetric viewpoint tuning emergence in artificial neural networks, providing significant and novel insights into this complex process.

2) The authors analyze reflection equivariance and invariance in both trained and untrained CNNs’ convolutional layers. This elucidates how object categorization training gives rise to mirror-symmetric invariance in the fully-connected layers.

3) By training CNNs on small datasets of numbers and a small object set excluding faces, the authors demonstrate mirror-symmetric tuning’s potential to generalize to untrained categories and the necessity of view-invariant category training for its emergence.

4) A further analysis probes the contribution of local versus global features to mirror-symmetric units in the first fully-connected layer of a network. This innovative analysis convincingly shows that local features alone suffice for the emergence of mirror-symmetric tuning in networks.

5) The results make a clear prediction that mirror-symmetric tuning should also emerge for other bilaterally symmetric categories, opening avenues for future neural studies.

We are grateful for your insightful feedback and the positive evaluation of our study on mirror-symmetric viewpoint tuning in neural networks. Your constructive comments considerably improved the manuscript. We eagerly look forward to exploring the future research avenues you have highlighted.

Major weaknesses of the methods and results:

Point 1.1) The authors propose a mirror-symmetric viewpoint tuning index, which, although innovative, complicates comparison with previous work and this choice is not well motivated. This index is based on correlating representational dissimilarity matrices (RDMs) with their flipped versions, a method differing from previous approaches.

We have revised the Methods section to clarify the motivation for the mirror-symmetric viewpoint tuning index we introduced.

Manuscript changes:

Previous work quantified mirror-symmetry in RDMs by comparing neural RDMs to an idealized mirror- symmetric RDM (see Fig. 3c-iii in [14]). Although highly interpretable, such an idealized RDM encompasses implicit assumptions about representational geometry that are unrelated to mirror-symmetry. For example, consider a neural RDM reflecting perfect mirror-symmetric viewpoint tuning and wherein for each view, the distances among all of the exemplars are equal. Such a neural RDM would fit an idealized mirror- symmetric RDM better than a neural RDM reflecting perfect mirror-symmetric viewpoint tuning but with non-equidistant exemplars. In contrast, the measure proposed in Eq. 2 equals 1.0 in both cases.

Point 1.2> Faces exhibit unique behavior in terms of the progression of mirror-symmetric viewpoint tuning and their training task and dataset dependency. Given that mirror-symmetric tuning has been identified in the brain for faces, it would be beneficial to discuss this observation and provide potential explanations.

We revised the caption of Figure S1 to explicitly address this point:

Manuscript changes:

For face stimuli, there is a unique progression in mirror-symmetric viewpoint tuning: the index is negative for the convolutional layers and it abruptly becomes highly positive when transitioning to the first fully connected layer. The negative indices in the convolutional layers can be attributed to the image-space asymmetry of non-frontal faces; compared to other categories, faces demonstrate pronounced front-back asymmetry, which translates to asymmetric images for all but frontal views (Fig. S8). The features that drive the highly positive mirror-symmetric viewpoint tuning for faces in the fully connected layers are training-dependent (Fig. S2), and hence, may reflect asymmetric image features that do not elicit equivariant maps in low-level representations; for example, consider a profile view of a nose. Note that cars and boats elicit high mirror- symmetric viewpoint tuning indices already in early processing layers. This early mirror-symmetric tuning is independent of training (Fig. S2), and hence, may be driven by low-level features. Both of these object categories show pronounced quadrilateral symmetry, which translates to symmetric images for both frontal and side views (Fig. S8).

Point 1.3: 3. Previous work reported critical differences between CNNs and neural represen- tations in area AL indicating that mirror-symmetric viewpoint tuning is less present than view invariance in CNNs compared to area AL. While such findings could potentially limit the use- fulness of CNNs as models for mirror-symmetric viewpoint tuning in the brain, they are not addressed in the study.

This point is now addressed explicitly in the caption of Figure S9:

Manuscript changes:

Yildirim and colleagues [14] reported that CNNs trained on faces, notably VGGFace, exhibited lower mirror- symmetric viewpoint tuning compared to neural representations in area AL. Consistent with their findings, our results demonstrate that VGGFace, trained on face identification, has a low mirror-symmetric viewpoint tuning index. This is especially notable in comparison to ImageNet-trained models such as VGG16. This difference between VGG16 and VGGFace can be attributed to the distinct characteristics of their training datasets and objective functions. The VGGFace training task consists of mapping frontal face images to identities; this task may exclusively emphasize higher-level physiognomic information. In contrast, training on recognizing objects in natural images may result in a more detailed, view-dependent representation. To test this potential explanation, we measured the average correlation-distance between the fc6 representations of different views of the same face exemplar in VGGFace and VGG16 trained on ImageNet. The average correlation-distance between views is 0.70±0.04 in VGGFace and 0.93±0.04 in VGG16 trained on ImageNet. The converse correlation distance between different exemplars depicted from the same view is 0.84±0.14 in VGGFace and 0.58±0.06 in VGG16 trained on ImageNet. Therefore, as suggested by Yildirim and colleagues, training on face identification alone may result in representations that cannot explain intermediate levels of face processing.

Point 1.4) The study’s results, while informative, are qualitative rather than quantitative, and lack direct comparison with neural data. This obscures the implications for neural mechanisms and their relevance to the broader field.

We addressed this point by conducting a quantitative comparison between the architectures of various networks and neural response patterns in monkey face patches (see Figures 6, S10-S13, appearing above).

Point 1.5) The study provides compelling evidence that learning to discriminate bilaterally symmetric objects (beyond faces) induces mirror-symmetric viewpoint tuning in the networks, qualitatively similar to the brain. Moreover, the results suggest that this tuning can, in principle, generalize beyond previously trained object categories. Overall, the study provides important conclusions regarding the emergence of mirror-symmetric viewpoint tuning in networks, and potentially the brain. However, the conducted analyses and results do not entirely address the question why mirror-symmetric viewpoint tuning emerges in networks or the brain. Specifically, the results leave open whether mirror-symmetric viewpoint tuning is indeed necessary to achieve view invariance for bilaterally symmetric objects.

We believe that mirror-symmetric viewpoint tuning is not strictly necessary for achieving view-invariance. However, it is a plausible path from view-dependence to view invariance. We addressed this point in the updated limitations subsection of the discussion.

Manuscript changes:

A second consequence of the simulation-based nature of this study is that our findings only establish that mirror-symmetric viewpoint tuning is a viable computational means for achieving view invariance; they do not prove it to be a necessary condition. In fact, previous modeling studies [10, 19, 61] have demonstrated that a direct transition from view-specific processing to view invariance is possible. However, in practice, we observe that both CNNs and the face-patch network adopt solutions that include intermediate representations with mirror-symmetric viewpoint tuning.

Taken together, this study moves us a step closer to uncovering the origins of mirror-symmetric tuning in networks, and has implications for more comprehensive investigations into this neural phenomenon in the brain. The methods of probing CNNs are innovative and could be applied to other questions in the field. This work will be of broad interest to cognitive neuroscientists, psychologists, and computer scientists.

We appreciate your acknowledgment of our study’s contribution to understanding mirror-symmetric tuning in networks and its wider implications in the field.

Reviewer 2 (Public Review);

Strengths

1) The statements made in the paper are precise, separating observations from inferences, with claims that are well supported by empirical evidence. Releasing the underlying code repository further bolsters the credibility and reproducibility. I especially appreciate the detailed discussion of limitations and future work.

2) The main claims with respect to the two convolutional architectures are well supported by thorough analyses. The analyses are well-chosen and overall include good controls, such as changes in the training diet. Going beyond ”passive” empirical tests, the paper makes use of the fully accessible nature of computational models and includes more ”causal” insertion and deletion tests that support the necessity and sufficiency of local object features.

3) Based on modeling results, the paper makes a testable prediction: that mirror-symmetric viewpoint tuning is not specific to faces and can also be observed in other bilaterally symmetric objects such as cars and chairs. To test this experimentally in primates (and potentially other model architectures), the stimulus set is available online.

We express our gratitude for your constructive feedback. Your acknowledgment of the clarity of our statements and the robustness of our empirical evidence is greatly appreciated. We are also thankful for your recognition of our comprehensive analyses and the testable predictions arising from our work.

Point 2.1: Weaknesses

My main concern with this paper is in its choice of the two model architectures AlexNet and VGG. In an earlier study, Yildirim et al. (2020) found an inverse graphics network ”EIG” to better correspond to neural and behavioral data for face processing than VGG. All claims in the paper thus relate to a weaker model of the biological effects since this work does not analyze the EIG model. Since EIG follows an analysis-by-synthesis approach rather than standard classification training, it is unclear whether the claims in this paper generalize to this other model architecture. It is also unclear if the claims will hold for: 1) transformer architectures, 2) the HMAX architecture by Leibo et al. (2017) which has also been proposed as a computational explanation for mirror-symmetric tuning, and, as the authors note in the Discussion, 3) deeper architectures such as ResNet-50 which tend to better align to neural and behavioral data in general. These architectures include different computational motifs such as skip connections and a much smaller proportion of fully-connected layers which are a major focus of this work.

Overall, I thus view the paper’s claims as limited to AlexNet- and VGG-like architectures, both of which fall behind state-of-the-art in their alignment to primates in general and also specifically for mirror-symmetric viewpoint tuning.

We understand your concern regarding the choice of AlexNet and VGG architectures. The decision to focus on these models was driven by the need for a straightforward macroscopic correspondence between the layer structure of the artificial networks and the ventral visual stream. However, acknowledging this potential limitation of generality, we have expanded our analysis to include the EIG model, a transformer architecture, the HMAX model, and deeper convolutional architectures like ResNet-50 and ConvNeXt. Our revised analysis, detailed in Figures S1, S9, and S10-S13, incorporates these additional models and offers a comprehensive evaluation of their brain alignment and mirror-symmetric viewpoint tuning. We found that while the architectures indeed vary in their computational motifs, the emergence of mirror-symmetric viewpoint tuning is not exclusive to AlexNet and VGG. It occurs for every CNN we tested, exactly at the stage where equivariant feature maps are pooled globally. We believe that the new analyses extend the generality of our findings and remove the concern that our claims apply only to older, shallower networks.

For details, please refer to Point 1 in the ’Essential Revisions’ section.

Point 2.2: Minor weaknesses

1) Figure 1A: since the relevance to primate brains is a major motivator of this work, the results from actual neural recordings should be shown and not just schematics. For instance, the mirror symmetry in AL is not as clean as the illustration (compare with Fig. 3 in Yildirim et al. 2020), and in the paper’s current form, this is not easily accessible to the reader.

Thank you for your feedback regarding the presentation of neural recordings in Figure 1A. We have updated Figure 1A to include actual neural RDMs instead of the previous schematic representations.

Point 2.3: 2. Figure 4 L832-845: The claims for the effect of training on mirror-symmetric viewpoint tuning are with respect to the training data only, but there are other differences between the models such as the number of epochs (250 for CIFAR-10 training, 200 for all other datasets), the learning rate (2.5 ∗ 10−4 for CIFAR-10, 10−4 for all others), the batch size (128 vs 64), etc. I do not expect these choices to make a major difference for your claims, but it would be much cleaner to keep everything but the training dataset consistent. Especially the different test accuracies worry me a bit (from 81% to 92%, and they appear different from the accuracy numbers in figure S4 e.g. for CIFAR-10 and asymSVHN), at the very least those should be comparable.

We addressed this point by retraining the models while holding most of the hyperparameters constant. Specifically, we standardized the number of epochs, batch size, and weight decay. The remaining differences are necessitated by the characteristics of the specific training image sets used (natural images versus digits). Please note that we do not directly contrast models trained on CIFAR-10 and SVHN; the controlled comparisons are conducted while holding the SVHN training images constant, and are not confounded by hyperparameter choice.

Manuscript changes:

The networks’ weights and biases were initialized randomly using the uniform He initialization [70]. We trained the models using 250 epochs and a batch size of 256 images. The CIFAR-10 network was trained using stochastic gradient descent (SGD) optimizer starting with a learning rate of 10−3 and momentum of 0.9. The learning rate was halved every 20 epochs. The SVHN/symSVHN/asymSVHN networks were trained using the Adam optimizer. The initial learning rate was set to 10−5 and reduced by half every 50 epochs. The hyper-parameters were determined using the validation data. The models reached around 83% test accuracy (CIFAR-10: 81%, SVHN: 89%, symSVHN: 83%, asymSVHN: 80%). Fig. S4 shows the models’ learning curves.

Point 2.4: 3. L681-685: The general statement made in the paper that ”deeper models lose their advantage as models of cortical representations” is not supported by the cited limited comparison on a single dataset. There are many potential confounds here with respect to prior work, e.g. the recording modality (fMRI vs electrodes), the stimulus set (62 images vs thousands), the models that were tested (9 vs hundreds), etc.

We agree that the recording modality and stimulus set may play a critical role in determining model ranking. Since we generalized the analyses to deeper models, we removed this statement from the paper. While we still believe that shallower networks may prove to be better models of the visual cortex, this empirical question is out of the scope of the current manuscript.

Reviewer 3

This study aimed to explore the computational mechanisms of view invariance, driven by the observation that in some regions of monkey visual cortex, neurons show comparable responses to (1) a given face and (2) to the same face but horizontally flipped. Here they study this known phenomenon using AlexNet and other shallow neural networks, using an index for mirror symmetric viewpoint tuning based on representational similarity analyses. They find that this tuning is enhanced at fully connected- or global pooling layers (layers which combine spatial information), and that the invariance is prominent for horizontal- but not vertical- or rotational transformations. The study shows that mirror tuning can be learned when a given set of images are flipped horizontally and given the same label, but not if they are flipped and given different labels. They also show that networks learn this tuning by focusing on local features, not global configurations.

We are grateful for your thorough reading, reflected by the comprehensive summary of our study and its main findings.

Point 3.1) I found the study to be a mixed read. Some analyses were fascinating: for example, it was satisfying to see the use of well-controlled datasets to increase or decrease the rate of mirror-symmetry tuning. The insertion- and deletion¬ experiments were elegant tests to probe the mechanisms of mirror symmetry, asking if symmetry could arise from (1) global feature configurations (in a holistic sense) vs. (2) local features, with stronger evidence for the latter. These two sets of results were successful and interpretable. They stand in contrast with the first analysis, which relies on observations that do not seem justified. Specifically, Figure 2D shows mirror-symmetry tuning across 11 stages of image processing, from pixels space to fully connected layers. It shows that images from different object categories evoke considerably different tuning index values. The explanation for this result is that some categories, such as ”tools,” have ”bilaterally symmetric structure,” but this is not explicitly measured anywhere. ”Boats” are described as having ”front-back symmetry,” more so than flowers. One imagines flowers being extremely symmetric, but perhaps that depends on the metric. What is the metric? At first I thought it was the mirror-symmetric viewpoint tuning index in the image (pixel) space, but this cannot be, as the index for faces and flowers is negative, cars have no symmetry, and boats are positive. To support these descriptions, one must have an independent variable (for object class symmetry) that can be related to the dependent variable (the mirror-symmetric viewpoint tuning index). If it exists, it is not a part of the Results section. This omission undermines other parts of the Results section: ”some car models have an approximate front-back symmetry...however, a flower typically does not...” ”Some,” ”typically:” how many in the dataset exactly, and how often?

We thank you for your insightful observation. You are correct that we did not refer to pixel-space symmetry; our descriptions relate to the 3D structure of the objects used in the study.

Following this comment, we objectively quantified the symmetry planes of the 3D objects. Unfortunately, we do not have direct access to the proprietary 3D meshes of these objects, only to their renders. Therefore, we devised measures that assess the symmetry of the 3D objects through the symmetry they elicit in the different 2D renders.

This analysis is described in the new supplemental figure S8. We believe that these measurements support the qualitative claims we made in the previous draft.

Point 3.2) The description of CIFAR-10 as having bilaterally symmetric categories - are all these categories equally symmetric? If not, would such variability matter in terms of these results?

When considering their 3D structure, all ten CIFAR10 categories exhibit pronounced left-right symmetry. These categories encompass vertebrate animals (birds, cats, deer, dogs, frogs, horses); They also include man-made vehicles (airplanes, cars, ships, and trucks), which, at least externally, are nearly perfectly symmetric by design. It is important to note that this symmetry pertains to the photographed 3D objects, rather than the images themselves, which could be highly asymmetric. Other axes of symmetry (e.g., back-front) in CIFAR10 cannot be measured without 3D representations of the objects.

Point 3.3) These assessments of object category symmetry values are made before experiments are presented, so they are not interpretations of the results, and it would be circular to write it otherwise.

We have changed the order so that the explanations follow the experimental results. This includes the relevant main text paragraph, as well as the relevant figure—both the order of panels and the phrasing of the figure caption.

Point 3.4) Overall, my bigger concern is that the framing is misleading or at best incomplete. The manuscript successfully showed that if one introduces left-right symmetry to a dataset, the network will develop population-level representations that are also bilaterally symmetric. But the study does not explain that the model’s architecture and random weight distribution are sufficient for symmetry tuning to emerge, without training, just to a much more limited degree. Baek et al. showed in 2021 that viewpoint-invariant face-selective units and mirror-symmetric units emerge in untrained networks (”Face detection in untrained deep neural networks”; this current manuscript cites this paper but does not mention that mirror symmetry is a feature of the 2021 study). This current study also used untrained networks as controls (Fig. 3), and while they were useful in showing that learning boosts symmetry tuning, the results also clearly show that horizontal-reflection invariance is far from zero. So, the simple learning-driven explanation for the mirror-symmetric viewpoint tuning for faces is wrong: while (1) network training and (2) pooling are mechanisms that charge the development of mirror-symmetric tuning, the lottery ticket hypothesis is enough for its emergence. Faces and numbers are simple patterns, so the overparameterization of networks is enough to randomly create units that are tuned to these shapes and to wire many of them together. How learning shapes this process is an interesting direction, especially now that this current study has outlined its importance.

We agree with the reviewer that random initialization may result in units that show mirror-symmetric viewpoint tuning for faces in the absence of training. In the revised manuscript, we quantify the occurrence of such units, first reported by Baek et al, in detail, and discuss the relation between Baek et al., 2021 and our work. In brief, our analysis affirms that units with mirror-symmetric viewpoint tuning for faces appear even in untrained CNNs, although we believe their rate is lower than previously reported. Regardless of the question of the exact proportion of such units, we believe it is unequivocal that at the population level, mirror-symmetric viewpoint tuning to faces (and other objects with a single plane of symmetry) is strongly training-dependent.

First, we refer the reviewer to Figure S2, which directly demonstrates the effect of training on the population-level mirror symmetric viewpoint tuning:

Note the non-mirror-symmetric reflection invariant tuning profile for faces in the untrained network.

Second, the above-zero horizontal reflection-invariance referred by the reviewer (Figure 3) is distinct from mirror- symmetric viewpoint tuning; the latter requires both reflection-invariance and viewpoint tuning. More importantly, it was measured with respect to all of the object categories grouped together; this includes objects with quadrilateral symmetry, which elicit mirror-symmetric viewpoint tuning even in shallow layers and without training. To clarify the confusion that this grouping might have caused, we repeated the measurement of invariance in fc6, separately for each 3D object category:

Disentangling the contributions of different categories to the reflection-invariance measurements, this analysis under-scores the necessity of training for the emergence of mirror-symmetric viewpoint symmetry.

Last, we refer the reviewer to Figure S5, which shows that the symmetry of untrained convolutional filters has a narrow, zero-centered distribution. Indeed, the upper limit of this distribution includes filters with a certain degree of symmetry. This level of symmetry, however, becomes the lower limit of the filters’ symmetry distribution following training.

Therefore, we believe that training induces a shift in the tuning of the unit population that is qualitatively distinct from, and not explained by, random-lottery-related mirror-symmetric viewpoint tuned units. In the revised manuscript, we clarify the distinction between mirror-symmetric viewpoint tuning at the population level and the existence of individual units showing pre-training mirror symmetric viewpoint tuning, as shown by Baek et al.

Manuscript changes: (Discussion section)

Our claim that mirror-symmetric viewpoint tuning is learning-dependent may seem to be in conflict with findings by Baek and colleagues [17]. Their work demonstrated that units with mirror-symmetric viewpoint tuning profile can emerge in randomly initialized networks. Reproducing Baek and colleagues’ analysis, we confirmed that such units occur in untrained networks (Fig. S15). However, we also identified that the original criterion for mirror-symmetric viewpoint tuning employed in [17] was satisfied by many units with asymmetric tuning profiles (Figs. S14 and S15). Once we applied a stricter criterion, we observed a more than twofold increase in mirror-symmetric units in the first fully connected layer of a trained network compared to untrained networks of the same architecture (Fig. S16). This finding highlights the critical role of training in the emergence of mirror-symmetric viewpoint tuning in neural networks also at the level of individual units.

Point 3.5) Finally, it would help to cite other previous demonstrations of equivariance and mirror symmetry in neural networks. Chris Olah, Nick Cammarata, Chelsea Voss, Ludwig Schubert, and Gabriel Goh of OpenAI wrote of this phenomenon in 2020 (Distill journal).

We added a reference to the study by Olah and colleagues (2020).

Manuscript changes: (Discussion section)

(see Olah and colleagues (2020) [60] for an exploration of emergent equivariance using activation maximiza- tion).

Point 3.6) Some other observations that might help:

I am enthusiastic about the experiments using different datasets to increase or decrease the rate of mirror-symmetry tuning (sets including CIFAR10, SVHN, symSVHN, asymSVHN); it is worth noting, however, that the lack of a ground truth metric for category symmetry is a problem here too. In the asymSVHN dataset, images are flipped and given different labels. If some categories are naturally symmetric after horizontal flips, such as images containing ”0” or ”8”, then changing the label is likely to disturb training. This would explain why the training loss is larger for this condition (Figure S4D).

We now acknowledge that the inclusion of digits 0 and 8 reduces the accuracy of asymSVHN:

Manuscript changes: (Figure S4 caption)

Note that the accuracy of asymSVHN might be negatively affected by the inclusion of relatively symmetric categories such as 0 and 8.

Our rationale for retaining these digits in the dataset was to manipulate the symmetry of the learned categories (compared to symSVHN) while keeping the images themselves constant.

Regarding ground-truth symmetry of these dataset: For CIFAR-10, the relevant measure of symmetry pertains to the 3D structure of the photographed objects, which we believe is unequivocally symmetric (see Point 3.2). Note that 2D, pixel-space image symmetry is not directly indicative of symmetry in 3D.

For SVHN, which consists of two-dimensional characters, the pixel-space symmetry of the images indeed reflects the objects’ symmetry. However, since we are worried that some readers might confuse our claims that relate to the symmetry of objects with claims (we did not make) about symmetry of 2D images, we prefer to avoid reporting measurements of image-space symmetry. We believe that our interpretation of the experiments with SVHN/symSVHN/asymSVHN holds even in the absence of such measurements.

For your reference, we include here a quantification of image-space horizontal symmetry for each category of CIFAR-10 and SVHN:

Point 3.7) It is puzzling why greyscale 3D rendered images are used. By using greyscale 3D render (at least as shown in the figures) the study proceeds as if the units are invariant under color transformations. Unfortunately, this is not true and using greyscale images impact the activations of different layers of Alexnet in a way that is not fully defined. Moreover, many units in shallow networks focus on color and exactly these units could be invariant to other transformation like the mirror symmetry, but grey scaling the images makes them inactive.

We use grayscale 3D rendered images to align with the setting in other studies investigating mirror- symmetric viewpoint tuning, including Freiwald et al. (2010), Leibo et al. (2017), and Yildirim et al. (2020). The choice of using grayscale images in these studies is motivated by the need to dissociate face-processing from lower-level, hue-specific responses.

Author Response

Reviewer #1 (Public Review):

In this manuscript, the authors perform a very thorough, extensive characterization of the impact of an iron-rich diet on multiple phenotypes in a wide range of inbred mouse strains. While a work of this type does not offer mechanistic insights, the value of the study lies not only in its immediate results but also in what it can offer to future researchers as they explore the genetic basis of iron levels and other related phenotypes in rodent studies. The creation of a web resource and the offer from the authors to share all available samples is particularly laudable, and helps to increase the accessibility of the work to other scientists. There is one shortcoming to the work however. To induce iron overload in mice in the main study in this work, mice were placed on an iron-rich diet that differed in its composition from the baseline diet in more than just iron. This could influence some of the phenotypes observed in this study.

We thank the reviewer for their comments. We hope that this work can provide insight and/or support for a wide variety of future studies. Regarding the diets, yes, in our initial pilot study with 6 strains, the baseline diet was inadvertently not isocaloric with the high iron diet, and it also used a different source of cellulose and contained individual amino acids in ratios found in casein, instead of casein, which was used as the protein source for the high iron diet. The baseline metal composition however was the same. We included data from the pilot study in this manuscript because it provided some important early insight, but made sure to note this caveat since it could potentially affect some results. We added some additional text to the Methods section to help clarify this further. The other subsequently performed studies in this paper were not affected, for example the Control study performed in C57BL/6J has a baseline diet that matches the high iron diet except for iron. For our HMDP genetic study with 114 strains, we did not have a baseline group, so all mice were on the same high iron diet.

Reviewer #2 (Public Review):

Here, the authors tried to identify the genes and biological pathways underlying iron overload and its associated pathologies in mice. Several wet lab experiments and measurements alongside many bioinformatic analyses like GWAS, RNA-seq data analysis (DEG), eQTL analysis, TWAS, and gene-set enrichment analysis have been performed. The study design is good enough and the author tried to validate the results. The data have been submitted (Accession #: GSE230674) but are not public yet.

Thank you very much for your detailed and thoughtful review and for helping us to improve our manuscript.

1) The main issue of this manuscript is its length. It's too long, especially the result section. It's hard for readers to follow the paper. Moreover, you added results about other minerals, mostly copper, which seems too much (considering the fact that this study is about iron). The text doesn't have the required Integrity and focus. You should decide where you want to put the focus of this manuscript and I strongly recommend shortening the manuscript, try to be short and sweet as much as you can.

Thank you for this helpful suggestion. We have moved or removed excess discussion from the Results section. We moved the specific GWAS results for copper and related red cell traits to the Supplementary text file “Supplementary File 24” so that only iron and triglyceride GWAS results are described in the main text. We kept in the discussion about the copper findings in the Discussion section, since we believe the deficiency is an important phenotype induced by the high iron diet that may impact other studies of dietary iron overload. We also believe that the copper and anemia GWAS loci may be of interest to some readers. We considered putting the copper and anemia findings in a separate manuscript, but ultimately decided to include it here, although we do agree it makes the manuscript longer.

2) Also, the "Methods" section is long, some parts are over-detailed (mostly wet lab procedures) and some parts are not detailed enough. It seems the "Statistical analyses" part doesn't have extra information. I recommend removing the first paragraph and moving some of the information from the second paragraph to the right place in the Method section.

We reorganized the first part of the statistical analyses section for clarity, and as mentioned further below, added in more detail regarding the GWAS significance thresholds:

“Analyses were performed using GraphPad Prism (GraphPad Software, La Jolla, CA) and in R. P < 0.05 was considered significant for these tests and for bicor analyses. All reported P values are based on a two-sided hypothesis. The initial number of mice per group in the pilot (N = 6 per group) and Control studies (N = 8 per group) were determined based on previous studies where similar phenotypes were measured. For the HMDP study, permutation and simulation studies were previously used to test the statistical power of the HMDP using parameters including the variance explained by SNPs, genetic background, random errors, and the number of repeated measurements per strain (Bennett, Farber et al. 2010). Appropriate sample sizes to achieve adequate statistical power were determined based on previous analyses. Differences in sample sizes among the HMDP strains were due to differences in strain availability as determined by breeding success and losses. For GWAS, thresholds for significant (P < 4.1e-6; -log10P > 5.387) loci were defined using permutation as previously described (Bennett, Farber et al. 2010). The suggestive locus threshold (P < 4.1e-5; -log10P > 4.387) was based on reducing the significance threshold by one log unit. The cis eQTL GWAS threshold (P < 1e-4) was based on a calculated 1% FDR threshold of 1.73e-3, adjusted to 1e-4 to be slightly more conservative. The trans-eQTL threshold (P < 1e-6) was based on the 4.1e-6 threshold, adjusted to 1e-6 to be more conservative as well.”

We tried moving the missing values notes in the second paragraph to the various method sections in the paper they apply to, but this led to much repetition and was in some cases not clear, so we decided to keep this information together in the statistical analyses section.

3) Some part of your discussion section, is retelling the results. Please discuss your results and compare them with previous findings.

We have revised the discussion to remove several parts that mostly just summarized the results and agree this improves the text. As mentioned above, we moved some discussion that was in the Results section to the Discussion section as well.

4) Add detail about your GWAS model. As you had repeated samples from each strain, it's good to mention how you considered this. Also, show how you determined the significance threshold.

Thank you for this suggestion. The GWAS software we used (FaST-LMM) derives a kinship matrix from the genotypes of the individuals considered in the analysis; this kinship matrix is used to correct for population structure including multiple individuals per strain.

The trait GWAS significance threshold was determined using permutation analysis (Bennett, Farber et al. 2010). The suggestive GWAS threshold was based on reducing the significance threshold by one log unit. The cis eQTL GWAS threshold was based on a calculated 1% FDR threshold of 1.73e-3, adjusted to 1e-4 to be slightly more conservative. The trans-eQTL threshold was based on the 4.1e-6 threshold, adjusted to 1e-6 to be more conservative as well.

To improve the text, we added to the Methods section under the “Genome-wide association analysis and heritability estimation” header the following:

“Traits were quantile transformed to normalize the distribution and then GWAS was performed using the FaST-LMM program (Lippert, Listgarten et al. 2011), which corrects for population structure (including multiple samples per strain) by using a kinship matrix derived from the genotypes to be analyzed.”

We also revised the GWAS threshold text to include more detail:

“Analyses were performed using GraphPad Prism (GraphPad Software, La Jolla, CA) and in R. P < 0.05 was considered significant for these tests and for bicor analyses. All reported P values are based on a two-sided hypothesis. For GWAS, thresholds for significant (P < 4.1e-6; -log10P > 5.387) loci were defined using permutation as previously described (Bennett, Farber et al. 2010). The suggestive locus threshold (P < 4.1e-5; -log10P > 4.387) was based on reducing the significance threshold by one log unit. The cis eQTL GWAS threshold (P < 1e-4) was based on a calculated 1% FDR threshold of 1.73e-3, adjusted to 1e-4 to be slightly more conservative. The trans-eQTL threshold (P < 1e-6) was based on the 4.1e-6 threshold, adjusted to 1e-6 to be more conservative as well. “

5) The abstract could be better. It also doesn't have a conclusion.

We revised the abstract and added in a conclusion:

“Tissue iron overload is a frequent pathologic finding in multiple disease states including non-alcoholic fatty liver disease (NAFLD), neurodegenerative disorders, cardiomyopathy, diabetes, and some forms of cancer. The role of iron, as a cause or consequence of disease progression and observed phenotypic manifestations, remains controversial. In addition, the impact of genetic variation on iron overload related phenotypes is unclear, and the identification of genetic modifiers is incomplete. Here, we used the Hybrid Mouse Diversity Panel (HMDP), consisting of over 100 genetically distinct mouse strains optimized for genome-wide association studies (GWAS) and systems genetics, to characterize the genetic architecture of dietary iron overload and pathology. Dietary iron overload was induced by feeding male mice (114 strains, 6-7 mice per strain on average) a high iron diet for six weeks, and then tissues were collected at 10-11 weeks of age. Liver metal levels and gene expression were measured by ICP-MS/ICP-AES and RNASeq, and lipids were measured by colorimetric assays. FaST-LMM was used for genetic mapping, and Metascape, WGCNA, and Mergeomics were used for pathway, module, and key driver bioinformatics analyses. Across the HMDP, we identified many traits that exhibited high inter-strain variability on the high iron diet, and we found a substantial contribution of genetics to many traits. Mice on the high iron diet accumulated iron in the liver, with a 6.5 fold difference across strain means. The iron loaded diet also led to a spectrum of copper deficiency and anemia, with liver copper levels highly positively correlated with red blood cell count, hemoglobin, and hematocrit. Hepatic steatosis of various severity was also observed histologically, with 52.5 fold variation in triglyceride levels across the strains. Most clinical traits examined had at least one significant GWAS locus, and notably, liver triglyceride and iron mapped most significantly to an overlapping locus on chromosome 7 that has not been previously associated with either trait. By genetically mapping liver mRNA expression, we identified cis- and trans-eQTL for thousands of genes, and we integrated this with trait correlation data to identify candidate causal genes at many trait loci. Using network modeling, significant key drivers for both iron and triglyceride accumulation were found to be involved in cholesterol biosynthesis and oxidative stress management. To make the full data set accessible and useable by others, we have made our data and analyses available on a resource website. Overall, our study confirms and expands upon the contribution of mouse genetic background to dietary iron overload and associated pathology. The numerous GWAS loci, candidate genes, and biological pathways identified here provide a rich public resource to drive further investigation.”

6) Page 8, lines 4-7: Please remove these lines or move them to the Method section. The last paragraph of the introduction should clearly explain the goal of the study.

We removed these lines and revised this paragraph for clarity:

In order to gain further insight into genetic contributors to iron overload and associated pathology, we measured clinical traits and hepatic mRNA expression in 114 mouse strains fed a high iron diet. The mice are from a genetically diverse cohort known as the Hybrid Mouse Diversity Panel (HMDP), a panel optimized for systems genetics studies that has previously been used to examine numerous complex traits, including obesity, diabetes, atherosclerosis, heart failure, carbon tetrachloride induced liver fibrosis, and fatty liver disease (Lusis, Seldin et al. 2016; Seldin, Yang et al. 2019; Tuominen, Fuqua et al. 2021; Cao, Wang et al. 2022).

7) Page 68, line 13: Explain the abbreviation (RINe) before use. Also, most probably it is RIN (RNA Integrity Number).

Thank you for pointing this out. We updated the methods text as follows: “All samples had RNA integrity number equivalents (RINe) values greater than 8 as measured on an Agilent 2200 TapeStation (Agilent, Santa Clara, CA).” We also added RINe to the abbreviations section.

8) The heritability estimates seem high and the 1% difference between broad- and narrow-sense heritability means there is almost no dominant and epistatic genetic variance between alleles affecting the studied trait (which is hard to accept). I recommend considering a within-group (strain) variance (common environmental effect) component in the model to absorb this source of variation in this component, so the genetic variance and consequently the heritability estimates would be more accurate. You also can consider this source of variance in your GWAS model.

Thank you for bringing up these points. While we try to minimize environmental effects by keeping these mice and samples in as similar environmental and experimental conditions as feasible, some will remain. Thus, in our analyses, we try to factor in remaining environmental variation by using data from multiple mice per strain. The programs we used for GWAS and heritability calculations take into account within-group (strain) variance. We added the following sentence to the Methods section just after mention of the programs used to calculate heritability:

“Both of the software packages used for heritability estimation account for environmental variance within strains.”

We agree that the broad-sense and narrow-sense estimates are close to each other for many traits and that this suggests low levels of dominance and epistasis. A low level of non-additive genetic variance is not uncommon and theoretically predicted for complex traits, as has been reported previously and discussed in the references below:

Hill WG, Goddard ME, Visscher PM. Data and theory point to mainly additive genetic variance for complex traits. PLoS Genet. 2008 Feb 29;4(2):e1000008. doi: 10.1371/journal.pgen.1000008. PMID: 18454194

Hivert V, Sidorenko J, Rohart F, Goddard ME, Yang J, Wray NR, Yengo L, Visscher PM. Estimation of non-additive genetic variance in human complex traits from a large sample of unrelated individuals. Am J Hum Genet. 2021 May 6;108(5):786-798. doi: 10.1016/j.ajhg.2021.02.014. Epub 2021 Apr 2. Erratum in: Am J Hum Genet. 2021 May 6;108(5):962. PMID: 33811805

It has also been argued that many human GWAS studies, as well as studies using populations of mice designed for complex trait analyses, including the HMDP population, inherently lack the statistical power to detect epistasis:

Buchner DA, Nadeau JH. Contrasting genetic architectures in different mouse reference populations used for studying complex traits. Genome Res. 2015 Jun;25(6):775-91. doi: 10.1101/gr.187450.114. Epub 2015 May 7. PMID: 25953951

Taking all this together we would argue that it is not surprising to see the little difference between the narrow and broad heritability estimates for many traits in our study. To provide more context to the reader regarding how to interpret our heritability findings, we added the following text to the discussion section, under limitations:

“Finally, in our study with the HMDP population, estimated broad and narrow sense heritabilities were similar for many traits, suggesting modest non-additive contributions (e.g dominance and epistasis) to the variance in these traits. While such results are common and theoretically predicted for complex traits (Hill, Goddard et al. 2008; Hivert, Sidorenko et al. 2021), our study population may also not be optimal for detection of these effects (Buchner and Nadeau 2015).”

Author Response

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

Reviewer #1 (Public Review):

Summary:

This study by Lee et al. is a direct follow-up on their previous study that described an evoluBonary conservancy among placental mammals of two moBfs (a transmembrane moBf and a juxtamembrane palmitoylaBon site) in CD4, an anBgen co-receptor, and showed their relevance for T-cell anBgen signaling. In this study, they describe the contribuBon of these two moBfs to the CD4-mediated anBgen signaling in the absence of CD4-LCK binding. Their approach was the comparison of anBgen-induced proximal TCR signaling and distal IL-2 producBon in 58-/- T-cell hybridoma expressing exogenous truncated version of CD4 (without the interacBon with LCK), called T1 with T1 version with the mutaBons in either or both of the conserved moBfs. They show that the T1 CD4 can support signaling to the extend similar to WT CD4, but the mutaBon of the conserved moBfs substanBally reduced the signaling. The authors conclude that the role of these moBfs is independent of the LCK-binding.

Strengths:

The authors convincingly show that T1 CD4, lacking the interacBon with LCK supports the TCR signaling and also that the two studied moBfs have a significant contribuBon to it.

Weaknesses:

The study has several weaknesses.

(1) The whole study is based on a single experimental system, geneBcally modified 58-/- hybridoma. It is unclear at this moment, how the molecular moBfs studied here contribute to the signaling in a real T cell. The evoluBonary conservancy suggests that these moBfs are important for T cell biology. However, the LCK-binding moBf is conserved as well (perhaps even more) and it plays a very minor role in their model. Without verifying their results in primary cells, the quanBtaBve, but even qualitaBve, importance of these moBfs for T-cell signaling and biology is unclear. Although the authors discuss this issue in the Discussion, it should be noted in all important parts of the manuscript, where conclusions are made (abstract, end of introducBon, perhaps also in the Btle) that the results are coming from the hybridoma cells.

We appreciate the Reviewer’s thoughWul comments and suggesBon. We now state in the abstract and introducBon that wet-lab experiments were performed with T cell hybridomas. We have also beXer highlighted work from Killeen and LiXman (PMID: 8355789) wherein they showed that C-terminally truncated CD4, which lacked the moBfs that mediate CD4-Lck interacBons, can drive CD4+ T cell development, proliferaBon, and T-helper funcBon because we now provide mechanisBc data to help explain those in vivo results. Also, as noted by the reviewer, we discuss how the sum of our data provides jusBficaBon for the investment in and use of mouse models to interrogate how the funcBonally important residues/moBfs idenBfied and studied here influence T cell biology.

We will take the opportunity to reiterate here that, while the study is based on a well characterized, albeit single, wet-lab experimental system, the whole study is based on two lines of invesBgaBon. The other approach was a systems biology computaBonal approach that analyzes data from real-world experiments in a variety of jawed vertebrate species over evoluBon. Specifically, we used a computaBonal reconstrucBon of the evoluBonary history of CD4 by performing mulBple analyses of CD4 from 99 jawed vertebrates spanning ~435 million years of evoluBon. This analysis allowed us to idenBfy residues, and networks of evoluBonarily coupled residues, that are predicted to be funcBonally important in vivo. Like other systems biology approaches, this allowed us to look at the larger picture by evaluaBng data points that have emerged from constant tesBng and adjustments of CD4 funcBon in vivo through selecBon on an evoluBonary Bmescale in more jawed vertebrate species, and under more real-world condiBons, than can be tested in the laboratory. Our structure-funcBon analysis provided a second, wet-lab reducBonist experimental system to cross-validate that the residues idenBfied by our evoluBonary analysis are funcBonally significant. This experimental validaBon is criBcal and elevates the relevance of our studies above ad hoc observaBons. Our work also provides mechanisBc insights for why the residues studied here are funcBonally significant (i.e., key determinants of pMHCII-specific signaling iniBaBon). In short, using both systems allowed us to cross-validate the funcBonal significance of the residues within the GGXXG and (C/F)CV+C moBfs studied here by two independent methods.

(2) Many of the experiments lack the negaBve control. I believe that two types of negaBve controls should be included in all experiments. First, hybridoma cells without CD4 (or with CD4 mutant unable to bind MHCII). Second, no pepBde control, i.e., acBvaBon of the hybridoma cells with the APC not loaded with the cognate pepBde. These controls are required to disBnguish the basal levels of phoshorylaBon and CD4-independent anBgen-induced phosphorylaBon to quanBfy, what is the contribuBon of the parBcular moBfs to the CD4-mediated support. Although these controls are included in some of the experiments, they are missing in other ones. The binding mutant appears in some FC results as a horizontal bar (without any error bar/variability), showing that CD4 does not give a huge advantage in these readouts. Why don't the authors show no pepBde controls here as well? Why the primary FC data (histograms) are not shown? Why neither of these two controls is shown for the % of responders plots? Although the IL-2 producBon is a very robust and convincing readout, the phosphoflow is much less sensiBve. It seems that the signaling is elevated only marginally. Without the menBoned controls and showing the raw data, the precise interpretaBon is not possible.

These comments, and those in point #3, concern our flow cytometry-based analysis of early intracellular signaling events where we asked: how do the moBfs under invesBgaBon impact phosphorylaBon of CD3z, ZAP-70, and PLCg1 in response to agonist pMHCII? Thank you for poinBng out areas of confusion regarding these analyses. We will try to clarify here and have worked to clarify the text.

Our approach was to mutate consBtuent residues within the moBfs that our evoluBonary analysis predicted to be funcBonally significant, compare the performance of the mutants to that of controls bearing WT moBfs, and then infer the funcBon of the moBfs based on the differenBal phenotype of the mutants relaBve to their controls. In most cases, the C-terminally truncated CD4-T1 mutant served as the appropriate CD4 control backbone against which to evaluate the phenotypes of the GGXXG and (C/F)CV+C moBf mutants. This is a convenBonal structure-funcBon strategy.

All experiments included APCs expressing null pMHCII (Hb:I-Ek) as negaBve controls. These were a necessary component of the data analysis, explained further below, which involved background subtracBon of the signal from control or mutant T cell hybridomas bound to these negaBve control APCs from those bound to the agonist pMHCII (MCC:I-Ek). Doing so allowed us to establish a true signal over background for calculaBng percent responders and signaling intensity. These negaBve controls served the same purpose of APCs expressing I-Ek not loaded with cognate pepBde requested by the reviewer. It is important to note that we previously published that TCR-CD3-pMHCII interacBons reciprocally increase CD4-pMHCII dwell Bme, and vice versa, such that dwell Bmes of the 5c.c7 TCR and CD4 to the null Hb:I-Ek are both basal in this system relaBve to antagonist, weak agonist, and agonist pMHCII (PMID 29386113). A recent study using different techniques also concluded that TCR-CD3 and CD4 cooperaBvely enhance signaling to pMHCII (PMID 36396644). The use of the null pMHCII, Hb:I-Ek, in each experiment thus serves as a well-characterized negaBve control for both TCR and CD4 engagement in this experimental system with regards to assembly of the TCR-CD3 and CD4 around pMHCII to drive signaling. In our view, it is the most important negaBve control for interpreBng our results, and it is present in each experiment. In Fig 1B and related supplemental figures we compare the Cterminally truncated CD4-T1 mutant to the full-length WT CD4 to evaluate the contribuBons of the intracellular domains to early signaling events. We found no significant differences for pCD3z, pZAP-70, and pPLCg1 levels demonstraBng that, in our system, CD4 WT and T1 are staBsBcally indisBnguishable.

In Fig 1C we asked: what is the contribuBon of CD4-pMHCII interacBons made by CD4 T1, which lacks the intracellular domain, using our CD4 T1Dbind mutant. Fig 2C and Table 3 show that pCD3z levels for T1Dbind were ~54% of T1, meaning that CD4 binding to pMHCII roughly doubles pCD3z levels (even without the intracellular domain). We also showed that the percent of responders were not different between the CD4 T1 and T1Dbind mutant in Fig 2C. The impact on ZAP-70 and PLCg1 are shown in Figure 2—figure supplement 4. These differences, including the magnitude of the decrease, were observed reproducibly (p<0.001) in three independently generated sets of lines. We believe that this analysis saBsfies the request by the reviewer for an analysis of the contribuBons of CD4 binding to pMHCII. We did not include this as a negaBve control in experiments evaluaBng the contribuBons of the GGXXG and (C/F)CV+C moBfs to CD4 T1 signaling because the quesBon being asked in those experiments was how do the moBfs impact signaling in the absence of the intracellular domain (i.e., within the CD4 T1 backbone, making CD4 T1 the proper comparator for the quesBon we were asking). We showed the average normalized intensity for the T1Dbind mutant, relaBve to T1, for this lower bound of signaling mediated by TCR-CD3-only as a doXed line in those figures to provide a reference point for the readers to evaluate and put into perspecBve how the mutants we generated impacted the overall contribuBon of CD4 to these early signaling events. The T1Dbind mutants were not always measured in the same experiment at the same Bme with other mutants, because the cell lines used were not always made at the same Bme, so we did not think it appropriate to graph the results together.

We do not know how to interpret the comment “Although the IL-2 producBon is a very robust and convincing readout, the phosphoflow is much less sensiBve. It seems that the signaling is elevated only marginally.” We will offer our perspecBve that we do not know how to equate the sensiBvity of the phos-flow to the IL-2. Because the IL-2 is a signaling output, it results from signaling amplificaBon from the membrane to the nucleus. If CD3z phosphorylaBon is the iniBaBng event for a signaling cascade that leads to IL-2 gene transcripBon and transducBon, as is widely believed, our data strongly suggests that the ~2-fold difference in pCD3z levels between CD4 T1 and T1Dbind (Fig 2C/Table 3 data) contributes to the difference between no IL-2 output for T1Dbind and IL-2 output by T1 in this experimental system. Because CD4 WT and T1 have significantly different levels of IL-2 output, but show no significant differences in pCD3z, pZAP-70, or pPLCg1 levels, there are likely to be other differences we did not measure via other pathways that intersect at the nucleus. At many levels, biology works on gradients such that small differences can Bp a system in one direcBon or another. The kineBc discriminaBon model (PMID 8643643), which is thought to be a reasonable descripBon of the relaBonship between pMHC engagement and signaling outcomes, suggests that very small differences in molecular interacBons at the earliest stages of a response can lead to big differences in signaling outcome. We therefore have no basis at this juncture to think that ~2-fold differences in pCD3z levels could not account for bigger differences in signaling output such as IL-2.

(3) The processing of the data is not clear. Some of the figures seem to be overprocessed. For instance, I am not sure what "Normalized % responders of pCD3zeta" means (e.g., Fig. 1C and elsewhere)? Why do not the authors show the actual % of pCD3zeta+ cells including the gaBng strategy? Why do the authors subtract the two histograms in Fig. 2- Fig.S3? It is very unusual.

We did develop and implement a novel strategy for measuring the impact of our mutaBons on CD3z, ZAP-70, and PLCg1 phosphorylaBon. This was explained in more detail in our prior study. The instrucBons to authors indicated that we should not repeat methods in the current manuscript. However, we will go through the approach here, and address why we did not show primary FC histograms for all experiments from above. First, we think that a brief explanaBon as to what moBvated us to develop our approach will add to a beXer understanding:

(1) For experimental and staBsBcal rigor, our goal was to perform both experimental and biological replicates by measuring and comparing the average of at least three independently generated sets of paired WT/T1 control Vs. mutant cells lines generated at different Bmes to determine the staBsBcal significance of the difference, if any, between averages of the control and mutant lines.

(2) Our quesBons necessitated that we measure signals generated naturally by the cooperaBve engagement of cognate pMHCII by TCR-CD3 and CD4 on APCs, rather than through aCD3/aCD4 crosslinking.

(3) We chose to use flow cytometry rather than bulk cell analysis by Western Bloung to analyze signaling occurring in cells that were engaged to the agonist APC in order to avoid diluBon of that signal by cells that are not engaged to APCs and not signaling. 4. For each experiment, we wanted to subtract background signals from cells bound to APCs expressing a null pMHCII (Hb:I-Ek) from signals generated by cells bound to APCs expressing agonist pMHCII (MCC:I-Ek). Doing so allowed us to idenBfy cells that are signaling (responders) to agonist over null pMHCII. The goal here was to quanBtate the level of signaling in an objecBve manner with a method that can be applied to all samples uniformly rather than seung a flow cytometry gate on posiBve cells (e.g. pCD3z) because gaBng is subjecBve and can vary from experiment to experiment. To put that another way, as detailed below, we used our subtracBon method to idenBfy signaling responders rather than seung a signaling gate on the posiBve populaBon.

Regarding gaBng schemes, controls, and data processing:

Figure 2—figure supplement 3 of the current study and Figure 6—figure supplement 1 of our prior study are designed to walk the reader through our experimental design, gaBng, data processing and thinking. Here we will provide a detailed explanaBon to complement the figure legend as well as the methods provided in our prior manuscript (see pt #4 below).

We will refer to Figure 2—figure supplement 3 here:

Panel A. The dot plots show our approach to idenBfying 5c.c7+ CD4+ 58a-b- T cell hybridomas (yaxis, GFP posiBve) coupled to M12 cells (x-axis, TagIt Violet) expressing the null pMHCII Hb:I-Ek (lev) or agonist pMHCII MCC:I-Ek (right). The gaBng shows the frequency of GFP+ T cell hybridomas that are bound to TagIt violet posiBve APCs (i.e., cell couples). The histogram on the right then shows the staining intensity for pCD3z on the x-axis for the 10,000 coupled events collected wherein the APCs express the null pMHCII (filled cyan) or the agonist pMHCII (black line).

Panel B. The data presented here is the same as in Panel A, but for CD4 T1 cells.

Panel C. The data presented here walks through how we idenBfy 5c.c7+ CD4+ 58a-b- T cell hybridomas responding (i.e., signaling) to agonist pMHCII, as well as the mean signaling intensity of the responding populaBon, in a gaBng-independent manner aver background subtracBon. For the lev graph, we exported the data for the histograms shown in Panel A from FlowJo 10 sovware and ploXed them here using Prism 9 as smoothed lines (500 nearest neighbors). The cyan line is therefore a replicate of the flow cytometry histogram shown in Panel A for pCD3z intensity from 5c.c7+ CD4+ 58a-b- T cell hybridomas coupled to M12 cells expressing the null pMHCII (Hb:I-Ek), while the black histogram is a replicate of the pCD3z intensity for 5c.c7+ CD4+ 58a-b- T cell hybridomas coupled to M12 cells expressing the agonist pMHCII (MCC:I-Ek). Next, to idenBfy the responding populaBon in a gaBng-independent manner, we used Excel to subtract the pCD3z intensity for the null pMHCII (cyan) negaBve control populaBon on a bin-by-bin bases from the pCD3z intensity for the agonist pMHCII (black) responding populaBon. We then transferred the background subtracted values to Prism 9 for smoothing and ploung (grey line: MCC:I-Ek minus Hb:I-Ek). The middle graph shows the same data processing for the data from Panel B for the CD4 T1 cells. Please note that the background subtracted grey line has negaBve values and posiBve values. The negaBve values represent intensity bins where signaling in response to agonist pMHCII leads to fewer cells per bin than in the null pMHCII populaBon that is not signaling, while the posiBve values represent bins of intensity where signaling cells outnumber non-signaling cells. The right graph in this panel shows the populaBons aver background subtracBon for intensity bins that had more cells with pCD3z signal in the agonist pMHCII populaBon than the null pMHCII populaBon (grey = WT full length CD4 and blue = T1). In short, the right graph shows idenBficaBon of those cells that are signaling in response to agonist pMHCII. This approach miBgated the need for subjecBve gaBng in FlowJo to idenBfy signaling cells (i.e., pCD3z posiBve) and allowed for background subtracBon which could not be done in FlowJo. We used this approach for all analyses of pCD3z, pZAP-70, and pPLCg1 in this study.

The number of cells in these background-subtracted populaBons were divided by 10,000 (the number of events collected and analyzed) to calculate the percent of responding 5c.c7+ CD4+ 58a-b- T cell hybridomas, while the mean fluorescent intensity for the cells within these populaBon represent the signaling intensity.

Panel D. The graph on the lev shows the mean fluorescence intensity (MFI) ± SEM for the posiBve signaling populaBon from the right graph of panel C. We see in this example comparing a WT and T1 cell line, generated at the same Bme from the same parental 58a-b- T cell hybridoma populaBon, that the T1 MFI is significantly greater than the WT. These intensity values represent one of the paired intensity values used in the main Fig 2B (Lev graph), where we show the paired MFI analysis of responding populaBons from 5 independently generated sets of cell lines. Please note that these single MFI values are directly derived from the flow cytometry histograms aver background subtracBon. Figure 2B, and similar figures, therefore equate to a disBllaBon of all of the histograms for the populaBons tested in a manner that we consider easier to digest than either overlaying all histograms or showing mulBple panels individually. It also conserves more space. This is why we only showed representaBve flow cytometry histograms, rather than all histograms.

The graph on the right shows the % responders for the posiBve signaling populaBon from the right graph of panel C. Specifically, the total number of cells that were determined to be signaling in response to agonist pMHCII was divided by 10,000 (the number of coupled cells collected by flow cytometry) to determine the percent responders. These values represent one of five sets of values used to determine the average normalized percent responders (all normalized to WT). There was no significant difference between these two populaBons in terms of percent responders.

Regarding graphing normalized values for the mean MFI for signaling intensity or the percent responders: in our first manuscript, we presented the individual MFI intensity values for matched pairs of cells as well as the actual percent responders per group. The feedback we received from colleagues on this presentaBon was that it was confusing, distracBng, and otherwise hard to digest. It was suggested to us by mulBple individuals that the normalized values would be preferable because it is easier and faster to understand. Upon reflecBon, we agreed with this feedback because the normalized presentaBon with staBsBcs allows for the two key relevant quesBons to be quickly evaluated: 1. Are the mutants different than the control? 2. By how much? We have lev the raw intensity values and well as the normalized intensity values in the version of record. Given the Reviewer’s comments, we have now graphed the average % responders instead of normalized values in the figures, and lev the normalized values in Table 3.

(4) The manuscript lacks Materials and Methods. It only refers to the previous paper, which is very unusual. Although most of the methods are the same, they sBll should be menBoned here. Moreover, some of the mutants presented here were not generated in the previous study, as far as I understand. Perhaps the authors plan to include Materials and Methods during the revision...

Because we submiXed this as a Research Advances arBcle we followed the journal instrucBons to reference the Materials and Methods in our prior publicaBon, upon which this work builds, as the methods used are the same. They are detailed in that study. We have now included a copy of the Materials and Methods for the eLife staff to determine how best to link with this manuscript. We have also included the gene sequences for the novel constructs used in this study. Thank you for poinBng out the omission.

(5) Membrane rafts are a very controversial topic. I recommend the authors stick to the more consensual term "detergent resistant microdomains" in all cases/occurances.

We agree this is a controversial topic with a variety of viewpoints. Because we are not experts in the field of membrane composition, we turned to the literature to inform our view of how best to refer to these membrane subdomains. In our reading, we found a 2006 meeting report from a Keystone symposium on lipid rafts and cell function authored by Linda Pike (PMID 16645198). At this meeting, a central focus was reaching a consensus on how best to refer to these domains. The consensus term agreed upon by this group was “membrane rafts”. Specifically, we will quote from this report published in the Journal of Lipid Research, ‘Together, the discussions permitted the generation of a definition for “lipid rafts” in an ad hoc session on the final day of the meeting. All participants were invited to contribute to this effort, and the work product reflects the consensus of this broad-based group…… First and foremost, the term “lipid raft” was discarded in favor of the term “membrane raft.”’ We chose to use the term “membrane raft” based on this consensus opinion.

(6) Last, but not least, the mechanistic explanation (beyond the independence of LCK binding) of the role of these motifs is very unclear at the moment.

We agree with this comment. One goal in making these results, and those in our prior study, available to the field at large is to provide evidence in support of our view that the dominant paradigm that is thought to explain the earliest events in T cell signaling needs re-evaluating. How T cell signaling is initiated in response to pMHCII is clearly more complex than is currently thought. However, out data is inconsistent with the dominant paradigm in which CD4 recruits Lck to TCR-CD3 to phosphorylate ITAMs to initiate signaling.

Reviewer #2 (Public Review):

Summary:

The paper by Kuhn and colleagues follows upon a 2022 eLife paper in which they identified residues in CD4 constrained by evolutionary purifying selection in placental mammals and then performed functional analyses of these conserved sequences. They showed that sequences distinct from the CXC "clamp" involved in recruitment of Lck have critical roles in TCR signaling, and these include a glycine-rich motif in the transmembrane (TM) domain and the cyscontaining juxtamembrane (JM) motif that undergoes palmitoylation, both of which promote TCR signaling, and a cytoplasmic domain helical motif, also involved in Lck binding, that constrains signaling. Mutations in the transmembrane and juxtamembrane sequences led to reduced proximal signaling and IL-2 production in a hybridoma's response to antigen presentation, despite retention of abundant CD4 association with Lck in the detergent-soluble membrane fraction, presumably mislocalized outside of lipid rafts and distal to the TCR. A major conclusion of that study was that CD4 sequences required for Lck association, including the CXC "clasp" motif, are not as consequential for CD4 co-receptor function in TCR signaling as the conserved TM and JM motifs. However, the experiments did not determine whether the functions of the TM and JM motifs are dependent on the Lck-binding properties of CD4 - the mutations in those motifs could result in free Lck redistributing to associate with CD4 in signaling-incompetent membrane domains or could function independently of CD4-Lck association. The current study addresses this specific question.

Using the same model system as in the earlier eLife paper (the entire methods section is a citation to the earlier paper), the authors show that truncation of the Lck-binding intracellular domain resulted in a moderate reduction in IL-2 response, as previously shown, but there was no apparent effect on proximal phosphorylation events (CD3z, Lck, ZAP70, PLCg1). They then evaluated a series of TM and JM motif mutations in the context of the truncated Lck-nonbinding molecule, and showed that these had substantially impaired co-receptor function in the IL-2 assay and reduced proximal signaling. The proximal signaling could be observed at high ligand density even with a MHC non-binding mutation in CD4, although there was still impaired IL-2 production. This result additionally illustrates that phosphorylation of the proximal signaling molecules is not sufficient to activate IL-2 expression in the context of antigen presentation.

Strengths:

The strength of the paper is the further clear demonstration that the classical model of CD4 coreceptor function (MHCII-binding CD4 bringing Lck to the TCR complex, for phosphorylation of the CD3 chain ITAMs and of the ZAP70 kinase) is not sufficient to explain TCR activation. The data, combined with the earlier eLife paper, further implicate the gly-rich TM sequence and the palmitoylation targets in the JM region as having critical roles in productive co-receptordependent TCR activation.

Weaknesses:

The major weakness of the paper is the lack of mechanistic insight into how the TM and JM motifs function. The new results are largely incremental in light of the earlier paper from this group as well as other literature, cited by the authors, that implicates "free" Lck, not associated with co-receptors, as having the major role in TCR activation. It is clear that the two motifs are important for CD4 function at low pMHCII ligand density. The proposal that they modulate interactions of TCR complex with cholesterol or other membrane lipids is an interesting one, and it would be worth further exploring by employing approaches that alter membrane lipid composition. The JM sequence presumably dictates localization within the membrane, by way of palmitoylation, which may be critical to regulate avidity of the TCR:CD4 complex for pMHCII or TCR complex allosteric effects that influence the activation threshold. Experiments that explore the basis of the mutant phenotype could substantially enhance the impact of this study.

We appreciate these thoughtful comments and suggestions. We will restate what we wrote in our preliminary response to the reviews to explain the scope of the current study:

To address comments about the limited scope of this study and referencing of the Methods secBon to our prior study, we would like to note that we submiXed the current study via the Research Advance mechanism. Our goal was to build upon the conclusions of our 2022 eLife publicaBon (PMID: 35861317) and address an unresolved quesBon from that study (as nicely summarized by Reviewer #2). In the current manuscript we present data from reducBonist experiments that were designed specifically for this purpose and, as noted by the reviewers, we provide answers to the quesBon being asked. We think that the Research Advance mechanism is an ideal opportunity to make these results available to the field given the stated purpose of such arBcles (for reference: “A Research Advance might use a new technique or a different experimental design to generate results that build upon the conclusions of the original research by, for example, providing new mechanis=c insights or extend the pathway under inves=ga=on…”). Now that we have provided evidence that CD4 does not recruit Lck to phosphorylate TCR-CD3 ITAMs in our system, nor do the GGXXG and (C/F)CV+C motifs play a role in enabling CD4 to regulate Lck proximity to TCR-CD3, we agree that it is important to form and test alternative hypotheses for how TCR-CD3 signaling is initiated.

Author Response

Reviewer #1 (Public Review):

Combining functional MRI with a decoder, the authors probe the neural substrate of the double drift illusion in visual cortex. Their elegant behavioural paradigm keeps the actual retinal position of the stimulus stable while inducing the illusion with a combination of smooth pursuit and visual motion. The results show that the illusory drift path can be decoded from a signal in extrastriate visual area hMT+ but not other visual areas. Importantly, this can be done in the absence of spatial attention to the stimulus location.

The particular strengths of this study lie in the elegant paradigm and the clear attentional control. The methodology of the decoder is powerful and at the same time straightforward, well explained, and well accepted in the literature. A potential weakness of the study is the lack of simultaneous eye movement recordings in the scanner. Such data could have provided further clarification of the potential underlying neural mechanism and whether differences in eye movements could contribute to the decoding of the visual illusion path. There are some controls that mitigate this.

We have addressed the Reviewer's comment by repeating the fMRI experiment in a new group of subjects in which we were able to also obtain concurrent, high-quality eye tracking. When we initially conducted the experiment, it was not possible to perform eye tracking in the 7T scanner at NIH. Because of this limitation, we were forced to depend on careful eye tracking in a pre-scan behavioral experiment. But in the ensuing period of time, we have developed a protocol for obtaining high quality eye tracking with an Eyelink 1000 mounted in the bore of the scanner. Now that we have the ability to collect concurrent eye tracking, we repeated the fMRI experiment and found that our main fMRI result replicated (i.e, it was possible to decode the direction of the illusion from fMRI responses in hMT+). Additional, the concurrent fMRI eye tracking enabled us to make four important observations (see new Fig 4):

First, subjects maintained stable fixation when the target was stationary during fixation and accurately pursued the vertically moving target during illusion (Fig 4). This analysis confirms that the drifting Gabor remained at a relatively fixed position on the retina during the illusory period.

Second, there were no differences in microsaccades between any of the conditions. We quantified the direction, amplitude, and frequency of all saccades for each condition. While we did observe small rightward microsaccades, none of the microsaccade characteristics differed between conditions. The rightward microsaccades may have been due to the sustained eccentric leftward fixation. Or, it may have been due to attention to the right visual field stimulus (despite the foveal attention task). Or it may have reflected the known horizontal microsaccade bias. Regardless, we do not believe our fMRI results are related to microsaccades because these small saccades did not differ across condition.

Finally, we wondered if small not-easily-quantified ocular deviations could have differed between conditions, and somehow result in differences in fMRI activity picked up by the decoding analysis. To test for this possibility, we trained a classier to discriminate condition based on the raw eye traces (just as we did in the main fMRI data analysis). But unlike the fMRI analysis, we found that it was not possible to decode the direction of the illusion from the eye traces themselves.

We conclude that the ability to decode the illusion from fMRI responses were not due to differences in eye movements caused by the illusion.

The authors provide important evidence for a potential neural substrate in the extrastriate visual cortex for encoding the perceived spatial location of a moving stimulus. This significantly extends previous studies that showed relevant spatiotopic signals outside visual cortex. Understanding the neural substrate and the underlying neural mechanisms for encoding perceived spatiotopic location are of broad importance for our understanding of the neural basis of sensory perception.

We thank the Editor for this positive assessment of our work.

Reviewer #3 (Public Review):

The authors studied the neural basis of the double drift illusion, an illusion in which a Gabor drifting both horizontally within an aperture and moving vertically along a path appears to follow a diagonal trajectory, perceptually displaced off its true vertical path in the direction of the horizontal drift. The illusion is strong and its neural basis is intriguing. The authors suggest it can be used to address the locus of spatiotopic processing in the brain. They find that fMRI BOLD activity in hMT+ can be used to decode the illusory drift direction of the stimulus, even under conditions of withdrawn attention. They internally replicate this result and ensure it is not due to local motion. They interpret the finding to indicate that hMT+ contains spatiotopic information. This was a carefully designed and conducted study, and the manuscript writing and figures are clear.

Despite the care that went into the study design and control experiments, I see some potential interpretational issues, and I am uncertain about the scientific advance. My main questions are about the interpretation of the findings, the possible confound of smooth pursuit eye movements, and the relation to previous studies, including previous fMRI studies of the same illusion. I also would like to see more thorough reporting of behavior.

Major comments

1) The authors motivate the study by saying that there have been conflicting results about which brain areas are involved in spatiotopic coding, but they did not give an indication about why there might be conflicting results or why the current study is suitable to address the previous discrepancies. Is this study simply adding another observation to the existing body of literature, or does it go beyond previous studies in a critical theoretical way?

There have indeed been conflicting results in the literature. One idea that has received some prior support in the literature is that spatiotopic location information can depend on the task. Our experiment tests this idea by measuring cortical responses during an illusion that involves spatiotopic coding. Previous human fMRI studies reporting spatiotopic coding have not really linked cortical activity with the perception of spatiotopic coordinates. Hence, we feel that our results make a unique contribution to the field.

2) The authors interpret the finding of illusory drift direction encoding in hMT+ to mean that hMT+ is coding the illusory spatial position of the stimulus. But could an alternative explanation be that hMT+ is coding the illusory global motion direction, and not the spatial position per se? If this is a possible account, then the result would still indicate that an illusory motion percept is reflected in hMT+ but it would seem not to answer the question about spatiotopic coding which motivated the paper.

Here, the Reviewer suggests an interesting alternative explanation—that responses in MT pertain to the direction of global motion rather than stimulus position. However, this alternative possibility would still involve spatiotopic coding. In order for the brain to compute the direction of global motion of a stimulus that is at a fixed retinal position, some spatiotopic computation must occur. So, we do not agree with the Reviewers suggestion that this alternative explanation undermines the motivation of this study.

3) It is good that the authors sought to rule out the possibility that smooth pursuit eye movements were driving the decoding results in hMT+, but I'm not sure they have yet convincingly done so. Decoding based on the pursuit selective voxels alone was very nearly significant (p = 0.052), which was not acknowledged in the text of the paper. Furthermore, because voxels that were both pursuit and stimulus selective were excluded from the pursuit selective ROI, decoding performance in that ROI may have been underestimated.

To clarify, voxels that were identified by both localizers were NOT excluded from either ROI. When we repeated decoding (from Expt 2, Fig 3B) using disjoint voxel selection (i.e., analyzing voxels that only responded in the stim localizer, or only responded in the pursuit localizer, and excluding voxels that responded to both), we obtained qualitatively similar results, although the magnitude of the effects were smaller, which is not surprising given the much smaller number of voxels remaining in the ROI, and hence the disjoint ROIs only proved marginally significant in MT for the stim localizer (p=0.049).

4) A previous fMRI study of the double drift illusion (Liu et al. 2019 Current Biology) also found above chance decoding of illusory drift direction in hMT+. The authors mention this study but do not discuss it, so it was unclear to me what the advance is of the current study over that study. The main differences I see are that in the current study, 1) the observer is also moving their eyes so that the double drift stimulus is theoretically stabilized on the retina, and 2) attention is withdrawn from the stimulus. But in both studies, hMT+ contains information about the illusory drift direction even though retinotopic information is the same, so it's not clear to me that the differences between these studies lead to fundamentally different interpretations.

The results of Liu et al. are not relevant to the reference frame used to encode the stimulus. Because subjects were fixating in Liu et al., the encoding of the illusion could have been in either retinal or spatiotopic coordinates. In our study, the stimulus must have been encoded in spatiotopic coordinates. One interesting feature of Liu et al. is the issue of cross decoding the illusion and actual percept (training the decoder on veridical motion of different angles, and then testing the decoder on data collected during the illusion). One potentially interesting extension of the cross decoding approach would be to train the decoder on a version of the illusion involving fixation (as in Liu et al), but then testing the decoder on the illusion during pursuit. One would expect cross decoding if spatiotopic coordinates are used in both cases. We now discuss this possibility (Discussion: Relationship to a previous study of the double-drift illusion).

Author Response

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

eLife assessment

This important study addresses the fundamentally unresolved question of why many thousands of small-effect loci contribute more to the heritability of a trait than the large-effect lead variants. The authors explore resource competition within the transcriptional machinery as one possible explanation with a simple theoretical model, concluding that the effects of resource competition would be too small to explain the heritability effects. The topic and approximation of the problem are very timely and offer an intuitive way to think about polygenic variation, but the analysis of the simple model appears to be incomplete, leaving the main claims only partially supported.

We thank eLife for recognizing the importance of our work. We hope the revised manuscript addresses the reviewers’ reservations.

Public Reviews:

Reviewer #1 (Public Review):

This study explores whether the extreme polygenicity of common traits can be explained in part by competition among genes for limiting molecular resources (such as RNA polymerases) involved in gene regulation. The authors hypothesise that such competition would cause the expression levels of all genes that utilise the same molecular resource to be correlated and could thus, in principle, partly explain weak trans-regulatory effects and the observation of highly polygenic architectures of gene expression. They study this hypothesis under a very simple model where the same molecule binds to regulatory elements of a large number m of genes, and conclude that this gives rise to trans-regulatory effects that scale as 1/m, and which may thus be negligible for large m.

We thank the reviewer for their thorough and thoughtful review of our manuscript.

The main limitation of this study lies in the details of the mathematical analysis, which does not adequately account for various small effects, whose magnitude scales inversely with the number m of genes that compete for the limiting molecular resource. In particular, the fraction of "free" molecule (which is unbound to any of the genes) also scales as 1/m, but is not accounted for in the analysis, making it difficult to assess whether the quantitative conclusions are indeed correct.

It is explicitly accounted for in the supplement.

Second, the questions raised in this study are better analysed in the framework of a sensitivity or perturbation analysis, i.e., by asking how changes in expression level or binding affinity at one gene (rather than the total expression level or total binding affinity) affect expression level at other genes. In the context of complex traits, where an increase in gene expression can either increase or decrease the trait, we believe the most important quantity of interest is variation in expression and, therefore, trait variation. Nevertheless, our results do show that the relative change in expression due to competition is also small.

Thus, while the qualitative conclusion that resource competition in itself is unlikely to mediate trans-regulatory effects and explain highly polygenic architectures of gene expression traits probably holds, the mathematical reasoning used to arrive at this conclusion requires more care.

In my opinion, the potential impact of this kind of analysis rests at least partly on the plausibility of the initial hypothesis- namely whether most molecular resources involved in gene regulation are indeed "limiting resources". This is not obvious, and may require a careful assessment of existing evidence, e..g., what is the concentration of bound vs. unbound molecular species (such as RNA polymerases) in various cell types?

We intentionally looked at the most extreme case of extreme resource limitation, and we conclude that since extreme resource limitation is a small effect, the same would be true of weak resource limitation, when unbound molecules play an important role. We put more emphasis on this point in our revised text.

Reviewer #1 (Recommendations For The Authors):

While the main conclusion that resource competition in itself is unlikely to mediate trans effects and explain high levels of polygenicity may well be correct, I am not convinced that the mathematical reasoning presented in support of this conclusion is entirely correct. I will attempt to outline my concerns mainly in the context of section 2, since the arguments in sections 3 and 4 build upon this.

(a) The key assumption underlying the approximations in equations 3, 4, and 5 is that there is very little free polymerase, in other words /_0 is a small quantity. However, the second and third terms that emerge in equation 7 are also small quantities and (as far as I can see) of the same order as /_0. Thus, one cannot simply use equation 4 or 5 as a starting point to derive eq. 7 and should instead use the exact x_i = (g_i [G])/ (1+g_tot [G]), in order to make sure that all (and not just some) terms that are similar in order of magnitude are accounted for in the analysis.

The concentration of free polymerase is marked as [P], and we explicitly assume (just before eq. 2) that [P]<<[P]0 with [P]0 being the overall concentration of polymerase. This is a conservative assumption – we consider extreme resource competition with little free polymerase and since we since only a small effect in this extreme scenario we assume it would be a small effect also for less extreme scenarios. We put more emphasis on this point in our revised text.

More concretely, the difference between the exact x_i = (g_i [G])/ (1+g_tot [G]) and the approximate x_i = (g_i / g_tot) is precisely 1/m (for large m) in the example considered line 246 onwards. Thus, I suspect that the conclusion that Var[x_i] = (1-1/m)Var[g_i] in that example is just an artefact of starting with eqs. 4 and 5. As a sanity check, it may be useful to actually simulate resource competition explicitly (maybe using a deterministic simulation) under the explicit model [PG_i] = g_i [G] and _0 = + Sum[[PG]_i , i=1,m] without making any further approximations to see if perturbations in g_i actually produce Order [1/m] effects in the variance of x_i for the example considered line 246 onwards (this would require simulating with a few different m and plotting Var[x_i] vs. m for example).

The exact equation the reviewer is alluding to describes a scenario of non-extreme resource competition. If g_tot [G]>>1, i.e. if most polymerase is bound to a gene then x_i is equal to g_i/g_tot and this is the scenario we are considering of extreme competition. If g_tot [G]<<1, then x_i=g_i [G] and competition has no effect. While the intermediate case is interesting, we see no reason for the effects to be larger than in the extreme competition case. We have added the results of simulations in the supplement to validate our arguments.

Lines 231-239: Because of the concerns highlighted above and questions about the validity of equation 7, I am not convinced that the interpretations given here and also in section 4 are correct.

(b) Lines 219-230 (including equations 6 and 7): I think to address the question of whether genetic changes in cis-regulatory elements for a given gene have an effect on other genes (under this model of resource competition), it is better to spell out the argument in terms of Var[ dx_i ] rather than Var[x_i], where dx_i is the change in expression level at gene i due to changes at all m genes, dg_i is the change in gene activity due to (genetic) changes in the relevant regulatory elements associated with gene i etc. Var[ dx_i ] can then be expressed as a sum of Var[dg_i], Var[dg_tot] and Cov[d g_i, dg_tot]. However, I suspect that to do this correctly, one should not start with the approximate x_i=g_i/g_tot : see previous comment.

The variance of the deviation from the mean is mathematically identical to the overall variance, Var[ dx_i ]= Var[ x_i ]. Our analysis is therefore equivalent to the suggested analysis.

Somewhere in all of this, there is also an implicit assumption that E[dg_i] is zero, i.e, mutations are as likely to increase as to decrease binding affinities so that one needs to only consider Var[dx_i] and not E[dx_i]; this assumption should be spelled out.

Our results concern the variation around trait means and therefore we have not included a possible mean effect of mutation, which would not affect the results but just shift the mean.

Some minor comments (mostly related to the introduction and general context):

• I think it would be worth connecting more with the literature on molecular competition and gene regulation (see e.g., How Molecular Competition Influences Fluxes in Gene Expression Networks, De Vos et al, Plos One 2011). Even though this literature does not frame questions in terms of "polygenicity of traits", these analyses address the same basic questions: to what extent do perturbations in gene expression at one gene affect other genes, or to what extent is there crosstalk between different genes or pathways?

We have expanded our introduction to refer to De Vos et al, as well as a few other papers we have recently become aware of. (e.g., Jie Lin & Ariel Amir Nature Communications volume 9, Article number: 4496 (2018))

• Lines 88-89: "supports the network component of the model" is a vague phrase that does not convey much. It would be useful to clarify and make this more precise.

We have clarified this phrasing in the text.

• Lines 113-114: In the context of "selective constraint", it may also be worth discussing previous work by one of the authors: "A population genetic interpretation of GWAS findings for human quantitative traits". What implications would stabilizing selection on multiple traits (as opposed to simple purifying selection) have for the distribution of variances across trait loci and the extent to which trait architectures appear to be polygenic?

While most definitely of great interest to some of the authors, the distribution of variance across loci does not affect our results.

References: Barton and Etheridge 2018 in line 54 is not the correct reference; it should be Barton et al 2017 (paper with Amandine Veber). Fisher 1919 in line 52 is actually Fisher 1918. The formatting of references in the next paragraph (and in various other places in the paper) is also a bit unusual, with some authors referred to by their full names and others only by their last. I believe that it may be useful to crosscheck references throughout the paper.

We have crosschecked the references in the paper.

Line 164: Some word appears to be missing here. Maybe bound -> bound to ?

Fixed

Reviewer #2 (Public Review):

The question the authors pose is very simple and yet very important. Does the fact that many genes compete for Pol II to be transcribed explain why so many trans-eQTL contribute to the heritability of complex traits? That is, if a gene uses up a proportion of Pol II, does that in turn affect the transcriptional output of other genes relevant or even irrelevant for the trait in a way that their effect will be captured in a genome-wide association study? If yes, then the large number of genetic effects associated with variation in complex traits can be explained but such trans-propagating has effects on the transcriptional output of many genes.

This is a very timely question given that we still don't understand how, mechanistically, so many genes can be involved in complex traits variation. Their approach to this question is very simple and it is framed in classic enzyme-substrate equations. The authors show that the trans-propagating effect is too small to explain the ~70% of heritability of complex traits that are associated with trans-effects. Their conclusion relies on the comparison of the order of magnitude of a) the quantifiable transcriptional effects due to Pol II competition, and b) the observed percentage of variance explained by trans effects (data coming from Liu et al 2019, from the same lab).

The results shown in this manuscript rule out that competition for limited resources in the cell (not restricted to Pol II, but applicable to any other cellular resource like ribosomes, etc) could explain the heritability of complex traits.

We thanked the Reviewer for his resounding support of our paper!

Reviewer #2 (Recommendations For The Authors):

The authors rely on simulated data, and although the conclusions hold in a biologically-realistic scenario given the big difference in effect sizes, I wonder if the authors could provide data from the literature (if available) that give the reader a point of reference for the steady state of cells in terms of free/occupied Pol II molecules and/or free/occupied transcription binding sites. This information won't change the conclusion of the manuscript, but it will put it in the context of real biological data.

We have scoured the literature, but have not found readily available data with which to validate our results (beyond that which is already referenced).

Reviewer #3 (Public Review):

Human complex traits including common diseases are highly polygenic (influenced by thousands of loci). This observation is in need of an explanation. The authors of this manuscript propose a model that competition for a single global resource (such as RNA polymerase II) may lead to a highly polygenic architecture of traits. Following an analytical examination, the authors reject their hypothesis. This work is of clear interest to the field. It remains to be seen if the model covers the variety of possible competition models.

We thank the Reviewer for his assessment, support and comments.

Reviewer #3 (Recommendations For The Authors):

This manuscript provides a straightforward and elegant quantitative argument that the competition for the RNA polymerase is not a significant source of trans-eQTLs and, more generally, of genetic variance of complex polygenic phenotypes. This is an unusual manuscript because the authors propose a hypothesis that they confidently reject based on a calculation. This negative result is intuitive. Still, the manuscript is of interest. Progress in understanding the highly polygenic architecture of complex traits is welcome, and the resource competition hypothesis is quite natural. I have three specific comments/concerns listed below.

(1) The manuscripts states that V(x_i)=V(g_i/g_tot). Unless I am missing something, this seems to result from a very strong implicit assumption that all genetic variance is due to variation in the binding of RNA polymerase, while x_i_max is a constant. I would expect that x_i_max may also be genetically variable due to many effects unrelated to the Pol II binding (e.g. transcription rate, bursting, presence of R-loops etc.). I guess that the assumption made by the authors is conservative.

Indeed. We made conservative assumptions throughout, aiming to consider the most extreme scenario in which resource competition may affect trait variation. Our logic being that if even under the most extreme scenario resource competition is a small effect then it is a small effect in all scenarios. We put more emphasis on this point in our revised text.

(2) The manuscript focuses on the competition for RNA polymerase but suggests that the lesson learned is highly generalizable. However, it is an example of a single global limiting resource resulting in first-order kinetics. What happens in a realistic scenario of competition for multiple resources associated with transcription and with downstream processes (free ribonucleotides, spliceosome, polyadenylation machinery, ribosome, post-translational modifications)? It is possible that in most cases a single resource is a limiting factor, but an investigation (or even a brief discussion) of this question would support the claim that the results are generalizable.

We expect competition for multiple resource to result in similarly weak effects. Since there is not a great number of such resources, we do not expect it to change our qualitative result. We added language to that effect in the main text.

(3) Alternatively, what happens in a scenario of competition for multiple local resources shared by a few genes (co-factors, substrates, chaperones, micro-RNAs, post-translational modification factors such as kinases, degradation factors, scaffolding proteins)? In this case, each gene would compete for resources with a few other genes increasing polygenicity without a global competition with all other genes. Intuitively, a large set of such local competitions may lead to a highly polygenic architecture.

This is indeed a scenario in which competition may be a large effect which we mention in our discussion. “the conclusions may differ in contexts where a very small number of genes compete for a highly limited resource, such as access to a particular molecular transporter”

Author Response

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

We greatly appreciate your positive assessment and the suggestions by Reviewer #2 on the previous version of our manuscript, all of which are very helpful and have greatly improved our manuscript. We have added a description of Biomineralized columnar architecture in the Results section, added a discussion of the Family Eoobolidae, provided more details in the Material and Methods section, and revised other parts of the manuscript based on her/his comments. We are grateful that these comments have enhanced the overall quality of our manuscript. In this letter, we take the opportunity to note and discuss the various changes as below.

Reviewer #2:

(1) Two early Cambrian taxa of linguliform brachiopods are assigned to the family Eoobolidae. The taxa exhibit a columnar shell structure and the phylogenetic implications of this shell structure in relation to other early Cambrian families is discussed. It is the interesting idea regarding the evolution of shell structure.

We thank Reviewer 2 very much for her/his very constructive suggestions. All the comments have been thoroughly considered, and introduced into the revised version of the manuscript.

(2) The early record of shell structures of linguliform brachiopods is incomplete and partly contradictory. The authors maintain silence regarding contradictory information throughout the article to an extent that information is cited wrongly.

We agree with Reviewer #2 that the early record of shell structure of linguliform brachiopods is incomplete and potentially in some instances contradictory. This situation is well demonstrated in the Introduction and Systematic Palaeontology sections of this paper. This is also the reason why we think the detailed investigation of early linguliform shell architectures is so important, and we hope this work will be useful for further comparative studies on brachiopod biomineralization. We also understand that more detailed studies of the complexity and diversity of linguliform brachiopod architectures (especially their early fossil representatives) require further investigation.

(3) The article is written under the assumption that all eoobolids have a columnar shell structure. Thus, the previously claimed columnar structure of Eoobolus incipiens which has been re-illustrated in the paper is not convincing and could be interpreted in other ways.

Yes, the type specimen of Eoobolus is poorly known and we do not know its shell structure, but the ornamentation, pseudointerarea etc. are well preserved and promote a character diagnosis. In this paper, we focus on the detailed study of Cambrian eoobolids with exquisitely well-preserved columns from the Cambrian Series 2 based on the collection of more than 30 thousand early Cambrian brachiopod specimens in China and Australia. With the wide preservation of columnar shells in early eoobolid specimens, it is likely that Eoobolus has columnar shell architecture, although there is no documentation of the shell structure from every single Eoobolus specimen.

The secondary columns of Eoobolus incipiens is well demonstrated in Fig. 4a. The size of these columns can be well compared with the columns from other Eoobolus species and acrotretide brachiopods, which are quite different from the criss-cross baculae. As we noted in the manuscript, the columnar structure Eoobolus incipiens is very simple (short columns and less number of columnar units) and can be readily secondarily phosphatised. This is also the reason why it is hard to find the columnar shell architecture in early eoobolids.

(4) The article needs a proper results section. The Discussion is mainly a review of published data. Other potential results are hidden in this "discussion".

I would recommend to reorganize the paper and make it a solid presentation of the new taxa and other new results, i.e., have a solid Results section. The Discussion should discuss relevant points that relate to the new results rather than reviewing shell structure in general but skipping relevant parts such as the tertiary shell layer.

We have reorganised the manuscript based on these comments. A general description of the biomineralized columnar architecture is added in the Results section. As the Supplementary section (main results) includes 7 figures and 3 tables, it will increase the size of the current paper if they are moved to the main text. We would prefer to keep the main results in the Supplementary based on the style and format of eLife.

As the current information on the shell structures of early linguliform brachiopods is unclear, we need to review most of the previous studies on brachiopod shells in the first part of Discussion section. It will help the readers to follow our results and conclusion. So, we think some of the review content is necessary and helps build the Discussion section. The tertiary shell layer, which is not developed in our studied material, is not discussed in the current research.

(5) In addition, a more elaborate Methods section is needed in which it is explained how the data for shell thicknesses and numbers of laminae was obtained.

The potential evolutionary patterns that are discussed towards the end (summarized in Fig 6) are interesting but rather unconvincing as the way the data has been obtained has never been clarified. Shell thicknesses and numbers of laminae that built up the shell of several taxa are compared, but at no point it is stated where these measurements were taken. Shell thicknesses vary within a shell and also the presence of the never mentioned tertiary layer is modifying shell thicknesses. Hence, the presented data appears random and is not comparable. The obtained evolutionary patterns must be considered as dubious.

A proper Methods section would be needed that explains how the data presented in Fig. 6 has been obtained. Plus it needs to be convincingly explained that the obtained data is in fact comparable and represents, e.g., equivalent areas of the shell in all involved taxa.

All the information is added in the Material and Methods section. We are aware of the marginal accretionary secretion of brachiopod shells. It is well known that the shell at the posterior is thicker (usually the thickest) than that at the anterior, we did not note this in the previous manuscript. We have measured all the shell data (shell thickness and number of columnar unit) from the posterior part of the adult shell for all the studied taxa. And the measurements of diameter and height of orthogonal columns are performed on available adult specimens from this study and previously published literature. Consequently, the obtained data are comparable and represent equivalent areas of the shell on all involved taxa.

In term of the tertiary shell layer, we do not find any evidence of this tertiary shell layer from our studied material. The tertiary shell layer is well developed in some recent and Palaeozoic lingulides (Holmer, 1989), but it is not recognised in the early eoobolides and acrotretides.

(6) A critical revision of the family Eoobolidae and Lingulellotretidae including a revision of the type species of Eoobolus and Lingulellotreta is needed.

Concerning the families Eoobolidae and Lingulellotretidae, we are aware of the current problematic situation of these families, and we have added more remarks regarding the Eoobolidae in the Systematic Palaeontology section of the manuscript. However, the revision of the families Eoobolidae and Lingulellotretidae falls outside the scope of this paper. We prefer to exclude it just now, as it will be part of an upcoming publication based on more material from China, Australia, Sweden and Estonia that we are currently working on.

Author Response

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

eLife assessment

This manuscript provides important insights into the degradation of a host tRNA modification enzyme TRMT1 by SARS-CoV-2 protease nsp5. The data convincingly support the main conclusions of the paper. These results will be of interest to virologists interested in studying the alterations in tRNA modifications, host methyltransferases, and viral infections.

Public Reviews:

Response to Public Reviews

We appreciate the reviewers’ assessment that our findings are well supported and provide important insight to the field. We also thank the reviewers for their comments and suggestions that have improved the quality of this manuscript. Through the requested edits and experiments, we provide additional results in this revision that further support and extend our original findings.

We acknowledge the major questions that remain to be addressed, including the biological relevance of TRMT1 cleavage by Nsp5. We note that elucidating the biological role of host protein cleavage by viral proteases has been a long-standing challenge. For example, several endogenous proteins have been identified as cleavage targets of HIV protease, but the functional relevance for many of these cases took decades to resolve or remain unknown to this day. Nonetheless, we have added additional experiments that suggest a possible role for TRMT1 and TRMT1 cleavage in SARS-CoV-2 pathobiology.

Key additions in the revised manuscript include:

• Subcellular localization of full-length TRMT1 and TRMT1 fragments (Supplemental Figure 4).

• Experiments demonstrating that TRMT1 levels are reduced to near background levels in SARS-CoV-2 infected human cells at higher MOI (Figure 6C and D).

• Results showing that expression of the non-cleavable TRMT1 mutant can promote virion particle infectivity (Figure 8).

• The addition of an “Ideas and Speculation” subsection that is now being offered to authors by eLife.

Reviewer #1 (Public Review):

Zhang et al. investigate the hypothesis that tRNA methyl transferase 1 (TRMT1) is cleaved by NSP5 (nonstructural protein 5 or MPro), the SARS-CoV-2 main protease, during SARS-CoV-2 infection. They provide solid evidence that TRMT1 is a substrate of Nsp5, revealing an Nsp5 target consensus sequence and evidence of TRMT1 cleavage in cells. Their conclusions are exceptionally strong given the co-submission by D'Oliveira et al showing cleavage of TRMT1 in vitro by Nsp5. Separately, the authors convincingly demonstrate widespread downregulation of RNA modifications during CoV-2 infection, including a requirement for TRMT1 in efficient viral replication. This finding is congruent with the authors' previous work defining the impact of TRMT1 and m2,2g on global translation, which is most likely necessary to support infection and virion production. What still remains unclear is the functional relevance of TRMT1 cleavage by Nsp5 during infection. Based on the data provided here, TRMT1 cleavage may be an act by CoV2 to self-limit replication, as the expression of a non-cleavable TRMT1 (versus wild-type TRMT1) supports enhanced viral RNA expression at certain MOIs. Theoretically, TRMT1 cleavage should inactivate the modification activity of TRMT1, which the authors thoroughly and elegantly investigate with rigorous biochemical assays. However, only a minority of TRMT1 undergoes cleavage during infection in this study and thus whether TRMT1 cleavage serves an important functional role during CoV-2 replication will be an important topic for future work. The authors fairly assess their work in this regard. This study pushes forward the idea that control of tRNA expression and functionality is an important and understudied area of host-pathogen interaction.

We thank the reviewer for the thoughtful assessment of our study.

We acknowledge that only a minority of TRMT1 undergoes cleavage during infection at the originally tested MOI. However, the ~40% reduction in TRMT1 levels after infection with SARS-CoV-2 is quite substantial considering that the TRMT1 in the nucleus and mitochondria are likely to be inaccessible to Nsp5. Moreover, we detected a reduction in m2,2G modification in the infected human cells, providing evidence for a functional impact on TRMT1 activity (Figure 1C).

To further test the effects of SARS-CoV-2 infection on endogenous TRMT1, we infected 293T cells at a higher MOI and measured TRMT1 levels. At MOI=5, we found that SARS-CoV-2 infection led to near complete depletion of TRMT1 in human cells. This result suggests that SARS-CoV-2 infection could have a profound impact on TRMT1 levels during pathogenesis. We have added this new experiment as Figures 6C and D.

Weaknesses noted:

The detection of the N-terminal TRMT1 fragment by western blot is not robust. The polyclonal antibody used to detect TRMT1 in this work cross-reacts with a non-specific protein product. Unfortunately, this obstructs the visualization of the predicted N-terminal TRMT1 fragment. It is unclear how the authors were able to perform densitometry, given the interference of the nonspecific band. Additionally, the replicates in the source data make it clear that the appearance of the N-terminal fragment "wisp" under the non-specific band is not seen in every replicate. Though the disappearance of this wisp with mutant Nsp5 and uncleavable TRMT1 is reassuring, the detection of the N-terminal fragment with the TRMT1 antibody should be assessed critically. Considering this group has strong research interests in TRMT1, I assume that attempts to make other antibodies have proved unfruitful. Additionally, N-terminal tagging of TRMT1 is predicted to disrupt the mitochondrial targeting signal, eliminating the potential for using alternative antibodies to see the N-terminal fragment.

We agree that the anti-TRMT1 antibody used here is sub-optimal for detection of the N-terminal TRMT1 fragment. However, as noted by the Reviewer, we provided multiple ways of corroborating that the lower-molecular weight band detected in human cells expressing Nsp5 corresponds to the N-terminal TRMT1 fragment. We have shown that the TRMT1 cleavage band is not detectable in human cells expressing GFP or inactive Nsp5. This indicates that the lower molecular weight TRMT1 band only arises when active Nsp5 protease is expressed. Moreover, the TRMT1 cleavage band is not detectable in TRMT1-KO cell lines, demonstrating that the band arises from TRMT1 cleavage rather than a non-specific protein. We have also detected the C-terminal fragment if TRMT1 is over-expressed with Nsp5. In addition, we have shown that the mutation of the predicted Nsp5 cleavage site in TRMT1 abolishes the appearance of the N- and Cterminal cleavage fragments.

Despite the drawbacks of this antibody, we identified gel running conditions that resolves the non-specific band from the N-terminal TRMT1 cleavage fragment. Thus, for quantification, we measured the total signal of both the cleavage band and the nonspecific band in all lanes (Figure 3). After normalization to actin, the total signal from the cleavage band and the non-specific band in the control lane from cells expressing GFP was subtracted from the lanes with cells expressing Nsp5 to calculate the signal arising from the cleavage band. We have updated our Materials and Methods to provide details on how we quantified the TRMT1 cleavage band.

While we did test other antibodies against TRMT1, none of them were sensitive enough to detect TRMT1 cleavage fragments at endogenous levels. For example, we included results with an antibody targeting the C-terminus of TRMT1 that could not detect TRMT1 cleavage products at endogenous levels (Supplemental Figure 3). However, the antibody could detect the C-terminal TRMT1 fragments if TRMT1 was overexpressed with Nsp5 (Supplemental Figure 3).

These technical issues reiterate the fact that the functional significance of TRMT1 cleavage during CoV-2 infection remains unclear. However, this study demonstrates an important finding that the tRNA modification landscape is altered during CoV-2 infection and that TRMT1 is an important host factor supporting CoV-2 replication.

We agree that the functional relevance of TRMT1 cleavage by Nsp5 remains an open question. Thus, we have added an experiment to test the functional impact of TRMT1 on virion particle production and infectivity (Figure 8). We find that TRMT1 expression is required for optimal virus production, consistent with our observation that TRMT1deficient cells exhibit reduced viral RNA replication. In addition, we find that expression of the non-cleavable TRMT1 mutant can promote virion particle infectivity (Figure 8, TRMT1-Q530N). These results are consistent with the Reviewer’s conclusion that “TRMT1 cleavage may be an act by CoV-2 to self-limit replication, as the expression of a non-cleavable TRMT1 (versus wild-type TRMT1) supports enhanced viral RNA expression at certain MOIs”. We discuss the potential implications of this result and their functional relevance in the “Ideas and Speculation” subsection.

Reviewer #2 (Public Review):

Summary:

The manuscript titled 'Proteolytic cleavage and inactivation of the TRMT1 tRNA modification enzyme by SARS-CoV-2 main protease' from K. Zhang et al. demonstrates that several RNA modifications are downregulated during SARS-CoV-2 infection including the widespread m2,2G methylation, which potentially contributes to changes in host translation. To understand the molecular basis behind this global hypomodification of RNA during infection, the authors focused on the human methyltransferase TRMT1 that catalyzes the m2,2G modification. They reveal that TRMT1 not only interacts with the main SARS-CoV-2 protease (Nsp5) in human cells but is also cleaved by Nsp5. To establish if TRMT1 cleavage by Nsp5 contributes to the reduction in m2,2G levels, the authors show compelling evidence that the TRMT1 fragments are incapable of methylating the RNA substrates due to loss of RNA binding by the catalytic domain. They further determine that expression of full-length TRMT1 is required for optimal SARS-CoV-2 replication in 293T cells. Nevertheless, the cleavage of TRMT1 was dispensable for SARS-CoV-2 replication hinting at the possibility that TRMT1 could be an off-target or fortuitous substrate of Nsp5. Overall, this study will be of interest to virologists and biologists studying the role of RNA modification and RNA modifying enzymes in viral infection.

We thank the reviewer for the thoughtful assessment of our study.

We agree with the possibility that TRMT1 could be a fortuitous substrate of Nsp5 due to the coincidental presence of a Nsp5 cleavage site in TRMT1. As considered in our Discussion section, TRMT1 cleavage could be a collateral effect of SARS-CoV-2 infection. While TRMT1 could be an off-target substrate during viral infection, the subsequent effect on tRNA modification levels could have physiological consequences on downstream processes that affect cellular health. This information could still be useful for understanding the pathophysiological consequences of SARS-CoV-2 infection in tissues.

Strengths:

• The authors use a state-of-the-art mass spectrometry approach to quantify RNA modifications in human cells infected with SARS-CoV-2.

• The authors go to great length to demonstrate that SARS-CoV-2 main protease, Nsp5, interacts, and cleaves TRMT1 in cells and perform important controls when needed. They use a series of overexpression with strategically placed tags on both TRMT1 and Nsp5 to strengthen their observations.

• The use of an inactive Nsp5 mutant (C145A) strongly supports the claim of the authors that Nsp5 is solely responsible for TRMT1 cleavage in cells.

• Although the direct cleavage was not experimentally determined, the authors convincingly show that TRMT1 Q530N is not cleaved by Nsp5 suggesting that the predicted cleavage site at this position is most likely the bona fide region processed by Nsp5 in cells.

• To understand the impact of TRMT1 cleavage on its RNA methylation activity, the authors rigorously test four protein constructs for their capacity not only to bind RNA but also to introduce the m2,2G modification. They demonstrate that the fragments resulting from TRMT1 cleavage are inactive and cannot methylate RNA. They further establish that the C-terminal region of TRMT1 (containing a zinc-finger domain) is the main binding site for RNA.

• While 293T cells are unlikely an ideal model system to study SARS-CoV-2 infection, the authors use two cell lines and well-designed rescue experiments to uncover that TRMT1 is required for optimal SARS-CoV-2 replication.

Weaknesses:

• Immunoblo0ng is extensively used to probe for TRMT1 degradation by Nsp5 in this study. Regretfully, the polyclonal antibody used by the authors shows strong non-specific binding to other epitopes. This complicates the data interpretation and quantification since the cleaved TRMT1 band migrates very closely to a main non-specific band detected by the antibody (for instance Fig 3A). While this reviewer is concerned about the cross-contamination during quantification of the N-TRMT1, the loss of this faint cleaved band with the TRMT1 Q530N mutant is reassuring. Nevertheless, the poor behavior of this antibody for TRMT1 detection was already reported and the authors should have taken better precautions or designed a different strategy to circumvent the limitation of this antibody by relying on additional tags.

We acknowledge the sub-optimal performance of the commercial anti-TRMT1 antibody used in our study. Nevertheless, we have provided multiple lines of evidence indicating that the lower molecular weight band detected using this antibody corresponds to the N-terminal TRMT1 fragment. As noted by the reviewer, we have shown that the lower molecular weight band disappears using the TRMT1-Q530N non-cleavable mutant. The lower molecular weight signal is also absent in TRMT1-KO cell lines expressing Nsp5. Moreover, we have shown that the TRMT1 cleavage band is undetectable in human cells expressing GFP or inactive Nsp5. We have also detected the C-terminal fragment when TRMT1 is over-expressed with Nsp5.

As discussed in the response to Reviewer 1, we did consider alternative approaches for detecting the N-terminal fragment. We thought about tagging TRMT1 at the N-terminus so that we could detect the cleavage band using a different antibody. However, as noted by Reviewer 1, the tagging of TRMT1 at the N-terminus is likely to disrupt the mitochondrial targeting signal and alter the localization of TRMT1. In addition, we spent considerable time and effort testing alternative antibodies against TRMT1. However, none of them were effective at detecting the N- or C-terminal TRMT1 fragments. For example, we included results with a different antibody targeting the C-terminus of TRMT1 that could not detect TRMT1 cleavage products at endogenous levels but could detect them when TRMT1 was overexpressed with Nsp5 (Supplemental Figure 3).

• While 293T cells are convenient to use, it is not a well-suited model system to study SARS-CoV2 infection and replication. Therefore, some of the conclusions from this study might not apply to better-suited cell systems such as Vero E6 cells or might not be observed in patient-infected cells.

We acknowledge the potential caveats associated with using 293T human embryonic cells as a system for testing SARS-CoV2 replication. However, we note that 293T cells have been used as a physiological model for discovering and characterizing key aspects of SARS-CoV-2 biology, including viral replication. For example, SARS-CoV-2 has been shown to exhibit significant replication and virion production in 293T cells expressing ACE2 that can be inhibited by known SARS-CoV-2 antiviral compounds:

• https://www.thelancet.com/journals/lanmic/article/PIIS2666-5247(20)300045/fulltext

• https://www.ncbi.nlm.nih.gov/pmc/articles/PMC9444585/

• https://www.science.org/doi/10.1126/sciadv.add3867

• https://www.pnas.org/doi/full/10.1073/pnas.2025866118

293T cells have also been demonstrated to exhibit cytopathic effects upon SARS-CoV-2 infection that are dependent upon the ACE2 receptor and mirror that of infected lung cells in culture and in patient tissues:

• https://www.embopress.org/doi/full/10.15252/embj.2020106267

• https://journals.asm.org/doi/full/10.1128/jvi.00002-22

• https://journals.plos.org/plospathogens/article?id=10.1371/journal.ppat.1009715

• https://www.nature.com/articles/s41559-021-01407-1

In addition to 293T cells, we have demonstrated that infection of MRC5 human pulmonary fibroblast cells with SARS-CoV-2 results in a decrease in TRMT1 levels and m2,2G modification (Figure 1). The reduction in TRMT1 levels in MRC5 cells after SARS-CoV-2 infection is similar to that observed in 293T cells.

• The reduction of bulk TRMT1 levels is minor during infection of MRC5 cells with SARS-CoV-2 (Fig 1). This does not seem to agree with the more dramatic reduction in m2,2G modification levels. Cellular Localization experiments of TRMT1 would help clarify this. While TRMT1 is found in the cytoplasm and nucleus, it is possible that TRMT1 is more dramatically degraded in the cytoplasm due to easier access by Nsp5.

We agree that the processing of newly synthesized TRMT1 in the cytoplasm is likely to be the main cause for the reduction of TRMT1 levels in the infected MRC5 cells. Thus, we followed the Reviewer’s suggestion to conduct cellular localization experiments of TRMT1 (Supplemental Figure 4). Through these experiments, we show that full-length TRMT1 exhibits localization to the cytoplasm, mitochondria, and nucleus, consistent with prior findings from our group and others. This result supports the conclusion that cytoplasmic TRMT1 is the likely target of Nsp5 cleavage while TRMT1 in the nucleus and mitochondria are inaccessible to Nsp5. We also note that the decrease in cytoplasmic TRMT1 could account for the reduction in m2,2G modifications if the cytoplasmic pool of TRMT1 is responsible for modifying any exported tRNAs that were not modified in the nucleus.

• In Fig 6, the authors show that TRMT1 is required for optimal SARS-CoV-2 replication. This can be rescued by expressing TRMT1 (Fig 7). Nevertheless, it is unknown if the methylation activity of TRMT1 is required. The authors could have expressed an inactive TRMT1 mutant (by disrupting the SAM binding site) to establish if the RNA modification by TRMT1 is important for SARS-CoV-2 replication or if it is the protein backbone that might contribute to other processes.

We agree that it would be interesting to test if the methylation activity of TRMT1 is important for optimal SARS-CoV-2 replication. However, the present study focuses on the cleavage of TRMT1 by Nsp5 and the biological effects of this cleavage. Thus, we feel that generating another human cell line lies outside the scope of this paper and would be an excellent idea for future studies. We thank the reviewer for the proposed experiment.

• Fig 7, the authors used the Q530N variant to rescue SARS-CoV-2 replication in TRMT1 KO cells. This is an important experiment and unexpectedly reveals that TRMT1 cleavage by Nsp5 is not required for viral replication. To strengthen the claim of the authors that TRMT1 is required to promote viral replication and that its cleavage inhibits RNA methylation, the authors could express the TRMT1 N-terminal construct in the TRMT1 KO cells to assess if viral replication is restored or not to similar levels as WT TRMT1. This will further validate the potential biological importance of TRMT1 cleavage by Nsp5.

Indeed, we did not expect to find that human cells expressing the TRMT1-Q530N variant exhibit higher levels of viral replication. This suggests that cleavage of TRMT1 is inhibitory for viral replication. To provide further support for this observation, we analyzed the viral titer and infectivity of supernatants derived from human cells expressing wildtype TRMT1 or TRMT1-Q530N. Consistent with our finding that TRMT1-Q530N cells contain more viral RNA, the media supernatants from TRMT1Q530N expressing cells exhibit higher viral titer and infectivity compared to supernatants from TRMT1-KO cells expressing wildtype TRMT1. These results provide additional evidence that TRMT1 is required to promote viral replication. Moreover, these findings suggest that TRMT1 cleavage and reduced protein synthesis could selflimit viral replication. The additional results have been added as Figure 8.

• Fig 7 shows that the TRMT1 Q530N variant rescues SARS-CoV-2 replication to greater levels then WT TRMT1. The authors should discuss this in greater detail and its possible implications with their proposed statement. For instance, are m2,2G levels higher in Q530N compared to WT? Does Q530N co-elute with Nsp5 or is the interaction disrupted in cells?

These are excellent points brought up by the Reviewer. As noted above, we have added an additional experiment that tests the functional relevance of TRMT1 expression and cleavage on virion production and infectivity (Figure 8). Moreover, we have followed the Reviewer’s suggestion and discussed the potential implications of these findings in the “Ideas and Speculation” subsection.

Reviewer #3 (Public Review):

Summary:

In this manuscript, the authors have used biochemical approaches to provide compelling evidence for the cleavage of TRMT1 by SARS-CoV-2 Nsp5 protease. This work is of wide interest to biochemists, cell biologists, and structural biologists in the coronavirus (CoV) field. Furthermore, it substantially advances the understanding of how CoV's interact with host factors during infection and modify cellular metabolism.

We thank the reviewer for the thoughtful assessment of our study.

Strengths:

The authors provide multiple lines of biochemical evidence to report a TRMT1-Nsp5 interaction during SARS-CoV-2 infection. They show that the host enzyme TRMT1 is cleaved at a specific site and that it generates fragments that are incapable of functioning properly. This is an important result because TRMT1 is a critical player in host protein synthesis. This also advances our understanding of virus-host interactions during SARS-CoV-2 infections.

Weaknesses:

The major weakness is the lack of mechanistic insights into TRMT1-Nsp5 interactions. The authors have provided commendable biochemical data on proving the TRMT1-Nsp5 interaction but without clear mechanistic insights into when this interaction takes place in the context of SARS-CoV-2 propagation, what are the functional consequences of this interaction on host biology, and does this somehow benefit the infecting virus? I feel that the authors played it a bit safe despite having access to several reagents and an extremely promising research direction.

We agree that our findings have prompted questions on the mechanistic and functional relevance of TRMT1 cleavage by Nsp5. To begin addressing the latter point, we have included a new experiment testing the impact of TRMT1 expression and cleavage on SARS-CoV-2 virus production and infectivity (Figure 8). We find that TRMT1-deficient cells infected with SARS-CoV-2 exhibit less virion production and the viruses produced are less infectious. Intriguingly, we find that expression of the non-cleavable TRMT1-Q530N variant in TRMT1-KO cells promotes an increase of viral titer as well as infectivity compared to expression of wildtype TRMT1. These results provide evidence for an unexpected role for TRMT1 expression in virus production and the generation of optimally infectious SARS-CoV-2 particles. We discuss the potential implications of this finding in the “Ideas and Speculation” subsection.

We agree that understanding the timing and effects of Nsp5-TRMT1 interaction will be an important area of investigation moving forward. We would like to include additional time points beyond 24- and 48-hours post-infection. However, we have found that the MRC5-ACE2 cells exhibited increased levels of cell death at 72 and 96-hours postinfection that could confound results (Raymonda et al 2022). Moreover, we would like to know how the reduction in m2,2G modifications affects host tRNA biology and translation. However, these experiments involve large-scale methods such as tRNA sequencing and ribosome profiling which are outside the scope of our current studies and will be the subject of future efforts.

We acknowledge the Reviewer’s assessment that we “played it a bit safe” in discussing the functional consequences of Nsp5-TRMT1 interaction. We aimed for a circumspect interpretation of our results and their biological implications, but might have been too cautious in our conclusions. Thus, we have added an “Ideas and Speculation” subsection that discusses possible reasons for how TRMT1 cleavage and interaction with Nsp5 could benefit the virus. We thank the Reviewer for pointing out this issue in our initial manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Having reviewed an earlier version of this manuscript, I appreciated the recent progress made by the authors. I felt the entire body of work is quite solid and the interpretations are clear and not overstated. One piece of data I thought deserved a sentence or two of discussion was the complementation assay with Q530N TRMT1. This experiment suggests the possibility that cleavage of TRMT1 by Nsp5 may be an act to self-limit replication, although this result could also be due to the elevated levels of Q530N TRMT1 expression compared to WT. I still think it is worthy of discussion. Another thing I would recommend is to include the length of infection by SARS-CoV-2 in the figure legends.

We thank the reviewer for their positive response and constructive comments.

We have followed the Reviewer’s suggestion to further discuss how cleavage of TRMT1 may act to self-limit replication in the “Ideas and Speculation” subsection. We have also included the length of infection by SARS-CoV-2 in the figure legends.

Reviewer #2 (Recommendations For The Authors):

In addition to the comments mentioned in the public review, this reviewer encourages the authors to address the following points:

• Please clarify the rationale behind choosing 24 and 48 hours post-infection as time points for the analyses (Fig 1). One would expect even lower levels of TRMT1 and RNA modification after 72 and 96 hours post-infection.

We chose the 24 and 48-hour time points since we have shown that MRC5 cells exhibit elevated accumulation of viral RNA at these time points (Raymonda et al 2022). However, at 72 and 96-hours post-infection, we have found that the MRC5-ACE2 cells exhibited cytopathic effects indicative of cell death that could confound results. We have included the rationale for these time points in our revised manuscript.

• In Supplementary Figure 3, please add in the legend the meaning of the asterisk symbol.

The asterisks denote non-specific bands that are still detectable in the TRMT1-KO cell line. We have updated the Figure Legend and thank the Reviewer for catching this omission.

• In Supplementary Figure 3B, there is an intermediate band in lane 3 with C145A when using the antibody 609-659. The authors should clarify what that band is.

The intermediate band in lane 3 (and in lane 6) of Supplemental Figure 3B represents non-specific detection of the Nsp5-C145A variant that exhibits extremely high levels of expression since it cannot self-cleave. We have clarified the identity of the band in the figure legend.

Reviewer #3 (Recommendations For The Authors):

I have only minor comments:

Although the authors have done a commendable job of providing compelling biochemical evidence of TRMT1 cleavage by Nsp5, it is not clear how this enhances viral infection. The discussion presents the experimental findings and prior publications as a series of correlated observations without clearly specifying the mechanistic benefits of TRMT1 hijacking towards CoV propagation, or even proposing a mechanistic hypothesis to this end.

We agree with the Reviewer that providing a mechanistic hypothesis on how TRMT1 cleavage impacts virus biology will help inform future studies. We have followed the Reviewer’s suggestion and discuss potential mechanisms in the “Ideas and Speculation” subsection.

How do these experiments inform us about the cell biology of SARS-CoV- infections? Does Nsp5-mediated degradation start early in infection? Is the loss of TRMT1 sustained over the course of the infection? Do Nsp5 concentrations or relative amounts correlate with TRMT1 loss during this period? For instance, is there only a modest increase in Nsp5 levels from 24h to 48h? I would suggest adding a few more data points than just 24h and 48h in the cell culture experiments. As the manuscript stands right now, it will be a bit difficult for readers to appreciate the relevance of this study in its present form.

These are excellent questions raised by the Reviewer. The temporal effects of SARSCoV-2 infection on TRMT1 levels will be an important area to dissect moving forward.

As mentioned above, we would like to include additional time points beyond 24- and 48-hours post-infection. However, at 72 and 96-hours post-infection, we have found that the MRC5-ACE2 cells exhibited increased levels of cell death that could confound results.

However, we do observe a correlation between the level of infection and the amount of TRMT1 depletion. In our newly added Figure 6C and 6D, we show that increasing the MOI leads to a concomitant increase in N-protein production that correlates with the amount of TRMT1 depletion. Moreover, we have added additional experiments to explore the biological relevance of our findings in terms of virion particle production and infectivity. We thank the reviewer for these insightful questions that have improved our manuscript and provide a foundation for future studies.

Related to this previous comment: how do the authors rationalize their inference that TRMT1 is essential for SARS-CoV-2 infection, yet it is cleaved during the infection? What seems to be the advantage of this seemingly contradictory but possibly quite intriguing inference?

We acknowledge the paradox that TRMT1 seems to be essential for SARS-CoV-2 replication but is cleaved during the infection. We propose several hypotheses to explain these findings:

Hypothesis 1: TRMT1 could be a bystander target. The loss of TRMT1 expression leads to a decrease in modifications that impacts translation. This decrease in translation capacity of the infected cells would lead to decreased production of viral proteins and reduced viral replication. This could explain why TRMT1-deficient cells exhibit less virus production. This could also account for why the TRMT1-Q530N mutant might produce more virus. In this case, the cleavage of TRMT1 and biological effects on viral replication and virion production are coincidental. However, even if TRMT1 cleavage and inactivation does not impact viral replication or production, it would still be important to know the cellular impacts that contribute to disease pathogenesis.

Hypothesis 2: The slight diminishment of viral replication due to host translation inhibition could outweigh the benefits of shutting down host responses dependent upon protein synthesis. The decrease in TRMT1-catalyzed tRNA modification caused by Nsp5 cleavage could severely inhibit host translation while viral translation can still be maintained through a tRNA pool optimized for viral translation, albeit at a slightly lower rate than if TRMT1 is not cleaved.

Hypotheses 3: The Nsp5-TRMT1 interaction could allow the virus to bind tRNAs that are packaged in viral particles as suggested previously (Pena et al., 2022). The finding that expression of the non-cleavable TRMT1-Q530N variant enhances viral replication and infectivity supports the hypothesis that TRMT1 could facilitate tRNA uptake into viral particles. The packaging of specific tRNAs in viral particles could enhance viral translation in the subsequent round of infection, thereby enhancing infectivity and perhaps facilitating the species jump of SARS-CoV-2 towards hosts with incompatible codon bias.

We have included these hypotheses in the new “Ideas and Speculation” subsection.